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: DECLINE IN CORAL COVER AND FLATTENING OF THE REEFS AROUND MAURITIUS (1998–2010)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Writing and organization are generally fine, I have some comments about specific lines, submitted under "other" below.
Experimental design: This is a study which analyzes data from a monitoring program.  It appears that the monitoring program was designed and implemented long before the analysis was done, by different people than those that analyzed the data, and the monitoring was not designed by those that analyzed the data and thus not designed specifically to make these particular analyses possible or robust.  (this is a common situation)  As a result, the design has a number of flaws that are common in monitoring programs, but which if the programs were designed for statistical analyses, would have been designed and carried out differently.  That leaves a variety of weaknesses that the analysis can’t completely compensate for, such as not randomizing locations, having only four reef slope sites, and so on.
      The analysis appears to be sophisticated, but suffers from a typical problem of modern, high-tech, statistical analyses, in that simple natural history observations preferably with some data recorded, could have documented the effects of bleaching and a cyclone directly.  Direct measurement of variables is almost always superior to indirect inference and guessing based on fancy statistics.
      The monitoring program design was pretty good for detecting change, since sites were marked.    Apples need to be compared with apples, not oranges, and if the sites change from year to year the measurement of temporal change is contaminated with spatial effects.  Figure 2 does show which sites were done which years.  2001 has a particularly low number of sites and probably should be excluded from temporal analysis.  Figure 2 shows that clearly the decrease in coral cover in the average wasn’t due to changes in which sites were recorded, by the end all sites were in negative territory.  So these problems may (may) be more theoretical than practical.  (but coral cover is only one part of the analysis)  But it would be good to have a way to estimate how much spatial differences contribute separate from time to the averages.  This is a very common problem.
Validity of the findings: Since sites were not chosen randomly, they are not necessarily representative of the various areas and thus concluding which variables controlled the variables being mentioned, could be influenced by site selection bias.  Could be the results are fine.  Bias in choosing sites is common, people want to monitor places that have good coral.  Unfortunately, the sites and collection of data can't be changed.
Additional comments: Line by line comments:
Line 42 the statistical methods aren’t necessary in the abstract unless they are the focus of the paper.  They don’t particularly hurt the abstract, just aren’t necessary.
Line 54 “however” doesn’t seem necessary
Line 75 wouldn’t you say that corals are very near the limits of their thermal tolerance during the summer?  About 1 degree above mean max temp and they start bleach, 2 degrees and they start to die.  They aren’t quite at threshold most years even at peak summer temperatures.
Line 86 driven to extinction.  Some have certainly been driven to local, economic and/or ecological extinction, but few in the marine world have been driven to global extinction.
Line 89 in the Caribbean
Line 115 a new study has also shown that light adds to heat stress in producing bleaching:    Coelho, V., Fenner, D., Caruso, C., Bayles, B., Huang, Y., Birkeland, C.  2017.  Shading as a mitigation tool for coral bleaching in three common Indo-Pacific species.  Journal of Experimental Marine Biology and Ecology 497: 152-163.
Line 120 regularly exposure
Line 140  contribute to the impact on
Line 167 that is a small number of sites, particularly on the forereef, for such a large island.
Line 167 how were the sites chosen?  They appear well spaced out along the coastline.  The back reef sites are located in a shallow “lagoon”, is the lagoon mostly sandy?  It is very wide in places, so how were sites chosen within that large area?  On the reef slopes, sites were located at a range of depths.  The depth could affect the reef community, how was the effects of depth separated from the other effects of environmental variables?
Line 172 one of the back reef site
Line 187 “permanent” is a popular word for a marked or staked transect.  However, little on earth if anything is permanent (since earth probably will last for another roughly 4 billion years) and especially on coral reefs where a cyclone can rip stakes out.  Marked or staked is more descriptive.  Staked or marked transects are likely to be better than transects relocated in other ways.  I presume the stake or mark was at the start of the 3 transects, and there were no further stakes or marks along the transects, is that so?  I presume that the transects were laid on depth contours on the forereef, you should state that.  At the backreef sites, how were the tape locations determined other than the stake at the beginning of the transect?  By compass bearing?  I assume they were on nearly flat substrate and the transect didn’t follow a depth contour, is that the case?
Line 209 Fungiid
Line 210 organisms
Line 267 need to define GHRSST
Line 272 suggest “these” instead of “they”
Line 274  ENSO certainly causes variation on an annual scale.  As far as I know, it is largely independent and on top of climate change.
Line 298  I think it would be worth showing (perhaps in a stacked bar graph) the cover for each site for one year, and the benthic trends of the means over years so the reader has some idea of the composition and trends of the categories.
Lines 304-305 how much variation was there in how many sites were surveyed in each year?  If the differences between sites were large (as they often are) then changes in which sites were surveyed can produce changes in the mean that are produced by spatial changes instead of the changes over time that you wish to measure.  If the number of sites and which sites change from year to year, how does the analysis remove the spatial contribution from the mean to reflect only changes in time?  (Figure 3 answers my question)
Line 326 not sure what you mean by spatially averaged.  Can that be explained?
Line 328 are these spatial averages for the forereef sites only, for backreef sites only, or for forereef and backreef sites?  Were the spatial averages done in two spatial dimensions or one?  Was it assumed that the reef area around a site had the same cover as the site?  Was cover interpolated between sites?  Any other assumptions?
Line 436 rubble
Line 557 in moving water  (in still water they are presumably similar)
Line 568  other studies in the Pacific implies that this study was in the Pacific.  Just remove “other” or change it to Indo-Pacific.
Line 585 are there any records of bleaching in Mauritius?  SST being the only variable correlating with the decline of coral certainly suggests bleaching might be the cause but it would sure be good to back that up with some information about actual bleaching events.  If there were no bleaching events there during this period, then some other process caused by SSTs probably caused the loss of coral cover.  Fancy statistics and assumptions like this are no substitute for in the water direct observations and recording of the effects of disturbances.  If you don’t have natural history observations, you can easily make mistakes with assumptions of causality.
Line 589  the logic behind this statement isn’t obvious.
Line 590 often causes(?)
Line 592  again, direct observation of cyclone damage is a far superior way to study the effects of cyclones than fancy statistics.
Line 604  as from?
Line 605 the trend with community structure was similar to that of many of the benthic groups studied?  But isn’t the community structure composed of benthic groups?
Line 629  I don’t see why you say “however”
639 different to   suggest different from
648 the resistance index
658 the differences between the width of the back reef at different sites is far greater than the distance between the back reef sites and fore reef sites.  So if the distance of the backreef sites from shore doesn’t affect the coral community, it is unlikely that distance alone is a good explanatory variable for the difference between backreef and forereef sites.  Do people walk out on the backreef for fishing and/or gleaning, or is fishing pressure much heavier on the backreef than forereef?
666 biodiversity correlates positively
673 coral reef
740 Porites astreoides needs to be italicized

Figure 3a you mean that a count of the human population in Mauritius is done every year, and in 2001 there was a big drop in population which was restored the next year?  Did a whole bunch of people move off the island and then return a year later?  Certainly a whole bunch of people didn’t die and then get reborn the next year.  This data looks suspect.  Population counts in the US are only done every 10 years, and are quite expensive since it is a huge task.
Figure 3b the dotted lines for cyclonic index and ENSO index are not the same as in the graph, and without blowing it up greatly are very hard to distinguish.  If they were the same as on the graph they would be much easier to distinguish.  I’d suggest thickening the lines as well.


