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 250 PLASTOME PHYLOGENY OF THE GRASS FAMILY (POACEAE): TOPOLOGICAL SUPPORT UNDER DIFFERENT DATA PARTITIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is an important contribution and a first step to obtaining a tree-of-life of grasses using plastome data analysis. The authors have used their own data and data generated by previous authors to build an updated plastome-based phylogeny of Poaceae. The background and literature provided is sufficient, but sometimes it is not discussed appropriately. The English style, figures and tables are correct and the authors share the raw data. The paper is extremely long (101 pages manuscript, excluding tables and figures) and basically descriptive. The authors describe, too profusely and sometimes redundantly, the phylogenetic relationships among taxa within each subfamily, tribe and other taxonomic ranks in the Results and Discussion sections; these two sections could probably be re-organized and reduced to make a shorter paper keeping only essential novel information. Some parts of the paper and even subsections deal with aspects/taxa that have not been analysed in this paper and are therefore superfluous.
Experimental design: The research is primarily original as the authors have used methodological approaches (e. g., phylogenetic searches using 14 alternative data partitions and a basic test for detection of purifying/non-purifying selection within coding regions) not assayed before in grass plastomes. The methods have been described in detail and the performed analyses are overall correct. However, some procedures could be questionable. For example, 1) the alignments were not curated manually, at the risk of leaving some microstructural mutations/indels to be misaligned or deleting valuable information; it would, indeed, have a minimum effect at deep-level phylogenies, but perhaps not at shallow-level phylogenies, especially for very closely related taxa, though the authors solved partially the problem by discarding the gaps in some partition analyses; 2) the authors replaced stop codons with gaps in codon data if they were present; it could leave putative non-functional copies (e. g., pseudogenes) in the CDS data set. Despite the number of pseudogenes is low in the grass plastomes, it would be desirable to discard them from the CDS-based analysis. The authors have not commented the presence of potential pseudogenes in the data set (nor if some of them were present in one of the discarded IR); 3) the authors used a codon-based Z test to test for purifying vs positive selection in coding regions across the 250 grass plastomes using the default options in MEGA and Positive selection options in HyPhy (using MEME, mixed effects model of evolution to search for episodic selection at individual sites), and provide a Fig. 1 with number and proportion of codons under purifying/positive selection for each CDS and a Suppl. Table 1 with information on dN, dS, omega and p and test values for purifying/positive selection for each CDS; it is not clear, however, which codons of the genes show positive selection (those located in the more conserved 5’-end or those located in the more variable 3’-end of the genes?) and which values of the tests support one hypothesis over the other (in Table S1). Also, and most importantly, the authors have not tested if episodic positive selection is distributed across all grass lineages or, more likely, only across a subset of them (or even a few of them) in each case. To do it the authors should run a complementary approach to find selected branches (under positive selection) by pooling information over sites as indicated by Kosakovsky Pond et al. (2011) Mol Biol Evol 28: 3033–3043 (branch-site REL model of evolution).
The hypothesis testing is mainly based in a classification of grasses proposed by several of the current authors (Soreng et al. 2017) which, in turn, compiles molecular and morphological data from different researchers (see General comments to author).
Validity of the findings: The data is robust and statistically sound, though most of the novelty resides in the re-analysis of an enlarged data matrix using different data partitions (coding and non-coding regions, full plastome, selected genes) with and without gaps and positively selected codons, and the comparisons of the topologies and support of clades between partitions. Discussions with respect to previous phylogenetic works and classifications are exhaustively, but some of them are misleading or are not limited to supporting results (see General comments to author). The interpretation of the potential negative impact of positively selected sites should be re-evaluated with more precise data on distribution of sites across lineages, as well as that of the informative value of coding and non-coding regions with respect to the evolutionary depth of the groups under study.
Additional comments: The paper is an important contribution to the tree-of-life of grasses using plastome data analysis. It deals with an evolutionary systematic study of the grass family based on phylogenomic analysis of a large collection of plastome data (250 taxa, representing 180 genera and 44 tribes of Poaceae) generated by the authors and by previous researchers that have been jointly analysed for the first time using 14 different data partitions.  The data, methodology and results are overall sound; however, the paper presents some flaws and misinterpretations that should be corrected and results that should be properly addressed. Additionally, the paper is extremely long, and parts of the Results and Discussion sections could probably be deleted or summarized to make a more readable paper.

I acknowledge the valuable efforts made by the authors to compile and analyse a large amount of current plastome data and to use it to help to resolve the phylogeny and systematics of Poaceae. Nonetheless, I am concerned about several issues that require throughout revision:

1.The paper is extremely long (101 pages manuscript, excluding tables and figures) and basically descriptive. The authors describe, too profusely and sometimes redundantly, the phylogenetic relationships among taxa within each subfamily, tribe and other taxonomic ranks of Poaceae in the Results and Discussion sections. These two sections could probably be re-organized and reduced to make a shorter paper keeping only essential novel information. Some parts of the paper deal with aspects/taxa that have not been analysed in this paper. For example, “Rooting the grass phylogenetic tree” subsection (of Discussion) is out of place here as the authors did not root the Poaceae tree with any close outgroup (but with basal Anomochlooideae lineages). In several instances, the authors comment grass subtribes for which plastomes have not been published yet. It is superfluous, as the current work is not intended to be a full revision.
