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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	This paper is well written and the quality of English is generally excellent – no issues
2.	The introduction is excellent in providing a background and review of the literature.
The literature review is well referenced but some references need to be double-checked and edited (Aranda-Valera (both entries), Garrido Castro 2018). The stated aims and objectives are not precisely defined – I expected a clinical validation paper of an established IMU system but the manuscript seems to try and cover a lot of technical detail as well as introducing several novel procedures/protocols which were applied simultaneously.
3.	The overall structure conforms to PeerJ standards but both technical and clinical readers will find this a difficult manuscript to digest. I believe that the clarity of presentation would be improved by separating out the technical from the clinical discussion - the authors may wish to consider submitting the detailed sections on kinematics as a separate article to a more technical journal. The mathematical basis for IMU calculations is well set out and this will be very useful for a technical audience – but (in my view) distracts from some of the more practical aspects of determining the best testing protocol. Removing some of this detail would allow the authors to focus more clearly on what they have done to develop a viable clinical protocol to measure spinal mobility.
There are a few specific issues that need to be addressed:
a.	Tables – each of the tables has ‘Table 1’ in the text of the table itself. Table 3 should use the same left hand column as Table 2 rather than small images which are hard to make out in black and white.
b.	figures 1,3, 5, and 6 are informative. In Figure 1, the black boxes with green lights are not labelled – were these relevant to the study? I presume that these may have been used for sEMG measurements. Figure 2 and 4 could be omitted from a clinical paper but may be useful for a technical paper. The explanation for figure 6 is not clear enough.
c.	Raw data – Matlab routines have been provided, but not the raw data.
d.	Suggestion for re-organisation. If the technical details were split into a separate publication, the ‘clinical’ section could then be expanded with tables showing the actual ROM detected in different parts of the spine (i.e. the relative contribution of each sensor segment to each planar movement) and with a better reasoned argument about the omission of cervical lateral flexion and trunk rotation. A thoughtful analysis of how many sensors are needed to assess spinal mobility would add greatly to its clinical impact. I have outlined below how the technical part of the article could be enhanced to clarify the impact of applying the kinematic constraints.
Experimental design: 1.	This study does present original primary research although it was not clear to me if they were using previously published kinematic constraints formulae or calculations devised specifically for this study.
2.	Was the research question well defined, relevant and meaningful? I think that a lack of clarity about the main objective is one of the main problems with this manuscript.
a.	The authors suggested that their aim was to establish the concurrent validity of the sensors in axial Spondyloarthritis. They used a novel method to co-locate the optical markers over the IMU sensors and they have succeeded in demonstrating a commendably low RMSE (albeit in a small group of healthy subjects). However, it is not clear whether these low RMSEs were attributable mainly to the close co-location of the sensors and markers, to the use of ‘cushioning’ between the spine and sensors, or to the kinematic constraints used to improve error correction. For the result to be relevant to the reader it should be made clear whether these results could be reproduced by an independent researcher or clinician using the same sensors/software. The authors would also be wise to suggest that a complete set of validation studies for this outcome measure would involve testing the protocol in subjects with the condition & establishing adequate test-test reliability and responsiveness to change.
b.	The researchers have employed a novel layout of IMU sensors to measure spinal movement across the whole spine – rather than the usual cervical and lumbar layouts used in most other IMU studies of the spine. This suggests that the authors intended to establish a novel testing protocol for spinal movement relevant to axSpA. The use of sensors at T1 and T6 to measure thoracic spine movement may well be appropriate and necessary in patients with axial Spondyloarthritis, but the contribution of these sensors cannot be evaluated without an analysis of the proportion of movement detected in each segment. It is a shame that they didn’t include a trunk rotation test in the protocol as most of the movement occurring in the thoracic spine would be expected to be rotational.
c.	Reading the extensive technical sections of the paper one may be tempted to conclude that the main objective was to test a novel amendment to the IMU correction algorithm using kinematic constraints. If these corrections are indeed novel, a detailed review should be published in a non-clinical journal such as ‘sensors (MDPI)’ and the results should be presented methodically to show the impact of the application of kinematic constraints to the RMSEs. It should also be made clear whether the kinematic constraint corrections/algorithms are open source or proprietary.
3.	Standard of Investigative methods. The authors appear to have carried out an ethical study with a detailed method of investigation using careful analysis of raw data.
a.	For a technical audience, more detail may be necessary on the error correction/filtering carried out by the Delsys ‘proprietary Kalman filter’ (Line 112]. The authors present their kinematic constraints in detail and appear to believe that the use of this correction method is responsible for their low RMSE results. It may be worth comparing a recent paper by Lee et al who also reported a systematic evaluation of new kinematic constraints:
"Testing a new correction algorithm for IMU sensors – ref. Lee JK, Jeon TH. Magnetic Condition-Independent 3D Joint Angle Estimation Using Inertial Sensors and Kinematic Constraints. Sensors (Basel). 2019;19(24):5522. Published 2019 Dec 13. doi:10.3390/s19245522"
1.	They used a simplified mechanical model for testing
2.	They studied the effect of magnetic perturbation near the IMU
3.	They compared RMSEs for KF with and without magnetometer correction; KF using kinematic constraints and finally with attitudes taken from the optical reference system.
b.	For clinical readers, the authors have not explained why trunk rotation and cervical lateral flexion were omitted from the measurement protocol. Since rotation is the main movement that occurs in the thoracic vertebrae, one wonders what the point was of including two thoracic sensors. It is impossible to tell from the data presented what these sensors add to the overall movement analysis. Most studies using sensors at L1 and S1 comment on lumbo-sacral movement and whether or not lumbar movement can be accurately and reliably measured. This is important for axial spondyloarthritis, where loss of lumbar flexion is regarded as an early and relatively specific sign.
b.	Overall the basic methodology is well described. The application of kinematic constraints to each planar movement is described in detail in the appendix. This level of detail is only necessary if the calculations are novel to this study.
Validity of the findings: 1.	Impact and Novelty: this is a rapidly developing field, and the results presented do provide important new evidence of the accuracy of IMU sensors in measuring movement in the spine. I am particularly impressed by their use of 3D printing technology to design a bespoke ‘housing’ for the IMU sensor that allows the motion sensor markers to be tightly linked with the sensor positions. This may well be a ‘gold standard method’ for assessing concurrent validity against motion capture systems.
It is difficult to balance the need for technical detail and to keep the attention of a clinical audience who want a simple accurate tool to perform a spinal mobility test. My feeling is that the manuscript probably should be split into two papers: a technical paper and a clinical one.  If the authors intend to provide novel open source algorithms on kinematic constraints to improve the accuracy of commercially available IMU systems then a technical approach is justified and the paper should not be directed at a clinical audience. On the other hand, this development will be of interest to a clinical audience, but for that paper the authors should remove much of the technical detail but focus more on the protocol development and segmental movement analysis. In this paper they would focus more on the reasons for choosing the particular set up and address some issues about how to fully validate the test for clinical use.
2.	In the introduction, the authors do briefly speculate on the reasons for differences between the RMSE in their study compared to other IMU studies. This speculation is reasonable, although the authors should be aware that the RMSE reported in the Aranda-Valera publication was based on ‘full-arc’ rather than ‘half-arc’ measurements.
3.	Completeness of data presentation.
a.	The authors have not presented the summary data relating to the mean range of movement obtained from each of the sensor segments. This should be presented in table format.
b.	The methods overall are statistically valid.
4.	The test ‘protocol’
a.	Selection and positioning of sensors: The positioning of the sensors for testing neck movement has been validated in the past. The positioning of sensors to test lumbar movement has also been tested in previous studies. These sensors were interpreted in isolation rather than in a ‘daisy chain’ configuration. The use of palpation to identify the correct position of vertebrae is of questionable validity and may lead to problems with repeatability especially in patients with a high BMI.
b.	The rationale for the additional inclusion of thoracic sensors for measuring trunk movement was not clearly stated. The authors claim to have followed Lee (2011) ‘with minor modifications’ [line 123]– but Lee did not use a sensor at T6. In fact, in this paper movement at T1 was minimal on flexion and extension (as expected). In particular, anatomically there are constraints on movement in the upper thoracic spine that would predict very little movement in the region of T1 to T6. There might be some movement between T6 and L1 but in this region the main movement would be expected to be trunk rotation (which was not tested).
c.	The authors mention that they are testing ‘functional movements’. They have actually selected some but not all of the classic planar movements
i.	Functional movements of the spine are ‘multi-dimensional’ and not restricted to movements in the sagittal and frontal planes.
ii.	It is also unclear why they chose not to include trunk rotation as this would be regarded as a functionally significant movement.
iii.	The figure demonstrating lateral flexion shows lateral flexion occurring in both the lumbar and cervical spine, but in this study the cervical lateral flexion was not measured – why was this not considered a ‘functional’ test?
5.	Conclusions: Although this is a small study, I think the authors are justified in concluding that their study does establish the 'concurrent validity' of the IMU sensors. Whilst they do say that this study is the first step in the validation process, they have not made it clear what other studies need to be performed to validate this as a clinical outcome tool. For instance, there is no mention of the need to test repeatability and responsiveness to change in patients with AS.
Additional comments: I would commend the authors on performing and presenting the results of an important study establishing the concurrent validity of IMU sensors in measuring spinal mobility. This manuscript represents a significant contribution to our understanding of how spinal mobility can be measured accurately in patients with axial Spondyloarthritis and will be appreciated by clinical researchers in this field. If there is a weakness it is that the authors have tried to pull together all the technical and clinical information into a single article - I feel that if this is not addressed the article will not have the desired impact, particularly among clinicians.