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: DECLINE IN CORAL COVER AND FLATTENING OF THE REEFS AROUND MAURITIUS (1998–2010)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors use clear, professional English language throughout the manuscript. The main point of the title (i.e., fore-reefs as refugia) seems in direct contrast to the first statement about results in the abstract that “There was in general a significant decrease in live stony coral cover and a significant increase in dead coral and/or rubble cover island-wide for both the back- and fore-reefs.” (L43-45). This statement is supported by the island-wide results for benthic cover that report significant declines in more stony coral groups for fore-reefs (7 groups) than for back-reefs (5)  (L431-440). In general, the study design, data analysis, and results do not support the conclusion as presented in the title. Suggest an alternative such as “Changes in coral reef cover and community structure for Mauritius,1998-2010, from anthropogenic and environmental stressors”. The Introduction provides background for the context of the paper but there are statements that either cite a reference inappropriately (e.g., L73 citation (De’ath) does not support statement) or do not list a reference (L69-70 citation(s) needed). A few specific recommendations for text improvements include L50 edit “population” to “human population”, L101 edit “reef organisms” to “coral species” as they are the focus of the paragraph, not all reef organisms, L120 edit “regularly” to “regular”, and L139 needs a citation for statement about less fisherman, probably due to overfishing. The structure of the paper conforms to PeerJ and discipline standards. The Figures and Tables are relevant and professional but required edits. The Figure 2 legend station name abbreviations don’t match those listed in the raw data table. Need to include a description of what “anomaly” represents here. For example, the anomaly is a percentage above or below the long term coral cover mean for a given year. The legend for the anomalies includes a range of values (-61 to -50 and -50 to -40) that doesn’t appear in the data for any year. If that is the case, remove those from the legend and recolor the blue dots with a stronger gradient so that the differences in values is easier to interpret. Table S1. You don’t need to include the fore reef sites (e.g., NAME.f) in the list since they just present entries with duplicate values. Your Methods describes the site names and identifies that some sites have both back and fore reef sites. Table S3. For what time period is the Evenness index calculated?
Experimental design: The primary research is original and within the scope of PeerJ. The research question is fairly well defined and meaningful for the field. The Introduction sufficiently details how the work contributes to the discipline. The Investigation was performed to a reasonable technical standard but there were a number of issues. A primary concern is drawing inferences for the island-wide trends in benthic cover drawn from an overall low sample size, the unbalanced sampling design between fore-reef and back-reef sites, and uneven gaps in samples for time series. Your study includes only 4 fore reef sites from the leeward side of the island and compares these to 11 back reef sites from both the leeward and the windward sides. The lack of any windward fore reef sites undermines the inferences that can be made regarding the back reef and fore reef for the entire island domain. Furthermore, using a visual observation of the long-term coral cover means and the coral cover anomalies through time for the four locations that had both back reef and fore reef sites in Figure 2, the fore reef sites had either lower or similar coral cover to the adjacent back reef sites and for a number of years had instances of lower coral cover anomalies than the adjacent back reef sites (e.g., 1998-2001, 2003-2004). Figure 2 also highlights gaps in the time series of data for particular locations with approximately 19% of your samples missing from all possible site x time combinations and only one site (most southerly) having samples for the entire time period. Many of these issues are addressed for your community structure analyses but basically ignored for the trends in benthic cover analysis.

I had a concern about the coarse resolution of your global stressors, in particular SST derived from satellite data as a proxy for subsurface water temperatures on the nearshore benthic ecosystems. The accuracy of satellite-based SST in shallow, near-shore environments may be adversely affected at sub-regional scales by land adjacency as well as localized optical and oceanographic factors, which introduce bias into analyses (Castillo and Lima (2010) Limnology and Oceanography: Methods 8: 107–117, Leichter et al. (2006) Journal of Marine Research 64: 563–588, McClanahan et al (2007) Ecological Monographs 77:503-525. For example, Smale and Wernberg (2009) found that SSTs were significantly different from benthic water temperatures (usually 1 to 2°C higher), and did not adequately detect ecologically important small-scale variability or provide reliable information on temperature extremes. The use of a single SST per year seems too simplistic since coral bleaching dynamics are driven by extreme high (or low) values. Given that “Remotely sensed SST data were used since observed data were sparse and not representative.” (L265-266), I encourage you to demonstrate a statistical relationship between the remotely sensed data that you used for your study and the available observed seawater temperature data. This would help justify the use of the satellite data. Since the crux of your time series changes seem to rely on the shift in coral cover around 2004-2005, I suggest that you include one or a few of the available SST satellite coral bleaching indices (such as degree heating weeks) that may be more appropriate to use than just SST to predict bleaching occurrence.

The description of study sites does not include mention of the seasons, months, or dates when sites were surveyed. Considering the temporal aspect of this study, it is important to describe when the sites were surveyed within each year as differences in biological observations may reflect season differences (especially for algal groups, Williams (1993) JEMBE 167: 261-275), thus confounding any inferences that you draw regarding inter-annual differences.

Are the transects at sites truly permanent? (L186-187) In other words, is the exact same location (e.g., permanent stakes in the reef) resurveyed during each sampling occasion or just the general vicinity? If the former is the case, you’ll have issues with the independence of your samples across time and your statistics should incorporate the structure of your data (i.e., through repeated measures or mixed modeling approaches).
Did the line transect field method include a measure of benthic complexity like rugosity? This would allow you to address a loss of structural complexity with declines in coral cover. Although not ideal, if you didn’t collect rugosity measures during the study, you might consider performing an ancillary study to collect a series of rugosity measures for the various coral categories included in this study. This would allow you to estimate a mean rugosity for each category and then calculate a weighted-mean rugosity from each line transect. An examination of changes in rugosity would provide evidence regarding the outcomes of your observation that some encrusting or massive groups increased while the Acroporids decreased (i.e., homogenization of habitat complexity).

I don’t agree with your definition of a global stressor. Like your definition of a local stressor, a global stressor has different levels of impact at different sites but the source of the stressor is not local (e.g., SST or cyclones generated from global and regional processes of the coupled ocean-atmosphere system can have variable impacts depending upon site location). The source of the local stressor is local (e.g., rainfall as a proxy for run-off from an adjacent watershed differs between watersheds).

Methods for the analysis of trends are not described in sufficient detail. How were missing data years dealt with in the calculation of a long-term mean? When were stations surveyed during each year (i.e., is season or month a missing factor in your analysis or was it controlled for by sampling during the same month/season each year)?

Methods for analysis of community structure and stressors finds no apparent change in community structure for fore reefs in the analysis yet these sites declined significantly in Acropora and non-Acropora coral cover. I suggest that the analyses should be modified by lumping certain categories (e.g., by coral structure or taxonomy) so that you do not sacrifice data as described in your exclusion of rare categories (L352-353).

Methods for benthic community resistance and recovery. Need to define “Biodiversity” as a metric (L384). For the resistance index, you need to clarify what constitutes the “21-group benthic data for all years for which data were available” (L387-388). The logical structure of this index is a bit confusing since you’re assuming equal strength of stressors at each site but have statistically shown a correlation with population and back-reef communities. Doesn’t that finding undermine the utility of this approach? Delete the section describing a test of “wind” on the resistance index since the test was not run. For the test of biodiversity on resistance and recovery, please provide evidence that the number of coral colony morphology categories is a suitable proxy for coral species diversity. If no evidence exists, please delete this analysis and accompanying results from the manuscript. Given the relatively short time between the observed large decline in coral cover around 2004-5 and the end of the time series (2010), it doesn’t seem reasonable to assume that recovery would occur on a 1-5 year time scale for corals. I’m not sure there is much utility for this analysis given this constraint. It also seems out of place to present the resistance index stratified by sites exposed to or sheltered from wind since this variable wasn’t part of any of your other analyses due to the incompleteness of the sampling design (i.e., insufficient windward/leeward replication for fore reef).
Validity of the findings: The general conclusions drawn about the study of fore-reefs as a refugia are not well supported in the study results. I suggest a reframing of the study that does not draw this conclusion as the central focus of the paper but instead promotes when/what/how of the large decline in corals during the time series. There should be additional analysis to examine the effects of the 2004-2005 change point in the decline of corals regarding SST anomaly indices, not just a single SST value per year. This could also include some reconsideration of categories to include in your multivariate analyses from lumping by taxa and/or morphology. One comment, the foundation of the analysis relies on the percent benthic cover data presented in the raw data table. The sum of cover for all categories should equal 100%. The data table includes 585 total records, 114 of which contain no data since no sampling occurred for that location by year, and 471 records have data. Of those 471 records, 171 or 36% of the records, do not have values that sum to 100% total benthic cover. Although most of the differences are most likely due to rounding errors, this lack of attention to the most basic component of the analysis should be corrected and provides some concern about any analytical details that were not explicitly presented. I think the resistance/recovery metrics as included should be discarded. Furthermore, the comments made in prior sections should be addressed. In summary, there are interesting findings here that can be explored further. Namely, the significant declines in coral cover for many stony coral groups around 2004-2005. Examine additional coral bleaching indices to bolster your evidence that SST was a potential driver for the large declines that occurred. The loss of coral groups with complex morphologies would suggest a decline in habitat complexity from the decline in branching, tabulate, digitate corals and an increase in encrusting corals. This homogenization of coral structural complexity is a potential outcome in the decline of coral communities (Alvarez-Filip et al. (2009) Proc R Soc B 276: 3019-3025).
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: DISINFECTION EFFECT OF POVIDONE-IODINE IN AQUACULTURE WATER OF SWAMP EEL (MONOPTERUS ALBUS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please clarify what the authors mean by 'Line 229: After the test, none of the survivals was dead within a month.'
Was the dose of 173.82 ppm lethal to the eels?