2. The hypothesis testing is mainly based in a classification of grasses proposed by several of the current authors (Soreng et al. 2017) which, in turn, compiles molecular and morphological data from different researchers. It is appropriate to use it as a baseline hypothesis and to compare the new results to it; however, the authors should give the credits to the researchers that contributed most to the phylogeny/classification of each group, trying to avoid undermining or skewed statements. For example, the authors indicate that “Danthonioideae includes a single tribe comprising 18 genera …. (Soreng et al., 2017)” and that “the plastome trees” (-based on 7 species representing 6 genera) “are better supported than trees based on a few plastid regions (Linder et al. 2010)”. However, systematic circumscription of Danthonioideae is mostly based in the work of Linder et al. (2010), who recognized 17 genera after their comprehensive molecular and morphological study of 281 danthonioid species, and the additional contribution of Teisher et al. (2017) with 1 genus. It is not surprising to know that the 7 species plastome trees of Danthonioideae are better supported than the >200 species plastid trees of Linder et al. (2010) but the two studies and their respective sampling sizes are not comparable.
3. The authors used a codon-based Z test to test for purifying vs positive selection in coding regions across the 250 grass plastomes using the default options in MEGA and Positive selection options in HyPhy (using MEME, mixed effects model of evolution to search for episodic selection at individual sites), and provide a Fig. 1 with number and proportion of codons under purifying/positive selection for each CDS and a Suppl. Table 1 with information on dN, dS, omega and p and test values for purifying/positive selection for each CDS. It is an interesting approach though it is not clear, however, which codons of the genes show positive selection (those located in the more conserved 5’-end or those located in the more variable 3’-end of the genes?) and which values of the tests support one hypothesis over the other (in Table S1). Also, and most importantly, the authors have not tested if episodic positive selection is distributed across all grass lineages or, more likely, only across a subset of them in each case. It would be advisable to conduct a complementary approach in order to find selected branches (under positive selection) by pooling information over sites as indicated by Kosakovsky Pond et al. (2011) Mol Biol Evol 28: 3033–3043 (branch-site REL model of evolution). It is highly relevant because some of the conclusions drawn by the authors about the potential effect that genes containing positively selected codons can have on phylogenetic disturbance (or “systematic error”) should be carefully checked.
4. The authors have built a grass phylogeny showing different evolutionary depths (from subfamily (deep phylogeny) to species/variety (shallow phylogeny) levels and have compared the levels of resolution and support of each of the 14 data partitions across the main clades. However, it would be worth to know which data partition (or even subpartition) is most adequate for solid reconstruction of the deep and shallow branches of the tree clades. Additionally, they indicate that widely used loci in grass systematics, such as ndhF, matK, rpoC2 and rbcL, particularly prone to positive selection in some codons, could cause phylogenetic artifacts. I am not convinced about this conclusion. These genes (or parts of them) are more variable than other plastid genes, and therefore more useful to resolve deep vs shallow phylogenies, as demonstrated in early studies of plastid phylogenies of angiosperms. All of them encode functional proteins, and episodic positive selection in some codons may occur only in some lineages. At least two of them (rbcL, matK) have been selected as barcoding molecules for plants (ToL project). The authors should make more solid arguments about the phylogenetic value/failure of these genes before recommending caution about them. Moreover, the suggestion of using the highly conserved psaA and psaB genes for phylogenetic reconstruction is not very useful for shallow phylogenies of grasses; they may content very few positively selected codons but do not contain enough phylogenetic signal for recently evolved lineages.
5. The core Pooideae clade should not include Brachypodieae. Several evidences support it. The sister but non-inclusive relationship of Brachypodium to the core pooid clade [Triticodae (Triticeae+Bromeae)/Poodae (former Poeae+Aveneae; now Poeae s. l.)], originally proposed by Davis and Soreng (1993), was abandoned in favor of the inclusion of Brachypodium within the ‘core pooids’, a non-taxonomic but independently evolved natural group, in some recent analyses (Davis & Soreng, 2007; Saarela et al., 2015; Soreng et al., 2015, 2017). However, recent studies (Minaya et al. 2015; pooids, b-amylase; Sancho et al., 2017, New Phytol. (accepted paper, phylogenomics of Brachypodium and grass plastomes) support the sister relationship proposed by Davis and Soreng as well as divergence times intermediate between those of the basal ancestral pooids and the recently evolved core pooids (Sancho et al. 2017). Additionally, pairwise plastome genetic and patristic distances have further confirmed that Brachypodium is closer to some basal pooid lineages than to the core pooid lineages (Sancho et al., 2017), corroborating similar results based on nuclear single copy genes (Minaya et al., 2015) and functional genomic studies of regulation of vernalization and flowering time genes (Fjellheim et al. 2014; Front. Plant Sci. 5: 431;
Woods et al. 2016, Plant Physiol. 170:2124-2135). Brachypodium is a highly isolated lineage, and the large length of its stem branch (compared to the short lengths of its crown branches) has been recovered in all phylogenetic studies conducted with representative species of this genus and other Pooideae lineages (see, for example, Minaya et al. 2015; Catalan et al. 2016 (not 2015); Sancho et al. 2017).  It would be advisable to recognize that Brachypodieae is not part of the core Pooideae from the very beginning; the authors could explain better their current results based on this hypothesis.