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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The structure of the article is correct, and the mathematical analysis is well explained. The supplementary data are abundant and complete. English grammar is good.
Experimental design: The study is very interesting and could have its application in axial spondyloarthritis (axSpA), although the number of subjects is very small it is explained that is only a protocol design for a future clinimetric validation study.
Validity of the findings: To develop new methods for functional assessment in patients with AS is very important and relevant. The classical evaluation methods, currently used, were defined in the 90s and are based on very basic instruments (tape measure and goniometers). The study proposes the use of advanced technological tools (IMU) for the evaluation of the patient with AS. The objective is very interesting, in the present study a protocol testing is made on five healthy subjects. The method and calculations are very interesting, and could be useful for future studies.
Additional comments: The study proposes the use of inertial sensors (IMU) for the evaluation of spinal mobility, taking into account measurements similar to the already used in the mobility assessment of patients with axial spondyloarthritis (axSpA), although they are indirect measurements and with tools with low precision and reliability. Describes a series of algorithms and formulas to evaluate spinal mobility (cervical, thoracic and lumbar). The results compared with a motion capture system, as Gold Standard, are good.
Changes in the original manuscript are done in this new version indicating that the study is a protocol design instead a complete clinimetric validation study on axSpA patients.
All changes suggested to the authors has been improved in the new version of the manuscript, and in my opinion the article must be accepted.


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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: The experimental design is sound and reproducible. However, the clinical applicability is questionable, since no patient was tested. It is well known that psychometric variables are population dependent. It is not possible to assume that the assessment protocol can be applied in the same form to a sample of patients with Axial Spondyloarthritis.
"This issue was not adequately solved. Indeed, the Title of the study is focused on Axial Spondyloarthritis although no patient was assessed."

No “a priori” sample size was performed.
"The sample size was 5 subjects in this study. No sample size calculation was done for this sample size."

Why no reliability calculation was performed? IMUs and Qualysis assessment could be assessor dependent. Thus, the consistency of the results should be determined.
This issue was not fixed. No ICC/SEM/MDC was obtained.

Some parametric tools were used, such as Pearson correlation coefficient, but the distribution of data remains unclear, even more when only 5 subjects were assessed.

"Although same data were not normally distributed, there is not any non-parametric tool in the statistical analysis."
Validity of the findings: The authors consider that the system is validated, but they only assessed five healthy individuals. More tests are necessary, performed in different types of patients, in terms of clinical stages and sociodemographic/anthropometric features, to affirm that any assessment protocol is valid.
The only clinical comments are in the last paragraph of the Discussion. The absence of an adequate clinical perspective limits the applicability and relevance of the results.

"The changes performed are insufficient to solution these concerns."
Additional comments: The study looks like a feasibility or even a pilot study, more than a validation study.
The experimental design is sound and reproducible. However, the clinical applicability is questionable, since no patient was tested. It is well known that psychometric variables are population dependent. It is not possible to assume that the assessment protocol can be applied in the same form to a sample of patients with Axial Spondyloarthritis.
An “a priori” sample size and a data distribution evaluation is lacking.
Each study objective should be associated to each analysis to improve the quality and understandability of the results.
The consistency of the results should be determined with a reliability analysis approach.
According to this review, the conclusions are clearly overestimated.

"These issues were not adequately fixed."


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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 2
Reviewer: 3

Output:
Basic reporting: •	The description of the statistical methods and in particular the calculation of sample size has been improved.
•	The range of movement is now clearly indicated in the Table which is much more informative.
•	The references have been reviewed and corrected.
•	The statement that this was a clinical validation has now been correctly modified to a ‘protocol validation’ and the authors have clarified that this will lead to a clinical validation study with a view to developing a new spinal mobility index. This satisfies my concerns to be clear that this is a technical protocol development rather than a clinical study.
•	The tables and figures have been modified to improve clarity, and I am satisfied with the changes.
Experimental design: •	The authors have clarified that the use of constraints presented in this study does represent novel research and will be made available to researchers in the future.
•	The authors have justified the placement of reflective markers on the sensors & clarified that the use of constraints contributed the greatest part to the reduction in RMSE.
•	The authors have defended the use of a series of sensors along the spine. I have no problem with them using that many sensors but I still don’t feel that they have fully explained the rationale for the number and positioning of each sensor. If they were able to reduce the error in rotation measurements (I understand that correction for gyroscope drift is now possible with several IMU brands) that these sensors on the thorax would be most useful in measuring rotation. I also would recommend that they do not regard the BASMI as a ‘gold standard’ but instead aim to measure the major movements in each part of the spine. However, these comments are more for future reference and I am happy with the wording of the revised article.
•	They have now referenced a relevant paper by Lee that also described a useful approach to the use of kinematic constraints.
Validity of the findings: •	I am satisfied with the further clarification provided in the revised article.
•	The authors have defended the use of digital palpation to identify positioning of vertebrae.  They have quoted relevant literature to defend their position and I would accept their response. However, I would recommend that the authors state that they measured the distance between the spinous processes C7 and S1 using a flexible ruler using the method of Ernst et al (2013) to determine the location of T1, T6 and L1.
•	I would agree with the authors that it would be wrong to presume at this stage whether or not thoracic sensors will be useful in carrying out measurements in axSpA. I would encourage them to consider measuring thoracic rotation in a future clinical study.
•	With regard to the choice of particular spinal movements to test rather than others, the authors have explained that some of the movements can be corrected better using the constraints method. That’s a valid reason, but it could be stated more clearly in the article.
•	Line 451 needs to be edited.
•	I am happy with the revised discussion and conclusions
Additional comments: Thank you for your detailed response & the further explanation you have provided. I'm satisfied with the changes/improvements to the manuscripts. Just a couple of minor edits needed as far as I'm concerned.


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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 3
Reviewer: 1

Output:
Basic reporting: Thank you for the opportunity to review the new version of the paper.

The issues were adequately fixed. No other concerns were identified.
Experimental design: The issues were adequately fixed. No other concerns were identified.
Validity of the findings: The issues were adequately fixed. No other concerns were identified.
Additional comments: Congrat for this good job.


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

Input:
Title: A NOVEL IMU-BASED CLINICAL ASSESSMENT PROTOCOL FOR AXIAL SPONDYLOARTHRITIS: A PROTOCOL VALIDATION STUDY
Review round: 3
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The further revisions to the document are satisfactory and I have no further issues with the wording or content of this section.
Validity of the findings: I remain satisfied by the statistical arguments put forward. The authors have clearly stated that a further study is required for a clinical validation of their proposed method.
Additional comments: No additional comments


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

Input:
Title: A TRACE FOSSIL MADE BY A WALKING CRAYFISH OR CRAYFISH-LIKE ARTHROPOD FROM THE LOWER JURASSIC MOENAVE FORMATION OF SOUTHWESTERN UTAH, USA
Review round: 1
Reviewer: 1

Output:
Basic reporting: I think that this is an interesting manuscript that presents unique findings that are of interest to the paleontology community, but it needs revision before it can be published. There are numerous issues with the manuscript as it is written that the authors should address:

The first of these issues is in how the authors use the word ichnotaxon, which is used as a synonym for an ichnospecies. A taxon, however, is any grouping at any rank, so an ichnogenus is also an ichnotaxon. Given that, it is not quite right to claim that the fossil that they describe is not a variant of any given taxon, because its general morphology is the same as Siskemia, as they note on lines 447 through 449. The only objection that could be raised is that Walker (1985) included a width measurement in her diagnosis of Siskemia, but as the present authors note on line 652 (and I agree with this), size is not a valid ichnotaxobase. It is fair to say that their specimen does not fit into any known ichnospecies of Siskemia, but saying that it doesn't fit any taxon is a bit too much of a stretch because its general layout fits the definition of Siskemia sans the measurement.