Please work on improving sentence construction in some places.
Example: Discussion: Disease is a main threat in aquaculture production and disinfection of water bodies has been used as an important measure to prevent waterborne pathogen transmission in aquaculture' and 'However, there is a great differences between sterile water and aquaculture water, and this might lead to wrong guidance in practice.
Experimental design: It is widely known that presence of organic matter will decrease the efficiency of antimicrobials such as iodine. I did not see a point in testing   iodine efficiency with sterile and distilled water.
The authors should instead add/include results for water testing from various aquaculture farms and determine the amount of iodine necessary to control Aeromonas hydrophila in real conditions.
Validity of the findings: The findings are not entirely novel as it is known that organic matter will decrease availability of disinfectants like iodine. Results from actual farm water samples or if not available, simulating farm water conditions and testing them would make the study more robust.
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: DISINFECTION EFFECT OF POVIDONE-IODINE IN AQUACULTURE WATER OF SWAMP EEL (MONOPTERUS ALBUS)
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are several sentences that require attention in terms of English and spellings.
Line 33: ...wildly --> ...widely
Line 61-63: It is better to use reliable reference/s to demonstrate the distribution of this swamp eel, such as the FishBase
Line 81: ...factor --> ...factors
Line 82: ..., PH,... --> ..., pH,...
Line 99: ... the pathogen... --> ... A. hydrophila... (italic)
Line 168: ...these were... --> ... these cage water samples were ...
Line 323: ... water had ... --> ... water has ...
Line 323-324: ...b  actericidal ... --> ... bactericidal ...
Line 326: ... A. hydrophila ... --> ... A. hydrophila ... (italic)
Line 357: ... Health. 29... --> ... Health 29 ...
Line 396-397: Title of article should be in sentence form, not using Capital alphabet.

Figure 1: Label properly the (A), (B), (C) and (D) in the figure.
Experimental design: Research questions are well defined.
The experiment was designed properly. There is no issue about animal ethics as this study is following guidelines by the ministry and have been approved by ACUC of the university.
The methods described are sufficient.
Validity of the findings: Results are discussed in a good manner.
Conclusions are written well to answer the research objectives.
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: DISINFECTION EFFECT OF POVIDONE-IODINE IN AQUACULTURE WATER OF SWAMP EEL (MONOPTERUS ALBUS)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article needed some editing to improve the English, but the writing was better than I have seen in many articles written by authors for whom English is not their native language.  See attached word file of the document for specific suggestions for rewording.  The introduction adequately introduced the work conducted.  The discussion could be improved by broader discussion of the iodine literature, disinfection in eel culture, and microbial resistance.
Figure font size needs to be increased to make it more readable.
Experimental design: see general comments for a discussion of the controls used in the study.
Validity of the findings: The results contribute some locally useful information.  However the effects of organic matter have already been reported and general bactericidal effects of iodine are already well known.
Additional comments: ‘Disinfection effect of povidone-iodine in aquaculture water of swamp eel (Monopterus albus)’
Review: The manuscript summarizes research on the effects of povidone iodine on water containing isolates of A. hydrophila.  The paper provides some useful data on the concentrations of iodine needed to kill bacteria and on the effect of organic matter on effective concentrations within an eel culture context.  There are several deficiencies in the research, but there is enough good data that I recommend publishing after some revision.  I have made some grammatical suggestions in the attached word file using track changes.  Other suggestions for improving the manuscript and concerns to address are as follows:
1.	The study inappropriately considers the deionized water treatment and LB broth treatment (high organic load) as negative and positive controls.  These are additional treatment variables not controls.  Proper controls for the Germicidal Test would be water samples with (positive control) and without (negative control) A. hydrophila to which no chemical was added.  The data for the LD50 assessment has a proper control (no iodine), but there is no control for the ddH2O trial or the LB broth trial.  The data for the ddH2O trial should be removed from the manuscript.  It is not applicable to aquaculture.  No aquaculture organisms can survive in distilled water and no one uses it for culture.  Soft water, i.e., with low hardness and alkalinity, is used, but that was not tested in this study.  To test the effects of organic matter, I would recommend adding several cm of pond mud and pond water to aquaria; after settling, add bacteria, then iodine; sample at the various time intervals.  This would be more representative of the actual organic load encountered in the pond.
2.	Another concern in the application of the data is the potential to create bacteria strains that become more resistant to iodine at marginal concentrations or those that are protected in part by biofilms or organics in the mud.  This is not addressed at all in your discussion, but should be mentioned as a concern to users of the results.
3.	The authors imply that using aquaculture water for their research was a better way to evaluate the effectiveness of the iodine than using sterile water.  The reason sterile water is used is to rule out effects of other bacteria, which cannot be done in this study.  There was no confirmation of any kind noted in the paper that the bacteria observed on the agar plates were A. hydrophila.  So the bacteria could have been any species that was in the water sample.  This affects interpretation of the results, which indicated that the effective doses were for all culturable (heterotrophic) bacteria that can grow on LB media, not A. hydrophila per se.  The discussion should be approached with this fact in mind.
4.	The figures need to be redone to increase the font size and make them more readable.
5.	Add a reference or recipe for the LB agar to the methods
6.	Line 107: a sentence is needed describing how water samples were added to the bacteria pellet
7.	L128: it is not clear how beads are used; please describe and reference as needed
8.	L142: add duration data
9.	Any tank aeration during the eel exposure trial?
10.	Add details and conditions to the Methods section regarding the long-term monitoring of eels (up to 1 month)
11.	L242: as mentioned under item 1, ddH2O has higher mortality because of the lack of Ca, Mg and the bicarbonate ions, not reduced organic matter.  See Claude Boyd’s book on water quality in aquaculture ponds for more details and references on water quality.  Deleting the ddH2O data will make this section unnecessary anyway.


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: DISINFECTION EFFECT OF POVIDONE-IODINE IN AQUACULTURE WATER OF SWAMP EEL (MONOPTERUS ALBUS)
Review round: 3
Reviewer: 1

Output:
Basic reporting: Generally well written with appropriate references and introduction to the research problem.
Experimental design: no comment
Validity of the findings: data should provide additional information on the utility of iodine for disinfection and the effects of organic matter on its efficacy.
Additional comments: just a few editorial suggestions, given by line number:
L83, 'includes' not include
L87, 'uses' not use
L149, 'status' not statues
Add/move probit analysis to statistical analysis section
L184 change 'killed' to 'kill'
L231 delete 'in' so sentence reads '...was present...'


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: TAXONOMIC PATTERNS IN THE ZOONOTIC POTENTIAL OF MAMMALIAN VIRUSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the presented manuscript, the authors reanalysed the virus dataset and revisited the conclusions of Olival et al., 2017 about the potential of non-human mammalian viruses to infect humans (zoonotic spillover). They used taxa of virus taxonomy as surrogate replacements of monophyletic clusters of the virus tree, which is not as readily available, to produce a phylogenetic perspective on traits associated with the dataset. The authors classified taxa as zoonotic or non-zoonotic which split the original dataset into two subsets accordingly. These subsets were then reanalysed using protocols of the Olival et al., 2017 study to assess propensity of spillover. The authors then calculated range of non-human hosts for the appropriate taxa and identified taxa with a high risk of zoonosis and a large host range as those that prone most to include viruses which could present a threat to humans. The Togaviridae, Flavivirus, and Bunyaviridae taxa were found to belong to this group, while the Herpesviridae to the opposite group with the least zoonotic potential.

This reviewer was left uncertain about differences between the conclusions of two studies, those by Olival et al., 2017 and the authors of this manuscript, respectively. Another concern is that the main conclusion may be trivial and incomplete. Just following news about emerging virus infections over the last 20 years may suffice to identify the above three virus taxa as of a high spillover potential. Also in the news are Coronavirinae, Filoviridae, and Arenaviridae, and their absence among the top runners of this analysis may warrant a comment from the authors.

The authors should also consider discussing considerable limitations of relying on virus taxonomy, instead of virus phylogeny, in this type of analysis.

To help the reader navigate the manuscript, please define zoonotic and non-zoonotic clades.

Consider replacing “breadth” with “range” in the “non-human host breadth”.

Consider replacing ICTV taxonomy with virus taxonomy, which is – by definition – ICTV approved.

All ICTV recognized taxa should be written in italic.

Discussion is too long and focused on aspects not immediately connected to the obtained results.
Experimental design: 101-106: ICTV taxonomy tree should be described in detail and comparison with virus taxonomy, which is a hierarchical five-level classification. The source of this tree should be provided.

“Bernoulli-distributed zoonosis data” should be specified in the Data collection. They are never mentioned elsewhere in the manuscript.

109-119: The authors should expand on explaining the meaning of “factors” in their phylofactorization analysis. In the manuscript text, it is apparent that virus clades and taxa are treated as “factors”. Is this reading correct? If so, what is the rational to write “Phylofactorization-derived Clades” in the line 129 and elsewhere? Are they simply taxa? Other examples of factors would be useful for the reader to understand the concept application to this study.

What is the difference between partitioning “ICTV taxonomy” by using phylofactorization and listing all taxa of virus taxonomy, which are accompanied with qualifiers describing certain propensity, e.g. human, zoonotic, etc?

All taxa identified in this study are at the four ranks, from genus to order. Have species been considered?
Validity of the findings: Figure legends are not informative for understanding figures, as explained below.
Fig. 1. Current legend is nice but it does not explain this figure. What do different arrows and colors show?
Fig. 2. Legend should explain parameters of Table (Taxonomic level=rank, name-> taxon name; n-?) and details of tree (black dots, etc). How was factor number determined? Should this list be ordered by %Zoonotic? Provide a supplementary Table with the data used to produce the tree.
Fig. 3. What is “Non-human phylogenetic distance on a cytochrome B phylogeny”, and its relation to this figure? What are the units used for the X axis in panels A and B? What data were used and how were they analysed for each of these panels? What does the “Original” stand for? What does the “No Common Name” stand for? Panel labels are missing.
Fig. 4. Provide explanation for the top plot (see my comments to other figures). Provide results for the “updated” along with those for the “original” dataset. Define the dataset for the updated. What does the Total clade size stand for in the bottom Table? Are the data in this Table from the Olival et al., 2017 or this study?
Table 1. Could we say, for this Table and all study, that “Original” = “All clades” and “Phylofactor-restricted” = “Zoonotic Clades”? If not, please explain the meaning of these terms in relation to zoonotic, since you use non-zoonotic as a derived dataset.
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: TAXONOMIC PATTERNS IN THE ZOONOTIC POTENTIAL OF MAMMALIAN VIRUSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The methods are not explained well (see below), but this is overall a well written manuscript with clear and engaging prose.
Experimental design: The questions that the paper addresses will be of wide interest to readers.  These results would be difficult to replicate without providing additional details about the methods.
Validity of the findings: The methods used and the the authors' interpretation of their results seems sound.  However, I had to do a good bit of reading outside of the material presented here to reach this conclusion.
Additional comments: In this study the authors apply a new method, phylofactorization, to investigate the properties of viruses that are prone to spillover in humans.  They find that non-human host breadth is an important predictor of zoonotic potential.

The study is of an important topic, and has generated a lot of interesting hypotheses.  The only real issue I have with it is that phylofactorization isn’t described very well.  Three studies describing the method are cited, but only one of them has been peer reviewed.  Somewhat confusingly, the one peer reviewed publication primarily concerns the analysis of microbiome data sets.

In figure 1, the authors attempt to illustrate how this method works.  However, it is unclear why the traits wings and birds are excluded, given that their distribution across the tips of the tree is identical to that of feathers and hollow bones.  The only trait that appears to contain any additional information about flight is “Lives in trees” in this example, and obviously many animals live in trees and don’t fly.  Aside from that, wouldn’t conventional phylogenetic comparative method find a significant association between living and trees and flight?  Why do we need to use phylofactorization to find a clade to restrict the analysis to?  Couldn’t we have identified the clade using ancestral character reconstruction (e.g., focusing on the largest clade or clades with a high likelihood of having a common ancestor with flight)?  The figure left me with more questions than answers.

By reading some additional papers I was able to get a better sense for how the method works.  I found Washburne’s (Washburn et al. 2018) paper in Nature Microbiology particularly helpful.  However, when presenting results using a method that very few readers will be familiar with, I believe the onus is really on the authors to 1. Explain how the method works clearly enough that most readers will understand it and 2. Explain why more widely known techniques such as PGLM analyses, concentrated changes tests of trait association, and/ or ancestral character reconstruction couldn’t have been used here.

The description of the methods  is also pretty vague in general.  They say that “the ICTV taxonomy tree was constructed using the R package ape.”  What version of ape?  What version of R?  Was it a zero branch length tree, or were all branch lengths assigned a value of one?  If neither of these, how were branch lengths derived?  How robust is the phylofactiorization method to branch length assumptions?   How were the phylofactorization analyses implemented?  Presumably using the phylofactor R package.  If so why isn’t the package mentioned?

Apart from these issues, I think this is an interesting study.  The results suggest which taxonomic groups should be the major focus on future work to understand viral spillover, and two traits that are strong predictors of zoonotic potential within those groups.  Other traits that have been shown to be important in a previous study seem primarily diagnose whether viral species are members of the taxonomic groups revealed by these analyses rather than having a function is spillover per se. These are all potentially important results.  Of course, given that the “Non-zoonotic clades” contain numerous (at least 15 based on figure 2) species known to be zoonotic, understanding variation outside of the phylofactor restricted clades is still also of interest.

Cited:

Washburne, A. D., Morton, J. T., Sanders, J., McDonald, D., Zhu, Q., Oliverio, A. M., & Knight, R. (2018). Methods for phylogenetic analysis of microbiome data. Nature Microbiology, 3(6), 652.


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: TAXONOMIC PATTERNS IN THE ZOONOTIC POTENTIAL OF MAMMALIAN VIRUSES
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper tackles the difficulties in predicting viral spill over. It presents a new approach, i.e. phylofactorization, for a better understanding of which viruses are more likely to jump between hosts. This method consists of re-organizing the virus taxonomy using the host range of non-human viruses and whether such viruses have infected humans. This is different to previous methods used, where virus traits were used to predict potential spill over. The authors claim that traits might be negatively associated with spill over due to the fact that the trait is shared by many different virus species and families, most of which might be non-zoonotic. Hence, the authors suggest regrouping viruses according to their spill over potential and then identify common traits within these groups.
The manuscript uses appropriate English throughout and is structured clearly, although I think the discussion is a bit too long, particularly lines 301 ff. could be cut down. Figures are specified in the correct places and of reasonable high quality. Raw data is supplied as requested. I have a few suggestions that I believe would improve the manuscript.
Figure 1. I understand this figure is used to explain the model, however, I found it difficult to associate the figure with the actual methodology used in the paper, as the figure used bird traits and the paper uses virus traits. Would it be possible to use virus traits as an example?
Table 1. I suggest using a text format instead of power point for this table. Maybe use the same format as in figure 4.
Experimental design: The experimental set up is well-described and reasonable for the question asked. Predicting viral spill over events is a difficult if not impossible task and the paper here uses a novel approach to address the issue. Methods are well described, and the data is available online for replication. The authors re-analysed an already published data set using their novel method and discuss the differences in the results.
Validity of the findings: The paper addresses the difficulties in predicting spill overs and how caution needs to be taken in consideration when analysing potential predictive traits. The authors assess these difficulties and resolve the problem partially by investigating traits common for viruses that spill over frequently in comparison to traits common for viruses that do not. The authors clearly state the different outcome in which trait is associated with spill over sing their method and previous method. However, I lack more information on which virus families are more associated with spill over using either methods. I think the authors could elaborate on that a bit more.
Additional comments: Line 13. I am missing the connection between the first and second sentence in the abstract. I suggest removing this sentence and add an introduction sentence on how current classifications might be misleading.
Line 189. ‘when’ is used twice.
Line 362. Replace ‘quasispecies’ with ‘variants.


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: TAXONOMIC PATTERNS IN THE ZOONOTIC POTENTIAL OF MAMMALIAN VIRUSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: My primary concern was that the new methods wern't described sufficiently in the paper for readers to evaluate it, and nothing peer reviewed fully describing the method seem to even be in press at the time.  However, by doing a lot of research beyond what was presented I was able to satisfy myself that the methods and conclusions were sound.  Now that there is an Ecological Monographs paper describing the method in press, I don't believe readers should have any issues with this.  The authors have also adequately addressed my more minor concerns.


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: TAXONOMIC PATTERNS IN THE ZOONOTIC POTENTIAL OF MAMMALIAN VIRUSES
Review round: 2
Reviewer: 2

Output:
Basic reporting: I am happy with the changes the authors have made and have no further comments.
Experimental design: I am happy with the changes the authors have made and have no further comments.
Validity of the findings: I am happy with the changes the authors have made and have no further comments.
Additional comments: I am happy with the changes the authors have made and have no further 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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is not well structured and very difficult to read. It took me some time to understand the aim and results of the research: basically, participants were shown a bi-stable figure (figure that can be interpreted in two distinct ways) that was flashed on a screen by rhythmically turning it on and off;  perceptual experience (rate at which percepts alternate and time a percept is sustained) was then measured as a function of flash duration and frequency. The main conclusion was that the alternation rate was modulated by the flash duration.
The authors failed to write an introduction that invites the reader to be drawn into their research: it lacks a clear hypothesis and does not explain why their research is important; instead they provide an incoherent overview featuring feature detection and brain waves that was confusing rather than clarifying.
Throughout the manuscript the authors refer to "an interaction between two streams: an external one (controlled and caused by the flash frequency and duration) and an internal one"; what that internal stream should look like, or how it is generated, is very unclear.
Experimental design: Just like the rest of the paper, the methods that were used were very unclear and hard to understand. The authors could of have used visuals or explain the concept better; for instance, they define absolute perception time (PT), then follow by the statement: “instead of PT we measured the changes of PT”; instead of explaining what this means conceptually, they immediately proceed with a confusing formula. Because the authors fail to explain the methods in a comprehensive fashion, I perceived the methods as abstract and detached from the experiment itself.
Validity of the findings: Given the lack in clarity and detail of the methods that were used (see 2), it was hard to judge the validity of the finding. However, based upon the p-values reported in table 1, and upon visual inspection of the figures 1-3, the claim that modulation of perception as a function of flash duration, is periodically at 4 ms intervals, seems to be quite robust.
Additional comments: Dear authors: I recommend seeking the help of an experienced writer. I struggled to understand your manuscript and was confused from line one until the very end. The manuscript lacks clarity and consistency and is incomprehensible in its current form.  Here are some questions/doubts/comments.

lines 2-3 (abstract): “We investigated whether the alternation rate of the perception of a Necker cube depended on the degree of synchronization between two streams of spikes”. Sorry, that is not what you did!