The second issue is in regard to the ichnotaxonomy and comparison sections, where the authors include track makers in their analysis. See, for example, lines 443 and 444, where they note that Getty et al. (2013) attributed the Siskemia that they studied to archaeognathans. Getty et al. (2013), however, did not imply that all Siskemia are the traces of archaeognathans. Based on the attribution of some specimens to archaeognathans, the present authors reject the idea that their trace falls within the hypothetical continuum for Siskemia. The original Siskemia specimens described by Smith (1909) were probably made by a different group of arthropods, so considering only archaeognathans in a hypothetical continuum is too narrow a view.

Here are some additional comments:

Title- the wording is a bit odd as it is written. Even though the hyphen indicates a compound adjective, I think that most readers will quickly look over the title and come away thinking how does a trace fossil walk. I recommend rewriting it as follows (or something like this): "A trace fossil made by a walking crayfish or crayfish-like arthropod...

Abstract- The whole point of this paper is to describe a previously unknown trace fossil morphotype from the SGDS, so leading off with a statement that the trace fossils from said site are well understood is a bit odd. I think that what the authors mean is that the vertebrate traces are well understood since they have been published on much more, and if this is correct, then I recommend rewording. Also here and elsewhere (as I discuss above), the specimen is a variant of the ichnogenus Siskemia, so it is a variant of a known ichnotaxon.

Introduction- Given that the paper is about a hitherto unknown crayfish or crayfish-like arthropod trace, some attention to what is known about fossil crayfish traces should be mentioned here to set the stage for the paper.

Materials and methods- there is no discussion of which measurements are actually taken. This should be added here, and I also recommend a figure to illustrate these measurements. It's not until we get to the description and the table that we have any idea of what measurements were taken. I also recommend taking measurements of the width between the inside and outside of the track rows and then doing a simple analysis that compares the track row width to the width of the medial impressions between your trackway and those of the other Siskemia species; doing so will show how much your specimen is distinct from previously described specimens.

Description-
Line 140 (and elsewhere in the manuscript)- are the sets closely appressed to each other or are the tracks within the sets closely appressed? It seems like the latter is meant, so rewording should be done to clarify.
Lines 144, 147, and 204- I recommend avoiding anatomical terms for bodies, such as cranial, and stick with words such as anterior.
Line 145- how is staggered with half a cycle of displacement different from alternating?
Line 166- add text about the ratios of width between track rows and width of the medial imprints here

Comparison- this is a very lengthy section for a good reason: the authors conduct an exhaustive comparison between the fossil that they are describing and previously described ichnospecies. I commend them for this because few authors do this. I do think, however, that this section should actually be moved to after the one on the trace maker because most readers will be more interested in what made the trace than what ichnotaxon it belongs to.
Line 212- D aenigma can't be the holotype if it were never designated as such. It could only have lectotype status.
Lines 452-453- the authors could point out here that the medial impressions of other Siskemia ichnospecies don't undulate, whereas the ones of the specimen that they are describing do

Discussion (Trace maker)- this is the most important part of the study, in my opinion. A stronger case should be made here that the trackway is that of a crayfish. The best way to do that is not by eliminating ichnotaxa, but by going to the neoichnological studies. One thing that I think is really important here is a close-up photograph of one of the crayfish trackways illustrated by Fairchild and Hasiotis (2011). A comparison of the trackway from figure 2E of Fairchild and Hasiotis with the fossil trackway would be especially compelling. As it is, the line drawing in Figure 4 (MM to NN) is very small and interpretive. Let the readers see how compelling case is for themselves. If the authors are unable to get an image from Fairchild or Hasiotis, I can provide them with one (although the medial impressions don't undulate in that experimentally produced trackway).

Conclusions- undulating isn't the opposite of linear

References- Olsen and Huber is correct here, but the in-text citation is misspelled as Olson and Huber. Also, Schindewolf (1928 isn't cited in the text).

Figures- I recommend deleting the northeastern USA and the southern tip of Texas from Figure 1A because they look like they are supposed to be part of Utah, but they aren't. I also recommend adding two figures: one on the measurements and another that should be  aside-to-side comparison between a modern crayfish trackway and the fossil.
Experimental design: The research background (i.e., what is known of crayfish trace fossils) could be better stated in the introduction.

I also strongly urge some additional measurements be taken. I've already mentioned these above, but I'll expound on them here. One of the three ways that the fossil described in this trackway is different from other ichnospecies of Siskemia is that its medial imprints are widely spaced relative to the rest of the trackway. This difference can be quantified by measuring the outer trackway width and then plotting this relative to the distance between the medial imprints. This will have to be done for the other Siskemia ichnospecies so that the comparison can be made.
Validity of the findings: I think the authors have a strong case that they have found a crayfish or crayfish-like arthropod trackway, but that they could do a better job in showing this to the reader with the side-to-side comparison figure that I recommend.

I do not agree with their statement that the trackway that they describe does not fit into any ichnotaxon, because it fits into the ichnogenus Siskemia. I do suspect, however, that they are right that they have a new ichnospecies, but I'd like them to show some measurements on a figure to demonstrate that the medial imprints are wider relative to the rest of the trackway than they are in other Siskemia ichnospecies.
Additional comments: No additional comments


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

Input:
Title: A TRACE FOSSIL MADE BY A WALKING CRAYFISH OR CRAYFISH-LIKE ARTHROPOD FROM THE LOWER JURASSIC MOENAVE FORMATION OF SOUTHWESTERN UTAH, USA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear profissional and native English;
Great literature review; unfortunately it is based on a single specimen
Professional structure, excellent figures
The comparison with crayfish-like trackways is well supported by literature comparison, especially with neoichnological data. Although highly variable morphology of modern crayfish trackways depends on the type and consistence of the substrate the single specimen studied can be positively compared with them. The fact that only up to 3 tracks are found in the trackway' sets of imprints do not discard the possibility of being produced by crayfish but there are insect producers attributed to the ichnogenus Siskemia, to which the specimen was attributed, and also a clearly difference in size. It would be relevant to have different specimens to compare preservational variants. A single specimen do not allow to have definite conclusions.
Experimental design: The paper is based on a rigorous investigation and is basically a ichnotaxonomic paper very well supported by a deep comparison with known ichnotaxa.
Validity of the findings: Until this paper, examples of fossil crayfish trackways have yet to be
described in detail, although they have been presented in figures (e.g.,
Hasiotis, 1991; Rainforth and Lockley, 1996); there were no ichnotaxa
readily attributed to crayfish locomotion.

The fact that only up to 3 tracks are found in each trackway set of imprints do not discard the possibility of being produced by crayfish but there are insect producers attributed to the ichnogenus Siskemia, to which the specimen was attributed, and also a clearly difference in size. It would be relevant to have different specimens to compare preservational variants and locomotory patterns, including the number of legs involved in locomotion. A single specimen do not allow to have definite conclusions.

The single specimen resembles a crayfish-type walking trace and comes from a stratigraphic succession with clear importance for understanding the evolution of early freshwater decapods, Thus, this paper may bring some important implications in the discussion about the evolution of the Astacida.
Additional comments: Great ichnotaxonomical review of arthropod repichnia! I like especially Fig. 4.


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

Input:
Title: A TRACE FOSSIL MADE BY A WALKING CRAYFISH OR CRAYFISH-LIKE ARTHROPOD FROM THE LOWER JURASSIC MOENAVE FORMATION OF SOUTHWESTERN UTAH, USA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I've gone over the manuscript again and think that the authors have made most of the substantive changes that I recommended. I think that the article should be considered ready for publication at this point.
Experimental design: They have addressed my concerns about experimental design
Validity of the findings: the authors have done a better job explaining their findings in the second version of the manuscript
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: ROCKS OF DIFFERENT MINERALOGY SHOW DIFFERENT TEMPERATURE CHARACTERISTICS: IMPLICATIONS FOR BIODIVERSITY ON ROCKY SEASHORES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear and unambiguous, professional English is used throughout. Literature references and  sufficient field background/context are provided. Tables and figures are appropriate. Hypotheses are not stated - objectives refer to methodology.
Experimental design: The question is well defined but not meaningful. Too what extent does a  boulder on turf mirror rocky shore conditions?
Validity of the findings: Impact under real circumslances on the shore was not assessed.
Additional comments: This study involved collecting temperature data from the surfaces of rocks, with a view to better understanding the thermal heterogeneity experienced by intertidal rocky-shore life. The idea was (I think) to deconstruct this typically complex set of circumstances that influence body temperatures, by isolating rocks and studying them away from the shoreline. Essentially, the study aimed to describe how rock type, elemental composition, and upper or lower surface affected the temperature. The results were always very predictable; for example the upper surfaces become hotter than lower surfaces, and so on.

I am not convinced that the idea behind this project has really worked out, and that the findings contribute to improving understanding of rocky-shore thermal heterogeneity. It is unclear how these data can be applied or used to predict the temperature conditions on a shore. In my view there is no clear context for the data, and perhaps some effort should have been made to integrate the data into a predictive heat budget model. I also had several issues with the methods; too what extent does a  boulder on turf mirror rocky shore conditions?

Whereas rock substratum characteristics are important there are several other equally important factors that effect thermal regimes on rocky shores, such as angle of the shoreline, gradient of the surface (azimuth), wind, and so on. All of these conditions vary from one shore to the next, and some vary within a shore at at fine spatialscale. All should be built into a heat budget model to predict shoreline temperatures.


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: ROCKS OF DIFFERENT MINERALOGY SHOW DIFFERENT TEMPERATURE CHARACTERISTICS: IMPLICATIONS FOR BIODIVERSITY ON ROCKY SEASHORES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: no comment - see below
Validity of the findings: no comment - see below
Additional comments: Review of article 50962v1
Janetzki et al
General comments

Abstract
Fine no comments
Introduction
L7: Probably not necessary as this is common knowledge…..or should be.
L98: talks of ‘behaviour’ but that is not really a feature of inanimate objects, would suggest  changing to ‘thermal regime’.
L101-106: These objectives are confusing. Not sure how objectives 1, 2, and 3 differ? Also if you are looking at maxima, wouldn’t you also specify minima? Objective 4, I would have thought this was implicit in the fact that they are different rock types and this would have been quantified before experiment began, thus not really a specific objective.
Methods
L114: what volume were the boulders? Also was shape standardized? Ideally they would be spherical or as close as possible to ensure comparisons were accurate and fair. A long sausage shaped boulder will not have the same thermal properties as a squat spherical one. More detail around this is needed.
Results:
Fine, potentially a bit long.
Discussion
L528: need to distinguish that this may be more problematic for sessile organisms such as oyster’s mussels etc. Mobile invertebrates will either seek boulder undersides or enter heat coma and roll down shore.
Importantly however, need to make mention that a significant caveat is differing rock dimensions tested….this is highly important for thermal properties of what you are testing and may confound some of your findings.


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: ROCKS OF DIFFERENT MINERALOGY SHOW DIFFERENT TEMPERATURE CHARACTERISTICS: IMPLICATIONS FOR BIODIVERSITY ON ROCKY SEASHORES
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper is rather lengthy for the amount of new material presented, and there are several places where more detail and clarification are needed (see below in general comments). Overall however the paper is clearly written.
Experimental design: There are some issues with the issue of the infrared camera using factory settings (see below).
Validity of the findings: See below.
Additional comments: X et al. experimentally explore the role that role minerology may play in driving temperature patterns in rocky intertidal shores during aerial exposure at low tide. I agree wholeheartedly with the authors that this is an understudied but potentially important mechanism that to this point has been largely ignored. This study provides an interesting entre into this question.

The introduction, while well-written, really needs to take a deeper dive into the mechanisms of why rock characteristics might be expected to drive patterns of temperature, and how this would be expected to influence patterns in the field. Doing so would also clear up some mis-statements that are made. For example, in several places the authors focus on the top sides vs undersides of rocks, and are correct that a major driver of differences is simply sun vs shade. But, as Ray “hot rocks” Huey et al. first showed in 1989, this is also strongly affected by the size (thickness) of the rock, which belies the idea that one can simply compare “tops vs bottoms” as in line 31.

In brief, there are several physical reasons why rock physical characteristics can drive temperatures, and these really need to be considered more carefully when interpreting these results and recognizing potential limitations of the approaches used. First, rock surface characteristics (albedo/reflectivity) can affect the total amount of solar short-wave radiative energy that is absorbed, i.e. white chalky rocks likely reflect more solar energy than do dark basaltic rocks.  Similarly, the surface emissivity of the rock determines release of infrared (long wave) energy. This is important, because the team measured surface temperatures using an infrared camera set at the factory default of 0.95 (line 187).  This is probably ok, but it is important to note that because this wasn’t tuned to each rock type (which would be done by changing the emissivity on the camera until it recorded a temperature that matched that of a thermocouple) any potential role of emissivity is ignored.  Once the heat energy enters the rock, the temperature change will be largely determined by its specific heat capacity and density. So, a very dense material will exhibit comparatively small changes in temperature for any given amount of heat energy input. Finally, the rate at which heat is conducted to the bottom of the rock will be driven by its thermal conductance (a material characteristic) as well as the rock thickness.  These latter reasons are the underlying mechanisms driving the different temperatures recorded by Huey et al under rocks of different thickness.

None of this invalidates the study, but instead it urges caution in statements that imply that one rock type is “hotter” than another (line 62), or that these differences can be untangled purely using experimental approaches.

Along these lines, the paragraph that begins on line 36 needs clarification. There are now quite a few studies that have measured baseline conditions of rock temperature on shorelines using temperature loggers, see for example a host of papers by Lima and Seabra. Realistically, however, one can’t measure temperatures on every shore or indeed on any microhabitat on any given shoreline. To try to tackle the latter, one needs to use heat budget models and again there is now a pretty long history of this from research groups such as mine (Helmuth), Wethey, Lima and Denny. The quite valid criticism of these modeling approaches- and where studies such as the one presented here provide significant value- is that they have almost universally made assumptions about rock type by, for example, assuming that an entire shore is made of granite or concrete. This study shows that rock type (for likely all of the reasons above) can potentially play an important but neglected role in driving patterns of heterogeneity in temperature.

A few more specific points and questions:
Line 164. I’m not sure what the point of this was. Am I reading this correctly that rocks were only submerged for 20 minutes?  This certainly would have wetted their surfaces, but since you allowed them to dry I assume you were trying to cool them to the same starting temperature, as would normally occur in an intertidal zone as the tide rolle out? From your data, can you confirm that they were all at the same starting temperature as one another at 9:00 at the start of each trial?  If so (or if not), this should be mentioned.

Lines 300-307. How did you quantitatively distinguish between a gradient and a mosaic? The examples shown in the figure seem pretty straightforward, but I am guessing there were some intermediates. Do you do some sort of spatial regression or other method of assessing variance from one spot to the next?

Line 327 Be a bit careful in the interpretation of quartzite- it is likely that at least some of the differences you observed were due to differences in emissivity, which would have falsely shown up as heterogeneity in the IR camera. If you still have the rocks, an interesting experiment to ground truth this would be to record patterns with the camera, and then again with something like a thermocouple to verify that you were recording actual differences in temperature and not just differences in surface emissivity (which would have shown up as apparent temperature differences in the IR camera which may or may not be real).

Line 476 “Air temperature also affected boulder temperature behaviour, with the hottest boulder temperatures measured on the hottest sunny days.” This actually is not evidence of the role of air temperature. Air temperature is driven indirectly by surface temperature, which in turn is driven by solar radiation. So, the reason why air temperature is hot on sunny days is because surface temperature is hot, not the other way around.

Line 495. I’m not sure what you mean here: “While within-microhabitat temperature differences have been described previously in terrestrial habitats (e.g. Huey et al. 1989), these results are novel for intertidal rocky substrata.” There have been a bunch of studies measuring small-scale (cm) differences on intertidal rock surfaces, driven largely by (or assumed to be driven by) differences in shading, which create the microclimates. Here you have shown that these microclimates can be influenced by rock type, but the patterns observed on top of the rock still are a combined influence of small-scale micro shading and rock type- this study doesn’t decouple those (e.g. even sandstone has small-scale features which can drive microshading).  See for example Choi et al. 2019 Conservation Physiology and Pincebourde and Woods 2020 Current Opinion in Insect Science.  Bottom line, I don’t think you are using “microhabitat” consistently. A single boulder is not a “microhabitat” but rather contains lots of microhabitats.