Lines 7-9 (abstract): “Knowing how a flickering stimulus with a given frequency and duration affects the alternation rate of bi-stable perception we could estimate properties of the
internal signal”; if true, then what are the properties and why are they not listed or mentioned in the abstract?

Lines 11-12 (abstract): “The values of the stimuli…”. I have no idea what “value” means in this context;

Introduction: throughout the manuscript you bring up that mysterious “internal signal”, which you referred as spikes and internal stimuli (abstract); or as “internal high frequency rhythms” and “internal impulse streams” (introduction). It is all very confusing. I recommend rewriting the introduction and focus on 3 points: (1) Explain what made you investigate how perception can be modulated by flash duration and frequency. In other words, why was it worth doing this effort? (2) Clearly state your hypothesis (3) Provide arguments for your hypothesis. For instance, what supports the existence of an internal stream that is independent of external influences and oscillates at a frequency that is sufficiently high (125 or 250 Hz) to explain your results.

Methods: the methods could use a figure for clarity. For instance: panel A, a cartoon of the setup; panel B: an image of the exact version of the Necker cube used for the experiment (with an arrow pointing from panel B to the location in panel A where the Necker cube is shown in the setup. Panel C: an example of a session, with 19 lines corresponding to the 19 blocks; each line represents 180 seconds and portions of the line are colored in one of two colors that represent when the subject was perceiving UP or DOWN. Then you can refer to this figure to explain the mathematical methods (for instance absolute perception time can then be explained as the total time represented by color 1, perceptual changes explained as … etc.)

Line 122: “... the mean dPT of UP and DOWN” should be “... the mean dPT of respectively UP and DOWN”

Data analysis: should be written more concise; in addition to explain the methods mathematical, an effort should be done to explain each method conceptually as well.

Line 146-147: It is not clear why 5 subjects were lumped together. This basically reduces the data to 4 sets: 3 from experienced subjects and 1 averaged across all naïve subjects; the results are thus heavily skewed in favor of subjects that are not naïve, presumably the authors of the manuscript; some concerns of bias might arise.

Lines 166-167: “The data revealed that the PT of the dominant image varied in timing from a few seconds to ten seconds depending on the subject.” Varied with respect to what? The non-dominant image, varied across blocks? Varied across sessions?

Lines 167-169: “For example, DOWN was perceived longer than UP by subjects RB and IS (2.09 s vs 1.67 s and 3.65 s vs 2.57 s respectively), but …” what does the 2.09 vs 1.67 represent? It is my understanding that each block last 180 s and that there are 19 blocks in a session (including the non-flashing condition); thus totaling 180 s * 19 =  3420 seconds in a session; this means that the time DOWN was perceived + the time UP was perceived should be 3420 seconds. I do not understand how the numbers mentioned in lines 167-169 are obtained. Please explain.

Result section: Could be explained more concise; many details are not relevant

Discussion section: reads like a fishing expedition, desperately trying to explain the “internal stream”; based upon your results, the opposite is true: oculomotor tremor (80-100 Hz) does not fit because the frequency range does not match; the non-linearity of the Broca-Sulzer effect is observed around 80-100 ms. I am not sure how this can be applicable to your findings. The gamma range (40-90 Hz) is also does not fit. So I think it would be better to organize the discussion as follow: we checked oculomotor tremor as a potential generator of our internal signal, but need to rule this out because of this and that; we checked gamma oscillations, but need to rule it out because… etc..

The discussion should also be used to consider alternative explanations for the results, not based upon an “internal stream”; eye-blinks for instance induce reversals in perception, and the rate of eye-blinks might be modulated by the flash duration and frequency.


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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is in general well structured, but it would be clearer if the description of the sinusoidal fitting were moved to the Methods section.
The authors should also clarify if the results described in lines 170-175 are calculated over dPT or deltaTao.
Experimental design: The authors performed the experiment on 8 participants, 3 non-naïve and five naïve. The amount of data collected on the different subject varies significantly, with some subjects taking part in 3 sessions, some in 10, and some in 20. An explanation of this discrepancy should be present in the text, and potentially the analysis should be repeated in such a way that there is the same amount of data for all subjects (i.e. the first three sessions for all subjects).
Validity of the findings: The major flaw I find in the manuscript is that the final data analysis presented is performed on heavily processed data, including two non-linear transformations. At the very least, a representation of the raw data, the changes in PT or dPT as a function of flash duration, should be provided along with an explanation of why this processing was performed and why it is the best way to analyze the data. As it is, it is hard to see if the conclusions are supported by the data or if they are a consequence of the performed manipulations.
Other issues I found with the data analysis and interpretation are as follows:
1.	The PCA analysis is not very clear. What is the dimensionality of the inputs to the PCA, and what are these inputs? The PCA was also run on the three of the subjects individually, since those are the ones that are claimed to perform 20 trials (although only two of them participated in three sessions as described previously, so this should be clarified), and on the aggregated of the other five subjects. Why is this? It seems like the correct way to do this would be to run the PCA on the aggregate of the 8 subjects if it was not possible to do it individually for each subject.
2.	Regarding the results of the PCA, it is unclear what insight this PCA analysis provides. It is specified that loadings F3 or F4 depended on stimulus duration. Assuming that subindices 3 and 4 specify the order of their weight (i.e., the third and fourth-most important factors), it would be interesting to know: a) what other factor affected these loadings, and b) what parameters were the most relevant (those that affect F1 and F2).
3.	In lines 303-315 the authors discuss the effect of stimulus duration in perceived brightness and cite the presence of the Broca-Sulzer effect at specific durations, but it is unclear how this discussion relates to the data at hand.
4.	In general, it feels the discussion could be made more concise.
Additional comments: There are two points that I would like to be included in the discussion:
1.	Whereas the authors claim the data point toward the existence of an internal oscillator of frequency around 125 Hz, it seems like the data could be explained with other models that do not include this type of oscillation. The authors even hint towards a potential role of microscopic eye movements (tremor). Why do the authors think the internal oscillator is the most parsimonious explanation?
2.	How would a change in stimulus duration would affect the percept time of the bistable stimulus if flashing frequency was to be kept constant (i.e. 1 ms flash on an 8ms period versus a 6 ms flash with 8 ms period), depending on the model chosen?


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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 2
Reviewer: 1

Output:
Basic reporting: See General comments
Experimental design: See General comments
Validity of the findings: See General comments
Additional comments: I am impressed with the improvements made by the authors. My previous comments are addressed in a satisfactory manner. However, the language throughout the manuscript is often too verbose, and the many grammar and spelling errors give a sloppy impression; I tried to catch some errors (see comments) but I am sure that I missed quiet a few; I recommend seeking the help of a native English speaker to “polish” the paper;

Comment 01: bistable (lines 30, 73, 75, 326 and 341) or bi-stable (title, lines 8, 13, 36 and 270)? Please be consistent.

Comment 02: lines 9-11 “… show that THE DURATION of the dominant stimulus perception depends …”
lines 13-14 “We can also conclude that it is NOT THE STIMULATION DURATION but the ….”
Please clarify this apparent contradiction.

Comment 03: lines 12-13: “… could be explained by existing of internal rhythm …” Suggested: “… could be explained by the existence of an internal rhythm”

Comment 04: line 61 “can not”; preferred: “cannot”

Comment 05: l “synchronisation” (line 62) or “synchronization” (lines 6 and 286)? Please be consistent.

Comment 06: line 63: “rythmically” should be “rhythmically”

Comment 07: line 67: “stumulation” should be “stimulation”

Comment 08: line 69: “in the study”; suggested: “in a study”

Comment 09: line 73: “is continuation”; suggested: “is a continuation”

Comment 10: line 110: “later in the work is named as”; suggested: “which we refer to as”

Comment 11: line 111: “minimal flash duration”; suggested: “minimum flash duration”

Comment 12: line 119: if PT represents the time accumulated across a block, then please add this information.

Comment 13: line 124: “Firsly” should be “Firstly”

Comment 14: line 158: “non-random factor” should be “non-random factors”

Comment 15: line 165: “…will repeat again, will increase, if the frequency…” I did not understand this sentence; please check use of commas or reformulate.

Comment 16: line 165-166: “Thus to avoid…” should be “Thus, to avoid…”

Comment 17: line 173: “… integer number, and defines…”; suggested: “integer number and defines…”

Comment 18: lines 195-197: For clarity, I suggest mentioning (explicitly) that small numbers indicate a high alternation rate.