Lines 510-511.  Nope, there actually have been quite a few studies looking at differences in physiology among intertidal organisms exposed to different microclimates.

Lines 524-532 Again here you are ignoring the role of small-scale structures/surface complexity in driving mosaics. Just because you chose rocks with limited surface texturing doesn’t mean these don’t exist, so it is a big stretch to state “Given predictions of an increased frequency of heatwaves and generally hotter air temperatures associated with global climate change (IPCC 2013), hot boulder surfaces with limited heterogeneity may be observed more often.” I agree, figuring this out is important, but you really can’t make this extrapolation based on this study.

Line 541-542: “cooler rock types that only warm small amounts when emersed may offer thermal refuges to thermally-sensitive species.”  As above, be more cautious in saying that one rock type is “cooler” than another.  For example, rocks with a high density and high specific heat capacity will that more slowly, but they will also cool more slowly and during long exposures (especially high on the shore) they may ultimately heat to higher temperatures.

Line 586: “However, our results, in conjunction with those published previously for the same siltstone boulders (Chapperon and Seuront 2011a; Chapperon et al. 2013), suggest that the magnitude of temperature relief that biota experience under boulders is actually quite small (<5 °C) when compared to temperature differences of up to 25.5 °C between sun-exposed and sun-protected microhabitats elsewhere on rocky seashores (e.g. Denny et al. 2011; Lathlean et al. 2012).” This is extrapolating well beyond your data. True, you only observed a 5C difference but then you also only recorded temperatures after 4 hours and many exposures can be much greater in the high intertidal zone. And, as above, rock thickness probably plays a much bigger role than rock type.

Lines 630-642. I would delete this paragraph. All it basically says is that the sun heats rocks and that is hardly surprising.

Lines 653-659. Again, I’d suggest cutting. This study certainly informs such studies, but these data alone from this one site likely won’t provide the baseline data needed to design experiments on different shores.


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: ROCKS OF DIFFERENT MINERALOGY SHOW DIFFERENT TEMPERATURE CHARACTERISTICS: IMPLICATIONS FOR BIODIVERSITY ON ROCKY SEASHORES
Review round: 2
Reviewer: 1

Output:
Basic reporting: n/a
Experimental design: n/a
Validity of the findings: n/a
Additional comments: I am happy with changes and clarifications made to revised manuscript


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: ROCKS OF DIFFERENT MINERALOGY SHOW DIFFERENT TEMPERATURE CHARACTERISTICS: IMPLICATIONS FOR BIODIVERSITY ON ROCKY SEASHORES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The paper is well written and while still a bit long is much better than the first revision.  Nice job in responding to reviewer comments.
Experimental design: There are still some issues with the generic value of emissivity used, and of the use of the term "gradient" which has a very real physical meaning, as opposed to the qualitative way it is used here.  I have made some suggestions in the draft.
Validity of the findings: Fine
Additional comments: See attached


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: DELIMITING THE GENERA OF THE FICINIA CLADE (CYPEREAE, CYPERACEAE) BASED ON MOLECULAR PHYLOGENETIC DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article has a clear structure, is well written and provides enough background information. The quality of the used methods, interpretation of the data and other content is very high.

Figures and tables are clear and relevant to the content.

In some parts of the texts such as the 'Discussion' chapter should be carefully checked for grammar, such as for lacking articles. I marked some of these with sticky notes is the PDF.
Experimental design: This study forms the next stage in a continuous effort of the authors to understand the molecular phylogeny of the Ficinia clade of Cypereae and its implication on the taxonomy of this challenging group.  This study provides further essential basis for a modern generic classification of Cypereae, and provides the foundation to tackle a final big challenge on this group: a modern monograph of the genus Ficinia. It is not the first molecular study performed on this group and most findings coroborate previous studies. However the use of a large array of markers from both nuclear and chloroplast DNA, state of the art analysis methods and a translation of the results to taxonomical changes within the group of study, make this article worth publishing in PeerJ.

The used methods (choice of markers, statistical analysis, …) are well chosen and correctly applied. As all sequence data are or will be available from Genebank, this study is replicable.
Validity of the findings: The authors use a critical language. Results are well analyzed and conclusions are well stated. Underlying data have been provided.
Additional comments: I have a few suggestions and questions which could enhance the quality of this article, however I my opinion these are not essential to the acceptance of this article for publication:

An additional plate with (field) photographs showing key morphological & ecological characteristics of typical core Isolepis vs core Ficinia (e.g. chartaceous vs coriaceous glumes) and of the species newly transferred to Ficinia would be valuable.

Isolepis species either have a Cyperus or a Ficinia embryo type. As the Ficinia type is derived from the Cyperus type, the latter is expected to be present only in the most basal clades of Isolepis. Is there support for a unique origin of the Ficinia type embryo? Did the authors check the occurrence of the embryo type with the different clades found in the nuclear vs chloroplast analysis? Especially for Isolepis hemiuncialis, incomtula, … of which the position is currently still unclear, this might add information? In addition I suppose the taxa newly transferred to Ficinia all have a Ficinia embryo type?


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: DELIMITING THE GENERA OF THE FICINIA CLADE (CYPEREAE, CYPERACEAE) BASED ON MOLECULAR PHYLOGENETIC DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The reporting in this paper is very clear.

The introduction starts with a very comprehensive description of the taxonomical history of the Ficinia clade, followed by the challenges on
distinguishing Ficinia from Isolepis and the dificulties with the delimiations. A very clear aim is stated:
"The aim is to establish whether the genera in the Ficinia Clade, particularly Isolepis and Ficinia, are monophyletic, and to evaluate what characters diagnose the inferred (sub)clades."

With the material and method section gives enough detail to be able to reconstruct this research.

Result are clearly reported, easy to follow with the figures by hand.

The discussion handles the 'research question' / aim of this paper.

After reading this article, the "research question" is fully answered. This paper is very well structured: after reading this paper only once I could fully grasp the outcomes and understand the results. The text is not too long and easy to comprehend, which makes it very accessible for everyone interested in this subject!

The taxonomic treatment with a key to the genera is very useful.

The figures are good. Although, I would summarize the cut-out part of the 1A and 1B trees as 'Cyperus-clade' (or outgroup), as done in Fig. 2.  Also, I would annotate Cyperus clade and Ficinia-clade on the trees?

Some small inconsistencies were found in the references, I annotated these in the pdf.
Experimental design: There is a well defined research question & aim in this paper: 'Investigating the generic limits of the Ficinia-clade'. The aim is to establish whether the genera in the Ficinia Clade, particularly Isolepis and Ficinia, are monophyletic, and to evaluate what characters diagnose the inferred (sub)clades.

This is very relevant. In the last decade there have been many changes within the Cyperaceae family and this paper handles one of the still unresolved issues.

With the material and method section gives enough detail to be able to reconstruct this research. I am happy to see that nuclear and plastid markers are not concatenated into one matrix but analysed separately. The large species sample makes this research very relevant!
Validity of the findings: I encourage the pragmatic approach that was chosen in adopting a classification framework based on the nuclear phylogeny (and thus recognizing clades that minimize nomenclatural changes).

 The data on which the results and conclusions are based are available.

The conclusion is very well stated and there is a clear link to the original research question. Conclusion are based on the supported results.
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: DESCRIPTION AND REDIAGNOSIS OF THE CRESTED HADROSAURID (ORNITHOPODA) DINOSAUR PARASAUROLOPHUS CYRTOCRISTATUS ON THE BASIS OF NEW CRANIAL REMAINS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Reviewer: Andrew T. McDonald

This is an excellent description of an important new specimen that clarifies long-standing ambiguity regarding the crest of Parasaurolophus and sets the stage for future work on the extensive Kaiparowits sample. Very little revision is necessary. I would suggest adding two brief thoughts to the Discussion.

1. In the "Phylogenetic and biogeographic considerations" section, perhaps mention that your results, with P. cyrtocristatus and P. tubicen as sister taxa, indicate that P. tubicen and P. walkeri evolved their elongated crests convergently, but that P. tubicen is more similar to P. cyrtocristatus in having a dorsoventrally broader crest. As you note in the next section, the crest of P. cyrtocristatus is broader than that of P. walkeri but narrower than that of P. tubicen.

2. In the "Comparison to the Kaiparowits Formation Taxon" section, in the last paragraph in which you tentatively identify the Kaiparowits specimens as P. cyrtocristatus, you could mention that other recent studies have found additional close relationships between the ornithischians of the Kaiparowits Formation and Fruitland/Kirtland formations. These include the ankylosaurines Akainacephalus (Wiersma & Irmis 2018) and Nodocephalosaurus (Sullivan 1999), and the chasmosaurines Utahceratops (Sampson et al. 2010) and the lineage of Pentaceratops-Navajoceratops-Terminocavus (Fowler & Freedman Fowler 2020).


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: DESCRIPTION AND REDIAGNOSIS OF THE CRESTED HADROSAURID (ORNITHOPODA) DINOSAUR PARASAUROLOPHUS CYRTOCRISTATUS ON THE BASIS OF NEW CRANIAL REMAINS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a great contribution to our understanding of lambeosaurine hadrosaurid anatomy and evolution, derived from a beautiful and exquisitely preserved specimen. The text is very clear and concise, and the descriptions are particularly insightful and contain a wealth of detailed information on the comparative osteology of Parasaurolophus (except in the case of the dentary, but I comment on that below). The figures are excellent, of great quality and very informative, enhancing the data provided by this study (I, however, have some minor remarks on the orientation of some of the elements, but see below). I agree with pretty much all the results and conclusions presented here, which are supported by sufficient evidence as documented here by the authors. Thus, I certainly recommend publication of this study, with the minor revisions detailed below.
Experimental design: Field Methods

Line 164: “Collection of DMNH EPV.132300 occurred in the Bisti-De-Na-Sin-Wilderness in
collected under Bureau of Land Management permit NM14009S.” I would delete “in collected”.

Phylogenetic Methods

How many replicates in the heuristic search?
Validity of the findings: Revised diagnosis of P. cyrtocristatus:
Line 293-294: “Preorbital portion of premaxillae straight, not convex”. I am looking at the lateral view of the holotype skull of P. walkeri, ROM 768, and I am also seeing a straight preorbital portion of the premaxillae. Thus, I would remove this character from the diagnosis of P. cyrtocristatus. What appears different to me in P. cyrtocristatus is that the preorbital region of the premaxillae (as shown in FMNH P-27393) is slightly, very gently, concave.

Line 294: “long common median chamber present that is equal in dorso-ventral breadth
to the bounding narial tracts”. Since other combinations such as “caudoventral” and “proximoanteriorly” have been written without a hyphen, I would write “dorsoventral” rather than “dorso-ventral”.

Description:

Lines 320-322: “In P. cyrtocristatus, FMNH P-27393, the dorsal processes propagate up the
dorsal surface of the skull in an autapomorphic straight line, which differs from the more
convex growth of the premaxillae seen on P. walkeri (ROM 768) (Fig. 1).” I see that happening when not restricting this condition to the preorbital region.

Lines 462-464: “However, unlike species such as Hypacrosaurus stebingeri (MOR 553S 7-27-2-93), Hypacrosaurus alitspinus (Evans, 2010), Corythosaurus (AMNH 5386), and Olorotitan
(Godefroit, Bolotsky & Bolotsky, 2012)”. But the species of Corythosaurus and Olorotitan are not given here, just the genera. Also, it should be written H. altispinus.

Line 570: “Laterosphenoid--“. There should be an “m dash” rather than two hyphens.

Line 593: The description of the dentary is too simple and lack details, particularly in comparison with the detailed description of the numerous skull elements. I would like to see the dentary described in more detail. Also, rather than “narrow tooth rows” (line 596) I would say “narrow alveoli” or “narrow alveolar sulci”. Overall it would seem as if the dentary was described in haste (the period is even missing at the end of the paragraph).

Results of the phylogenetic analysis

Lines 611-613: “The unambiguous synapomorphies uniting all species of Parasaurolophus exclusive of other hadrosaurids are characters 103, 111, 128, 216, 220, 221, and 234.” To prevent the reader from having to leave this page and search what characters are 103, 111, 128, 216, 220, 221, and 234, I would prefer to see these characters spelled out here. After all, space is not a problem in PeerJ.

Discussion

It would be helpful to have an additional figure showing the stratigraphic position of all Parasaurolophus spp. specimens, that are discussed in the text.

Figures

Fig. 1. In the caption, instead of just “skulls”, I’d write “holotype skulls” to be more precise.

Fig. 6. A and B should better be placed vertically, as if looking at the skull mounted. I don’t think that by being shown sideways, the images can be displayed in substantially greater size.

Fig. 10. These elements are shown in an odd orientation. Why not display them in anatomical position?

For the sake of completeness, why not add a figure with BYU 2467? Since it is discussed alone with UCMP 143270, which it is beautifully illustrated here.
Additional comments: 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: DESCRIPTION AND REDIAGNOSIS OF THE CRESTED HADROSAURID (ORNITHOPODA) DINOSAUR PARASAUROLOPHUS CYRTOCRISTATUS ON THE BASIS OF NEW CRANIAL REMAINS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a nice paper describing interesting new material of Parasaurolophus, with interesting discussions about Parasaurolophus taxonomy and palaeogeography. I have just sfew questions/comments listed below:

Line 211: "frontonasal platform extended posterodorsally to underlie crest" This character is also present in Charonosaurus. At all, comparisons with Charonosaurus (regarded as the sister-taxon for Parasaurolophus) are extremely limited in this paper. More comparisons with this closely-related taxon would be helpful.

Line 321. Why do you estimate that the straight process of the premaxilla in P. cyrtocristatus is the autapomorphic condition?

Line 351 (7) should be (Fig. 7)?

Line 360: “The anterior half of the nasals can be observed on DMNH EPV.132300 to share a long straight articulation with the lacrimal posterolaterally”. Are you sure about it??? If so, please illustrate it accordingly.

Line 363: “sharing an extended articulation with this element and the lacrimal anterior to the platform”. Idem, not in adequation with the illustrations!

Line 370: “(Figs. PCSKULL and 7)”. What is PCSKULL?

Line 381: “Medially, the lacrimal shares a long articular surface with the nasal.”. Idem, requires illustration.

Line 400: replace “lambeosaurins” by “lambeosaurines”.

Line 420: shortening of the frontal also observed in Charonosaurus.
Experimental design: Taphonomy: Your explanation about the preservation of articulated skull roofs in Parasaurolophus is interesting, but I have another question: is the postcranial material of P. cyrtocristatus really rare, or is it just an excavation/publication/description bias (nobody likes to excavate or describe disarticulated postcranial material)?
Validity of the findings: As already mentionned above, additional illustration of the lacrimal-nasal articulation should be provided.

In general, more references towards the figures should be helpful to clarify the text.
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: DESCRIPTION AND REDIAGNOSIS OF THE CRESTED HADROSAURID (ORNITHOPODA) DINOSAUR PARASAUROLOPHUS CYRTOCRISTATUS ON THE BASIS OF NEW CRANIAL REMAINS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think that the authors adequately responded to the questions/concerns of the three reviewers, so the ms can be published as such in Peer J.
Experimental design: Idem
Validity of the findings: Idem
Additional comments: Idem


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: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clear, the english is good and professional. The literature references are sufficient and give a good background of the topic.

The figures and tables are good, raw data are given.

However: I am missing the relevance or hypothesis.
I keep wondering myself why individuality in vocalisations (in adult individuals) should not be stable over time (like here over the frame of about one year). Why should that change? What is the scientific hypothesis behind that?  In particular if you have fully grown males, (over 35 years). Individuality in vocalisations arises because of morphological and anatomical characteristics of the vocal tract. In a fully-grown, adult individual, why should this change within a time frame of one year?
This question, in my opinion, is only interesting when we consider individuality during vocal ontogenesis, while the animal develops and grows older and bigger, (including puberty). Or during hormonal changes (e.g. musth non musth), or comparing social and sexual communication (which is not done here, because vocalisations in any kind of sexual context were excluded).
Is there a study in any mammal suggesting that acoustic individuality is not a constant trait (in adults)?