Comment 19: please compare lines 242 and 244: in an enumeration, you sometimes use units for each value; sometimes none at all; I suggest that you, throughout the paper, use units only when mentioning the last value: for instance: 10, 20 and 30 s.

Comment 20: line 245: “Some years ago we…” should be “Some years ago, we… “

Comment 21: line 256:  I am confused by this sentence; because you start the sentence with "in both cases...", I expect a single value (for instance in both cases the period equals X).

Comment 22: line 262-263: “…duration of flashing stimulus influence the perception time…” should either be: "... duration of a flashing stimulus influences the perception time..." or "duration of flashing stimuli influence the perception time…"

Comment 23: line 276: “Considering the influence of rhythmically flickering stimulus on…”  should either be “Considering the influence of a rhythmically flickering stimulus on…”  or “Considering the influence of rhythmically flickering stimuli on… ”.

Comment 24: line 283: “… to high-gamma frequency brain rythms…” should be “…to high-gamma frequency brain rhythms…”

Comment 25: line 290: “It should be noted that our results allow to propose that…”: too verbose

Comment 26: line 296: “Thus it can be related…” should be “Thus, it can be related…”

Comment 27: line 309: “…(or tremor)”; suggested “…(or ocular tremor)”

Comment 28: line 310: most investigators in fixational eye movements provide lower estimates for the frequency of ocular tremor; please revise.

Comment 29: lines 319-320: since “Critical Flicker Fusion” in only used once, I don’t see the need to provide the abbreviation.

Comment 30: line 350: “…maxima demonsrate that…” should be “…maxima demonstrate that…”

Comment 31: line 353: “…suppose the existance of…” should be “…suppose the existence of…”


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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: After the rewriting of the methods section, I still have some issues with the methods as described:

-I still do not understand what the PCA analysis adds on top of the rest of the data. It seems to me like components above the noise level were extracted, and then the one component that matched the experimenters hypothesis, which was not even the same for all subjects nor the one with the highest weight, was represented. I suggest authors either clarify exactly what they were trying to achieve with this analysis and the procedure, and provide a more extensive discussion of the results, or remove the analysis altogether.

- The description of the analysis methodology still needs some improvement. As it stands, it is very hard to understand and requires to go back and forth paragraphs to understand the analysis of extrema distribution in particular. A more descriptive naming of variables would be a start.

- I would like to see the breakdown of the data for the group of subjects labeled as Rm5, even if the PCA analysis is not possible.
Validity of the findings: Several issues here. In the results section:

-"The statistical analysis (post hoc LSD test) of the experimental data (dPT) confirmed that the differences between the minimum and maximum values were statistically significant, and the extreme points were recurrent": what does it mean for the extreme points to be recurring? How was this assessed? Where are the results for the LSD analysis? I only see the ones for the basic ANOVA

Regarding the discussion and conclusions: the authors need to explain better what this internal oscillator they propose is exactly. Are they talking about an internal rhythm generated somewhere in the brain and then distributed across different areas? Where is it coming from? Or is it a matter of input timing as it relates to processes internal to the cells? Something else? The suggested explanations are extremely vague and highly speculative. The fact that the periodicity they observe falls within the bandwidth of ocular micro tremor and high-gamma rhythms seems irrelevant given the information provided here, since it can easily be a coincidence (specially with the big bandwidth associated with both phenomena, which makes this type of coincidence easier).

Also, the authors claim that these results show that only frequency of flashing and not flash duration influence bistable perception, which is not true. The effect of these parameters can not be disentangled from a duration effect by the fact that in their experimental paradigm those two variables follow a one-to-one relationship (the authors themselves use duration to refer to frequency at some points in the manuscript). Whereas the data points toward flashing frequency as a relevant factor, effects of duration can not be discarded.

It is unclear what the authors are trying to communicate in the paragraph explaining the effect of duration, flicker frequency, and perceived contrast.
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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 3
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The manuscript underwent, after two rounds of editing, a major transformation; given that the authors can resolve some minor issues (see below), I can now finally recommend the publication of the manuscript in PeerJ.

Some minor comments:

Line 25: “… time of dominant stimulus depends on...” should be either “… time of the dominant stimulus depends on“ OR “… time of dominant stimuli depend on…”

Line 28:  “125 cps”; but  line 295: “125 c/s ”. Since neither “cps” nor “c/s” is defined, maybe use “cycles/s” in both cases?

Line 44:  “… physical properties of stimulus… “ should be replaced either by “… physical properties of stimuli… “ OR “… physical properties of a stimulus…”

Line 58: “… the absence of stimulus on …” should be replaced either by “… the absence of stimuli on …” OR “… the absence of a stimulus on …”

Line 175: “… about 67 – 75 % …”; but line 236: “average 66.72– 75%...”; begin and end of the range should show the same precision, or both should be rounded.

Line 249: “…(from 3.68 to 4 ms)…”: same comment as above; if the 4 ms has a precision of 3 digits, then use: “…(from 3.68 to 4.00 ms)…”.


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: FAST CYCLIC STIMULUS FLASHING MODULATES PERCEPTION OF BI-STABLE FIGURE
Review round: 3
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: The explanation and interpretation of the PCA analysis is much clearer in the rebuttal letter than in the manuscript. Please rewrite using that as a model.
Validity of the findings: Make the fact that the effect of perceived brightness of stimulus due to temporal effects does not affect the periodicity (due to its monotonic shape in the range of durations and frequencies tested) clearer.
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: DIFFERENCES IN PERSISTENCE BETWEEN DOGS AND WOLVES IN AN UNSOLVABLE TASK IN THE ABSENCE OF HUMANS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 110-116 In this sentence the authors claim that it is possible that dogs do not turn to humans to seek assistance with a problem solving task, but rather as a result of lack of persistence and that there is nothing else for the dog or wolf to do. Can they not also choose to explore the room/enclosure or simply do nothing? Persson et al. 2015 did a principal component analysis including both human-directed behaviours as well as task interactions. They showed that there was no correlation between task interactions and human interactions. If the dogs turned to the human as a result of lack of persistence, this would have shown as a negative correlation in the principal component loadings.

Line 163-164 “Based on literature, we predicted a positive correlation between persistence and behavioural variety.” ; it would be helpful if the authors could add a few of those literature references here.

Line 168 “subjects that show an unsure body posture” ; do the authors mean insecure body posture? Or do they mean that they are unsure about the body posture displayed by the individual? I think this needs clarification or perhaps just a change of word choice.

The authors write “based on literature” or similar on line 163, 172 and 175; I suggest that they re-phrase some of these sentences to make it easier and nicer to read.

Line 178-180 – I like that they summarise their aims in the end of the introduction. Very helpful!

Materials and methods

The authors do not mention the breed/s of the dogs. They refer to another study where there is a more thorough description of the animals. However, I believe that this manuscript would benefit of a bit more information about the animals such as breed, handling, social experiences etc. Have both of their species been subjects of the same studies previously e.i. could they have different experiences from previous studies possibly affecting problem-solving behaviour?

There is quite a large age difference between the dogs and the wolves of this study. This should be addressed and the implications discussed in the discussion section.

The authors use a lot of “we” e.g. “we tested”, “we placed” etc. throughout the entire materials and methods section. Hence, I believe that some re-phrasing to remove some of the “we” will improve the text in this section. Example: they write on line 212 “We mounted a smartphone..” , instead they could write “ A smartphone was mounted..” or similarly.

Line 240 I cannot find this supplementary video among the reviewing material.
Line 242 I suppose it should read “first contact with the object” and not “First contact object”?
Line 242 change “Defined” to “defined” with a small d.

Results

Line 322, 324-235, 338 etc and in Table 3 as well as in the text of the results section (perhaps also in other places) the authors write “unsure” as opposed to “confident”. I believe they are referring to the “insecure” body-posture of table 2? This should be changed so that they consistently stick with the same term. I personally think that “insecure” is preferable in this case.

Discussion

As previously mentioned, some discussion about the age difference and effects of age on problem solving behaviour should be added to this section.

Line 434-435 add a “to” “may help to better understand”

Table 1
I think this table would look better if you removed the horizontal line except for the header row. You could probably remove the vertical lines as well and make the headers and columns centered except for the first column.

Table 2
I think the design of this table can be improved, see comment on table1

Table 3
I think the design of this table can be improved, see comment on table1 e.g. remove the lines among the values but keep header lines and first column vertical line.

Figure 3
One of the labels read “unsure”, does this refer to insecure?

Figure 4
Looks good!

Figure 5
Looks good!
Experimental design: The dogs have a mean age of 4 years while the wolves had a mean age of 6.3 years. By looking at the age presented in table 1 you can see that there is a great variation where there are several dogs at the age of 2 years and several wolves at the age of 8 years. This could have effects on your data. There are studies showing that age affects boldness and explorative behaviours in dogs e.g.

Starling MJ, Branson N, Thomson PC, McGreevy PD (2013) Age, sex and reproductive status affect boldness in dogs. Vet J197: 868–872.

Siwak CT (2001) Effect of
age and level of cognitive function on spontaneous and exploratory behaviors in the beagle dog. Learn Mem 8: 317–325.

I cannot see that the authors have included age in their models. Did they correct for age in any other way? Otherwise, this needs to be done.

The authors seems to have controlled for hunger and/or food motivation in the individuals by testing them at roughly the same time of day and by not feeding them in the evening prior to testing. Even so, could it not be the case that what is tested is not really task persistence but rather food motivation or willingness to work for food. Could it be the case that the wolves in this case, found the bait more favorable than the dogs? Could this be controlled for in any way? Or, at least, it should be discussed in the discussion section.
Validity of the findings: no comment
Additional comments: In this study, the authors have investigated the difference in problem-task persistence in socialised dogs and wolves raised under similar conditions. This is important since it can give an alternative explanation to why dogs and wolves differ in their problem solving behaviour where dogs are typically less persistent and instead choose to interact with a nearby human. The authors have used a unique setup of both dogs and wolves with similar experiences of human contact resulting in a very interesting study. Generally the manuscript is well written and constructed and the findings are meaningful.


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: DIFFERENCES IN PERSISTENCE BETWEEN DOGS AND WOLVES IN AN UNSOLVABLE TASK IN THE ABSENCE OF HUMANS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, the manuscript is well-written but there are some sections that need to be rewritten for clarification. I have included several comments into my corrected pdf file.

The literature is well covered but see some of my comments for improvement.

It seems that one animal has been removed from the raw data (.xlsx file). See my comment. This might explain why I was not able to replicate some of their results using the same analyses.

I am not certain all figures should be included. For instance, fig 3 is not easy to read. Please remove or modify.
Experimental design: The experimental design is well thought and original. Excluding humans from the equation to determine whether dogs and wolves differ is very clever (I should have figured it out myself...). However, I have some problems to link the notions of persistence and flexibility to this latter. I see these questions as an afterthought.

For myself, I would have preferred that the authors had focused on testing the difference between both species first, and then, had examined the factors that could contribute to the differences, if dogs and wolves differ. The way the manuscript is written, the factors that could explain why dogs and wolves differ are examined first before testing the difference between dogs and wolves and this is not in link with the premium questions asked by the authors.

I would appreciate if more details were provided when describing the different behaviours measured by the authors and why they selected these particular behaviours. Also, as mentioned in my comments, I wonder if the behaviours were mutually exclusive one from each other. See lick and touch/lick as an example.
Validity of the findings: Having access to the dataset, I have attempted to replicate some of the results presented by the authors. Overall, I was not able to replicate the analyses.

1) I suggest to remove the two-steps cluster analysis. As described in my R file, this type of analysis is justified when the number of observations (participants) is over 200 (see attached article). In the current study, there were 27 participants. And the analysis was performed on non-normally distributed continuous variables, violating some assumptions for this test. And some variables were discrete (not continuous - as requested by a multivariate approach), with some variables having 2 possibles values. Finally, I think that a discriminant analysis would have been more useful for finding the variables that can be used to discriminate dogs and wolves. It seems to me that the two-steps cluster analysis did not answer the main question asked by the authors but it was rather used to explore the "concepts" that could be used to discriminate dogs and wolves. Just for fun, I have used R to run a two-steps cluster analysis (see R file). I was not able to replicate their results (not surprising with these variables and a small number of participants).

2) I don't understand the rational for selecting some variables in the analyses and excluding some others. Please be transparent here. See attached pdf file.

3) Some variables are discrete (e.g. behavioural variety) but appeared to be treated as continuous. These variables should be fitted using a discrete probability mass function (e.g. binomial) and not a continuous density function. Some variables (e.g. approach posture or likelihood of manipulation) are discrete. But nowhere the authors explained how they have treated them and how they were integrated into the models (e.g. for the cluster analysis).

4) I was pleased to see the use of generalized additive models for location, scale and shape. However, a better justification must be provided relative to the different distributions used to fit the data. Sometimes, instead of "playing" around with the different distributions and find the one that fit the best the data, one has to rethink about how his/her data were collected and sometimes the best option is to regroup the data or split them. Otherwise, one can face the problem of overfitting his/her data (using too much parameters).

5) Sometimes, the authors analyzed separately the two species and sometimes, they  were compared within the same analysis. There is no consistency between the different analyses.

6) I was not able to replicate the Fisher test results... See my R file.

7) The rational for using some variables in different models is not presented.

8) The rational for scaling the subjects' persistence and contact latency is not provided.

9) What were the contrasts (post-hoc tests) used following the GAMLSS models?

10) I don't think that the variable "behavioural variety" is valid. My point is that some animals produced the same behaviour many many times and some animals produced the same behaviour only once. But when compiled for the behavioural variety variable, both animals were given the same score (1).

11) I did not read section 4 (Results) because of all my concerns presented above.

12) I did not read the conclusion as well.
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: DIFFERENCES IN PERSISTENCE BETWEEN DOGS AND WOLVES IN AN UNSOLVABLE TASK IN THE ABSENCE OF HUMANS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I am happy with how the authors have addressed my previous comments on this manuscript. Here are some minor suggestions:

Line 76: Remove an s from task-focussed to focused
Line 119 & 168: Do you really mean “teasing”?

Figure 5. The text in the upper parts of the figure is perhaps a bit too small?
Figure 6. In the generated PDF we got as reviewing material, this figure is much too small to read axis lables and legend.

Tables look good!


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: DIFFERENCES IN PERSISTENCE BETWEEN DOGS AND WOLVES IN AN UNSOLVABLE TASK IN THE ABSENCE OF HUMANS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment.
Validity of the findings: no comment.
Additional comments: This is my second reading of this manuscript. I just want to congratulate the authors for having modified the manuscript in lines with my previous comments, especially those related to the statistical analyses.

The conclusion is also in lines with the data and the results. More interestingly, the authors suggest several nice alternative explanations that need further investigations, such as do wolves display more flexible and adaptative behaviours than dogs.

In brief, I don't have any additional comment. Nice work.


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

Input:
Title: POSTMORTEM TRANSPORT IN FOSSIL AND MODERN SHELLED CEPHALOPODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: English is good, the ms is well-structured, with supporting references. The figures are generally good but some improvement can be made. Figure 1might not be so informative for people in this field but it may be good for the general public. Figure 2 is a copy of a figure in Reyment (1973), but what he exactly did (what kinds of conch parameters he measured and so on) is not clear. This is important because the argument of this paper is mostly based on the experiments in Reyment (1973). For Figure 3, I would suggest adding some explanations of what are w, U and Th, (like w = a/a’ and etc..). The contrast between the orange and brown circles in Figure 7A is not clear. The samegoes for green circles in Figure 7B. I would suggest making a clearer contrast.
Experimental design: The topic of ammonoid and Nautilus postmortem transport is of great interest not only for cephalopod paleontologists but also for a broader range of palaeontologists and biologists.
The research question is clearly stated in a good context.
The methods used are clearly explained to the extent that this study is reproducible.
Validity of the findings: The author’s argument is largely based on the experiments carried out by Reyment (1973), in which he found that the various morphologies of ammonoids correspond to differing buoyancy. But I am wondering about the validity of his study. There are many newer studies which discuss ammonite buoyancy, as the author mentions in the text. I would suggest checking the validity of Reyment (1973) and discussing it thoroughly in the ms. I quickly looked at some data published a couple of years ago by Naglik et al. (2015; Lethaia) and Tajika et al. (2015; Historical Biology), and then calculated masses of the ammonoids without soft tissue (Fidelites, Diallagites, Goniatites and Normannites) and water displaced by the shells. It looks like all the ammonoid shells are positively buoyant in the sea, when phragmocone is empty. When these ammonoids are plotted in Westermann Morphospace, however, it appears that Fidelites and Diallagites are plotted in the “non-buoyant field”, whereas Goniatites and Normannites in the “buoyanct field”. This emphasizes the importance of discussing Reyment’s study (whether it is consistent to newer studies and etc.) more comprehensively. Since no empirical 3D models are available other than the above mentioned ammonoids, the author would be able to apply theoretical models of ammonites to test buoyancy of various ammonoid shell shapes to discuss this. Oxyconic and serpenticonic ammonoids would be very important here. If this kind of work was formerly carried out by some others, it should be discussed here as well.

The conclusion is clearly stated, which is also consistent to the results. The initial questions are answered in the Conclusion.
Additional comments: Overall, I think this paper is good. The postmortem transport potential of cephalopod shells is a key issue for various important paleontological studies. This well-written paper will surely contribute to better understanding of this topic. Although I would recommend this paper for publication, I also would suggest revising the ms before acceptance. Some more comments are as follows.