The authors keep emphasising that previous studies on individuality on male elephants were only using recordings that were collected during a two week period. But without given a scientific explanation why they would expect that individuality would not be a constant trait in adult individuals.
In addition the authors keep emphasising that the study they refer to as being insufficient used captive elephants (which I would then assume to be zoo elephants.) But in fact Stoeger et al. showed individuality in males controlling for age factors, and these elephants were not zoo elephants, but elephants living in a semi-captive condition in natural environments (private game reserves)  in South Africa. (not a captive environment as one would expect in a zoo). They also used similar contexts (social contexts) as observed in this paper.  there are differences between wild elephants and the ones in the Stoeger study, but these were not captive elephants in the classic sense as one would expect after reading the current study.
Experimental design: The research question is explained but with little scientific relevance.

Otherwise, data collection seemed to be sound, they used high quality equipment suitable for recording elephants. The methods and the analysis are described in a sufficient way.
Validity of the findings: A main point of criticism here is the dataset, which as not balanced at all. There are 36 calls from individual D, 25 from individual A, while only having 6 calls from individual B and E. This is very little data for doing a long-term study on individuality. In my opinion an N of 6 is not enough data for any kind individual analysis.

Acoustic analysis: Why would you exclude acoustic parameter like fundamental frequency and formant frequencies, known to be important features for individuality in almost all vertebrate species, including elephants. Since you just recorded elephants older than 35 years old, you do not have to worry much about maturity effects (that occur in these parameter). Plus, it is possible to control for that “problem” when doing statistics.
There are multiply elephant studies reporting individuality in elephants (Soltis et al. 2005, McComb et al, Stoeger et al., and also studies investigating Asian elephants Nair et al. 2010; or de Silva et al.2009) and all showed that frequency parameter and formants are important as well.  You also did not consider any shape parameter, which are also known to be important.
So how do you want to investigate “true individual differences” while omitting those parameter that have already been shown to be individually distinctive in elephant (Soltis et la. 2005 and Soltis 2010, and the McComb studies)?
 What makes you belief that 'your' parameters are the truly important ones, so that you can neglect the ones that are typically analysed as well.
I am not saying that you are wrong, but this is not the correct approach:
Why not analysing source and filter parameter in addition to the ones you think are more important, and then you can statistically analyse which parameters are more relevant and contribute more to individual discrimination.  This would be the proper scientific approach. Not simply omitting parameter without any comprehensive reason.
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: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript needs rework and additions, and does not meet basic reporting criteria in the following ways:

The manuscript needs to be written more clearly in general, and grammar needs correction. The terminology should reflect that of the field of study (i.e. use terminology in the field of acoustics) to make it technically correct and unambiguous.

The literature references are insufficient in the areas of acoustic communication signals and musth.  Individuality in vocal signals among males of other terrestrial mammalian species should be discussed for comparison. Background should be added on what is known and not known regarding acoustic communication in elephants, including individuality in acoustic signals in females and how this is relevant in a social context (if known). Communication modalities of elephants should be presented in general. Olfactory and visual cues are mentioned, but needs to expanded on with literature citations. Furthermore, the argument that obstacles are less of a barrier for acoustic v. visual signals is more relevant in a forested environment. This goes back to providing a stronger background discussion on communication signals in general. My master’s thesis provides some basic background in acoustics that might be helpful.
Glaeser, S. S. 2009. Analysis and Classification of Sounds Produced by Asian Elephants (Elephas maximus). Master of Science, Portland State University, Portland, Oregon.

The article structure is professional. Raw data is not shared, but it is not necessary for this study.

The following needs to be added to make the findings more convincing or relevant: (1) mean values and range of the 5 acoustic parameters for each individual, (2) within-individual variability. (3) acoustic parameters that have the most discriminative power (could use methods from Stoeger et al., 2014),

DETAIL PROVIDED IN REVIEW PDF
Experimental design: This primary research is within the aim and scope of this journal.

The research questions were well defined, relevant and meaningful, and the authors do clearly state how this research fills a knowledge gap.

The investigation was performed to a high technical standard.

The acoustic parameters measured should be shown on the spectrogram for better understanding. It would be helpful to describe factors that could influence these parameters; e.g., size of the caller, distance to the source.

One design aspect that is lacking is consideration of size of the elephants. The age criteria was over 35, but there still could be size differences. In mammals, there is a relationship between body mass, vocal fold size, and the fundamental frequency. Although the authors state that fundamental frequency was not measured, the Frequency 5% parameter appears to be influenced by the fundamental frequency, and thus animal size. If this is not the case, then this parameter needs further explanation. If there is justification not to consider size, then this needs to be discussed.

Methods need clarification of factors accounted for versus not accounted for. Use consistent and technically accurate terminology to identify factors. The following terms are all used:  behavior, social context, state, elephant activities, social scenario. It appears that the factors are: behavior, social context, and reproductive state.

DETAIL PROVIDED IN REVIEW PDF
Validity of the findings: The impact will be stronger with the suggested additions and significant rewrite.

This research would be difficult to replicate without significant changes to the Methods section.

The conclusions are well-stated and linked to original research question. However, conclusions are not fully supported by results presented. Adding suggested results would address this.
Additional comments: No other general 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: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 1
Reviewer: 3

Output:
Basic reporting: a.	Well written, concise, with a thorough review of the literature.
Experimental design: a.	The research question is clear and concise and demonstrates a gap in our understanding of the individuality of wild male elephant vocalizations.
b.	The methods section was clear and the reason for excluding individuals based on the sexual state, age, region, presence of females was well explained. The sample size was ample for this study.
c.	It is curious why the authors chose only five parameters to measure for their determination of individual identification, when formants and fundamental frequency as was used in previous publications. Stoeger & Baotic 2016 used several different parameters, including the ones these authors use. McComb et al., 2003, also used formant and fundamental frequencies to determine individual identity in adult females and found significant differences. Since the paper by Stoeger & Baotic was so recent, and specifically focused on male elephants, why didn’t these authors use these additional parameters?
d.	 In addition, a more robust analysis such as a linear model that includes the additional parameters used in previous publications may have shown significant differences between all dyads compared, and thus, provide a stronger result. Because previous papers did such, and one has already been published about male elephants, it seems these authors need to use the same parameters, or at least explain why they are not needed. It seems to me that the more robust analysis is needed in order to show significance of a signature rumble for ALL individuals. The fact that the authors did not get significance between all dyads indicates that these additional parameters are needed. If not, they need to explain why not.
Validity of the findings: a.	Given the findings reported within Stoeger & Baotic, 2016, the only new finding reported here is that the study was conducted in the wild over a longer period of time. That should also be clearly stated so as not to seem deceptive.
b.	Given this previous paper, these authors need to be equally as thorough in their analysis and they use less parameters and don’t find significance between all dyads which indicates that a more robust analysis should be completed. If the additional analysis is performed and the authors still find significance and are able to scale back their analysis and still find significance using fewer parameters, that would be important for future researchers to know--i.e. only these 5 components of an analysis are needed to obtain an individual rumble signature. that would be an interesting finding in and of itself. but these authors do not discuss why they do not use methods that were previously used to obtain the same, or more robust result.
c.	In line 201 – the reference to Table 2 seems to be in error. It should be referencing table 3.
d.	The reason behind the insignificant/significant differences between individual vocalizations was not discussed.
e.	Raw data was clear and concise and inconclusive results were addressed.
Additional comments: a.	Instead of Fig. 1 depicting a spectrogram of the elephant vocalization with no labels, the authors should use supplemental figure S1 with all of the labelled measurements that were taken. It clearly shows the parameters that were measured and analyzed and would be a helpful visual for the readers, without taking up any extra space, and having to refer to supplemental information.
b. In Figure 1, the y-axis (frequency) was reported in intervals of 20 but goes from 100 to 112 to 140 – should 112 be 120? If not, why 112?
c.	In lines 170/171 the bandwidth measurement was not mentioned but was in the raw data and table 4
d.	Line 273 – “Goldenberg et.al.” changed to Goldenberg et al.
e.	Abstract says data was collected over several years but it was only 1.5 years – reword to avoid being misleading.
f.	Line 182 – “now” should be not.


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

Input:
Title: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 2
Reviewer: 1

Output:
Basic reporting: Review:

Thank you for addressing my comments: however, I have to correct you, formant frequencies do also contribute to individual distinctiveness (they are not only coding size) in many mammals, including elephants. Why? This is easily explained: the supralaryngeal vocal tract is distinctive from individual to individual. Therefore, leaving out this parameter cannot be really explained by your argument. Formant values in Stoeger et al. had the PIC (potential for individual coding) above 1, and thus contributed to the result.