Line 43: I think a couple of references should be added here.
Line 129–130: Are there any previous studies which observed this?
Line 136–140: If it takes soft tissue a few to several days to get detached from the shell, I would assume that there is also transport to some degree during the time, which is not discussed in the text. Does it affect also the transport potential? This must be related to buoyancy of living animals with soft tissue.
Line 164–166: What happens if you use other morphospace like PCA? Reyment’s and Ritterbush and Bottjer’s species can be also plotted into a non-Westermann morphospace. Is there a specific reason to use Westermann Morphospace for this study? I think you can easily draw a buoyant/ non-buoyant line in PCA as well. I am saying this because I am slightly afraid about some possible modification of original data when you translate the morphometry datasets to Westerman Morphospace parameters (w, Th and U) due to the scaling and normalizing. It may be good to compare results of different morphospaces.
Line 191–193: The author states that original measurements in Reyment (1973) were not available, and thus congeneric species had to be used in some cases. This statement sounds like Reyment’s study is actually not reproducible. I would strongly suggest using at least the same species as Reyment used because morphology within a genus (even within a species) often considerably varies. In particular, whorl width (Th in Westerman Morphospace) should be an important diagnostic characters in ammonoids in general. Finding the same species and taking measurements should not be a lot of work.
Line 195–196: If readers do not have Ritterbush and Bottjer (2012) with them, it is hard to imagine what these parameters are. I would suggest adding a small figure with an ammonite cross section together with these parameters.
Line 206–208: There are no explanations for U, Th, and w here, even though these abbreviations appear for the first time here in the ms. The author explains these in Line 232–248. I would suggest adding a short phrase like “for definition of these parameters see Westermann Morphospace and postmortem buoyancy below”.
Line 232: Same as above. The parameters should be visualized.
Line 269–280: Does the buoyancy increase as Th increases? As stated in Validity of the findings, there appears to be no difference in buoyancy between 4 empirical ammonite models in Naglik et al. (2015) and Tajika et al. (2015). This should be discussed in the method or introduction section.
Line 275: What is the definition of intermediate buoyancy? Is it neutral buoyancy?
Line 281–286: Is there any correlation between the size (conch diameter) of ammonites and position in the field? The size has been discussed in previous studies. I am wondering if the author had a look at it. In fact, there is no information on ontogenetic stage and size of ammonites used for this study, which should be also important.
Line 322–324: I think it is better to make a stronger contrast between the two different circles in Figure 7A. The current ones are not easy to differentiate.
Line 330: What are data sources for the geographic ranges? References would be needed.
Line 377: Maybe N. pompilius is much more abundant than the other species? Just a thought.
Line 386: Looking at Figure 7B, there were also reports on living Nautilus in southern Japan and off Burma. I wonder how the author interprets this. Is it also worth investigating these places? Did these individuals just get lost from their original populations?


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: POSTMORTEM TRANSPORT IN FOSSIL AND MODERN SHELLED CEPHALOPODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I feel that this manuscript is well designed to PeerJ. English is very clear (at least I feel so), because this manuscript is easily understandable even for non-native speaker (=me). The manuscript has sufficient introduction and background to demonstrate. Figures are beautiful, which is relevant to the content of the manuscript. The raw data is shown in figures and supplementary file. Therefore, in this point of view, the manuscript totally follows the standards of PeerJ.
Experimental design: I feel that the experimental design of this manuscript is well organized. The investigation of the manuscript was conducted rigorously with a high technical standard. Therefore, in this point of view, the manuscript totally follows the standards of PeerJ.
Validity of the findings: I found one point that should be revised, to increase the robustness.
(1) How to classify buoyant or non-buoyant shells.
How to classify buoyant or non-buoyant species is crucial to this study. This totally depends on the assessments of Reyment (1973). I feel that the Reyment’s assessment are better to be explained more in detailed, which increase the robustness of this interesting study. In relation to this, I have some questions.
(a) What are the definitions of “buoyant”, “intermediate”, and “non-buoyant”? I cannot understand what these terms means and what are differences. Did shells of such “intermediate” species float, or sink down without surfacing or keep almost neutral buoyancy even after death? After surfacing, “buoyant” shells never sink down? If such shells sink down after some periods of floatation (is this “intermediate”?), how long such shells float and drift? Also, it is much better to explain the definition of “non-buoyant”. Did shells of such “non-buoyant” species sink down without surfacing? If shells of “non-buoyant” species sank down after a short interval of surfacing, this is not “non-buoyant”, which should be mentioned as “least-buoyant”. In line 270, the author mentioned “The lease buoyant taxa”, however in line 274, the author mentioned “non-buoyant”. I feel it is better to discriminate these terms, which mean different post-mortem history (”non” is not equivalent to “least”, at least I think so).
(b) Can we really recognize the taphonomic history (buoyant or non-buoyant) only from shell shapes? I actually have some doubt on the Reyment’s assessments. Even if shell shapes are similar, two species could live in different depth. If so, the taphonomic history of these species are expected not to be same, because the infilling rates of seawater into empty phragmocones after the removal of soft parts are expected to be different, which is related to what water depth the soft parts were removed. This is fully examined in Chamberlain et al. (1981), however, the Reyment’s assessments is in 1973, so that the assessments are probably not include such points of views. Therefore, I cannot understand why “buoyant” or “non-buoyant” can be recognized from shell shapes only.
(c) The infilling rates of seawater into empty phragmocones after the removal of soft parts would also depend on the characteristics of siphuncle tubes. Did the Reyment’s assessments contain this point of view?
(d) If the Reyment's assessments suppose that shells are not to be flooded and therefore never sink down after surfacing, this scenario would be not close to the true, considering the results of Wani et al. (2005). The Reyment’s assessments is in 1973, so that the assessments are probably not include this point. Even so, how can we recognize “buoyant” or “non-buoyant” shells?

(2) Several minor suggestions
I added comments of pdf files, which are minor suggestions. Some of my comments might be trivial or due to my misunderstanding, if so, please ignore it.
Additional comments: This manuscript is of great interest for many paleontologists, especially cephalopod workers, because it provides an interesting information that (1) only highly inflated shells were likely to float for significant periods after death, and (2) the observed fossil geographic range are adequate proxies for living geographic ranges. However, I found some points that should be revised, to increase the robustness. Therefore, I would like to strongly recommend accepting this interesting manuscript for the publication in PeerJ, with minor revision.


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

Input:
Title: POSTMORTEM TRANSPORT IN FOSSIL AND MODERN SHELLED CEPHALOPODS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The author has written a particularly interesting contribution about the contentious issue of port-mortem drift influence in cephalopod biogeography. Overall the contribution is well written and provides a good argument against drift having a heavy influence on biogeographic distribution of ammonites. Moreover, the suggestion of cryptic Nautilus populations is important for potential conservation efforts.
Experimental design: The research certainly fits within the scope of PeerJ. The goals are well stated and the data provided is well documented and annotated. Some comments about the approach are included in the general comments section.
Validity of the findings: I have some concern about the validity of the underlying buoyancy evaluation but validating this data is beyond the scope of the submitted paper. However, the distribution of buoyant shells in the morphospace, as noted in the general comments, doesn't seem to fit the described results.
Additional comments: Pg. 9, line 94 – The author brings up the issue of septal neck length on potential drift behaviour. While I understand this parameter couldn’t be included in the morphological analysis it does bring up the question of Spirula. Spirula has septal necks extending for most of the chamber and the shells do have evidence of port-mortem drifting. The dynamics are of course somewhat different since the shell is internal, but the occurrence of encrusting organisms on the shell and final septum would suggest at least some drifting after soft-tissue detachment. I’m curious how Spirula fits into this picture.

Pg. 14, line 190. Since you had to re-measure Reyment’s data, it perhaps would be nice to try to recreate the PCA of Reyment with your data in order to assess potential differences between your data and his and to assess the reproducibility of Reyment’s data.
This also begs the question, why did you do a Westermann morphospace at all? Why not just do a PCA analysis. I’m a bit unclear as to what benefit the Westermann morphospace has especially after doing a PCA with your data the results are fairly similar.

Pg. 14, line 197, 203-205. Considering that the only shell we have for a “control” for buoyancy assessment is nautilus and variation among extant forms is fairly small, how much do you really trust Reyment’s potentially reductive assessment of buoyancy?

Pg. 15, line 215. How exactly did you differentiate between artificially large geographic ranges and “true” geographic ranges for ammonoids?

Pg. 16, line 240. In the supplementary data, it would be nice to label the data from Ritterbush and Bottjer the same as the other data, i.e., if the U, Th, W, are raw/scaled or normalized.

Pg. 17, line 273. Here you state that the plotted data from Reyment only had two buoyant shells plotting in the non-buoyant field. But when I replotted the data I noticed a cluster of shells from this dataset that plot in the non-buoyant area, including Kamerunoceras, Ovaticeras, Eoderoceras, Amaltheus, among others. What is going on with these guys?
If post-mortem drift occurs infrequently, I would think that some groups would have occurrences that would cluster around their living occurrence area with maybe a handful of occurrences outside of this geographic range. Are there any ammonoid groups that show this kind of distribution? What parameters might we look for in judging a potential drift shell in the fossil record?