Second: of course it is difficult to collect vocalizations in the wild, but if you do not have the sample size for a certain study (or investigation), than this is to be accepted. You address this now with changing statistics, still, sample size is so low for investigating individual differences. I would request the authors to tone down their arguments /discussion / results. So for example as mentioned below- don’t state that you show an individual signature, for example. This is a very strong term.

In addition I still have some concerns about the acoustic measurements, that need further explanation.

Abstract: vocal signature is a very strong term. We know that from signature whistles from dolphins, for example, were we can clearly see individual differences in the spectrograms. Could you stick to the term “individual differences”. To me, the paper does not significantly enough show a signature. (for this, more acoustic parameter should have been measured) and a true signature should be visible. Although you argue different, you did not measure all relevant acoustic parameter. Stoeger Baotic 2016 do not state that formants are not relevant for individual differences, in fact they are as well.

And there are some referencing that I belief should be adjusted:

Line 71: references: these are not the proper references that should be used. The author of the chapter about vocalizations in the Moss et al book is Joyce Poole. So you should cite her chapter instead of simple citing the entire book.

Line 89: again, please cite the chapter within the book that is addressing male societies.

Introduction: you gave some arguments of why you belief that it is important to investigate whether individuality is persistent over time in the rebuttal letter. But not so in the paper, thus the rationale for your study is still not really addressed yet. Can you please add that into the introduction, because you not only need to convince me, but ultimately also the reader of your paper.
Experimental design: Methodology: acoustic analysis. I still do not understand why you omit the common acoustic parameter. Your arguments do not convince me, and are partly wrong.
I repeat my comment from the first round:
“Why not analyzing source and filter parameter and the ones you think are more important, and then you can statistically analyze which parameters are more relevant and contribute more to individual discrimination.  This would be the proper scientific approach. Not simply omitting parameter without any comprehensive reason. “

Formant frequencies do contribute to individual coding in many mammals, including elephants. I tend to assume that maybe it was not possible due to quality reasons to measure some of these parameter? This can happen if you record in the wild, at maybe greater distance to the elephants. If this is the case, simple mention it, and tone down conclusions.
If you decide not to add those parameter, tone down your conclusions and mention that it would be important in the future to measure the other parameter as well in order to reveal an acoustic signature. (but not state that you now revealed an acoustic signature).
Validity of the findings: Ok in principle, but tone down conclusions.
Additional comments: Please tone down conclusions; due to low sample size, missing acoustic analysis.


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: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The basic reporting is significantly improved and meets all of the criteria in reviewer guidelines. The expanded coverage on acoustic communication in general and specifically on African elephant rumbles is a significant improvement. The details added on methods eliminates previous concerns. (I also appreciate that my editorial suggestions were incorporated.)
Experimental design: The experimental design meets all of the criteria in reviewer guidelines. I had only one previous concern on the acoustic parameters  measured, which has been addressed.
Validity of the findings: The validity of findings meets all of the criteria in reviewer guidelines. The detail added addressed all previous concerns.
Additional comments: Remarkable improvement. I have only a few editorial suggestions plus citations to add for hormonal correlates of musth. See attached file.


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: ACOUSTIC CUES TO INDIVIDUALITY IN WILD MALE ADULT AFRICAN SAVANNAH ELEPHANTS (LOXODONTA AFRICANA)
Review round: 2
Reviewer: 3

Output:
Basic reporting: •	The authors tell us that filter (formant) frequencies are associated with the length of the vocal tract and therefore correlated to the maturity and age of the bull elephants (Stoeger & Baotic, 2016). They also go on to say that McComb et al. 2003 mentions that the ability of formant frequencies to carry individual identity over long distances is likely to be severely reduced as was confirmed by rerecording measurements but the recordings taken of the elephants in this manuscript do not take into account long distance communication as some of the rumbles were produced in social situations and during feeding – we have no idea if they’re being produced in the context of long distance communication. Therefore, it doesn't seem to make sense to just completely remove it from the analysis and not compare the results with it and without it. Just because it was found to mostly correlate with maturity, shouldn’t it be incorporated with the wild bull population to rule it out? Because one of the big differences between this manuscript and the Stoeger paper is that it was conducted on wild elephants, shouldn’t a formant analysis be included? Wouldn’t this be a great way to show that formants are not that important for individual vocal identity?
o	The authors mentioned the difficulty of collecting data from dangerous animals but is it not possible to analyze formant frequencies from the data already collected? If Raven doesn't have this feature, Praat does. It seems that this would be an important component to include since the only distinction these authors make from Stoeger & Baotic is the fact that their data are collected on wild adult males. And yet they dont include one of the measures that the other authors do in order to make the study equally as robust.
Experimental design: •	The table reporting the significance between individuals was removed. The authors say it does not provide additional information. Yes, the PERMANOVA tests for differences between all groups at once but like they said, to provide additional information about the intricacies of the differences between dyads, it was revealed that most are significantly different but some are not. This could be interesting for future studies, especially since there could be a reason that some individuals vocalizations are more similar than others (perhaps relatedness or some other reason?). Perhaps this could be in the supplemental materials?

Results Section

Table 2: Please confirm that these numbers are correct for the 95%, 5% and Center frequencies. The 5% frequencies are very high.
Validity of the findings: Discussion Section
•	Lines 229-239: The authors discussed the possibilities of increased hormone levels of the bulls in “pre” or “post” musth, therefore making their results even more robust (because testosterone has been found to influence male vocalizations). I recommend removing this part of the discussion because they do not have any data on this and it seems unnecessary to mention.
•	Perhaps they should discuss the limitations of their data in the discussion section so it’s clear to readers that it was challenging to collect all of the parameters used in previous studies.
Additional comments: Grammar
•	Line 106, sentence starting with “This will allow for a better…” needs to be rephrased
•	Lines 173-174, the authors wrote “limit recordings to a specific behavioral or social contexts” so contexts should be singular.
•	Line 186, “used” should be “found”?
•	Line 158 – says “McComb et al., 2001” and is not cited in the reference section. Should this be 2003?
•	Line 166 & 168 – Charif and Sharif – spelled two different ways; if it is Charif, it is not in alphabetical order in the references section


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: ACPT GENE IS INACTIVATED IN MAMMALIAN LINEAGES THAT LACK ENAMEL OR TEETH
Review round: 1
Reviewer: 1

Output:
Basic reporting: Mu et al. provide a potentially interesting study on the evolutionary loss of the ACPT gene in enamel-less and edentate mammals.

Overall, I like the paper but there is much work that still needs to be done. The writing style needs work as does the English. Switching of tenses is also prevalent throughout paper - some examples are given below. Figures are fine but where did the images come from?
Experimental design: The question is well defined but more investigation is required.

What about Manis spp. (pangolins)? They are edentulous as well. There is no discussion on this group at all. Why are there no sequences from this species in this study given that two genomes have been sequenced?
Validity of the findings: I  question, whether or not there is anything known about different isoforms of ACPT. This obviously could directly impact results of this study if there is evidence of an isoform that excludes exon 4 and 5 or any other exons that have deleterious mutations. If there is nothing known than that should be stated as well.

I find the whole section "Is inactivation of ACTP neutral or adaptive" to be very speculative. Dating methods between the different studies used both in this paper and others are not the same. This might also be influencing the discussion in this section - the assumptions of the equations will strongly affect the resulting date estimates. This section is also assuming that the oldest describe fossils are indeed the oldest representative of that lineage which we know is probably not the case given the incompleteness of the fossil record.
Additional comments: Italicize Amelogenesis imperfecta throughout paper

line 48: etc. not needed
line 49-50: Awkwardly written
line 77: Not necessarily true. ACTP could play an important role in amelogenesis but simply being pseudogenized does not guarantee that

line 78: delete "To our knowledge"
line 79: delete "where instead of" replace with "and instead have"

line 111: Alignment and phylogenetic analysis of mammalian ACPT
No mention of checking for convergence among chains in Bayesian analysis. Why a 50% majority rule tree?

line 129: do you mean "related" not "unrelated"

line 151: Estimation of inactivation times
This section is not properly cited. The method Sharma et al used was published by two other studies - see the paper for details.

line 219: I'm not following this sentence

line 222: " Our study highlighted that four
223 residues (191N, 269N, 330N and 339N) of the extracellular region were for glycosylation, two 224 residues (41H and 289D) directly involved in catalysis. "
Where were the methods for this result or what paper did this come from??

line 238: replaced "showed" with "shows" - this paper

line 304: replace "Furtherly" with "Furthermore"

Italicize species names throughout

Italicize gene names throughout