6. The authors have misinterpreted the results of Christin et al. (2007, 2008) about convergent evolution of C4 photosynthetic pathway genes. The sentence (ls. 758-760) “For example, in grasses in which photosynthetic genes, such as rbcL or PEPC, converge under selection for C4 photosynthesis, misleading phylogenies can result (Christin et al., 2007, 2008)" is incorrect. Convergent evolution caused by selection resulting in (false) monophyly of C4 grasses was found in analysis of some coding positions of the PEPC gene (Christin et al. 2007), whereas polyphyletic origin of C4 grass lineages was recovered in analyses of non-coding positions of the same PEPC gene (Christin et al. 2007) as well as in plastid rbcL and ndhF genes (Christin et al. 2008). Christin et al. never indicated that the plastid rbcL gene was under convergent selection; by contrast, they used this gene and the plastid ndhF gene to construct a reliable phylogeny to estimate the divergence times of the polyphyletic C4 grass lineages.

Additional points:

7. The alignments were not curated manually, at the risk of leaving some microstructural mutations/indels to be misaligned or deleting valuable information; it would, indeed, have a minimum effect at deep-level phylogenies, but perhaps not at shallow-level phylogenies, especially for very closely related taxa, though the authors solved partially the problem by discarding the gaps in some partition analyses.
8. The authors replaced stop codons with gaps in codon data if they were present; it could leave putative non-functional copies (e. g., pseudogenes) in the CDS data set. Despite the number of pseudogenes is low in the grass plastomes, it would be desirable to discard them from the CDS-based analysis. The authors have not commented the presence of potential pseudogenes in the data set (nor if some of them were present in one of the discarded IR).
9. Despite their critics about genes showing positively selected codons the authors chose as their reference tree, tree X, based on plastome data including positively selected codons.
10. l. 250. ‘Unsupported’ should not be used for clade support < 50%, you could use very low or very weak support instead.
11. ls. 304-306. What is the sentence for?
12. l. 663. Please give details on number of clades and percentages.
13. ls. 667-668. Please identify the 30 clades. Do they correspond to shallow clades?
14. ls. 674-675. The argument is not convincing; character conflict does not necessarily to be connected with selection effect. The authors should test this hypothesis.
15. l. 821, 836-841. Bambusoideae. Most of the Discussion on bamboos is based on previous plastid-based phylogenetic studies, despite the fact that many bamboos are polyploids. What is the conclusion here? Can the authors identify hybrid/allopolyploid clades or introgression events that could explain the conflicting topologies obtained from plastomes and from nuclear data?
16. ls. 964-966. Confusing sentence, the authors have not described properly the relationships among the 5 Phyllostachys species.
17. ls. 1003-1008. Unnecessary paragraph. The current study could not resolve it as Neohouzeaua has not been included in the study.
18. ls. 1053-1054. The pivotal paper that proposed Brachypodium distachyon as model system for grasses was that of IBI (International Brachypodium Initiative) or Vogel et al. 2010. Nature 463: 763-768.
19. 1066-1069. A sister relationship of Diarrhena and Brachypodium was recovered in the beta-amylase tree of Minaya et al. (2015) though some sequences (Diarrhena, B. distachyon clone 2-3) could be recombinant. The authors cite this reference in the manuscript but do not comment these results.
20. ls. 1085-1098. See comments above about phylogenetic studies of Brachypodium (Minaya et al. 2015; Catalan et al. 2016 (book chapter), and the accepted work by Sancho et al. 2017, that could be discussed by the authors.
21. ls. 1102-1109. I recommend the authors to read the recent work by Sancho R, Cantalapiedra CP, López-Álvarez D, Gordon SP, Vogel JP, Catalan P, Contreras-Moreira B. 2017. Comparative plastome genomics and phylogenomics of Brachypodium: flowering time signatures, introgression and recombination in recently diverged ecotypes. New Phytologist (in press) for a robust dating analysis of the Brachypodium lineages within the grass phylogeny framework based on plastome analysis and nesting dated approaches. The paper will be published as early view soon.
22. ls. 1197-1198 and more. Please indicate if the work by Saarela et al. (in review) is already published.
23. ls. 1205-1207. Pimentel et al. (2017) found a sister relationship of Lagurus to Aveninae-Koeleriinae in their 5-genes plastid tree. The authors should comment it. This paper [Pimentel M, Escudero M, Sahuquillo E, Minaya MA, Catalán P. 2017. Diversification rates and chromosome evolution in the temperate grasses (Pooideae) are associated with major environmental changes in the Oligocene-Miocene. PeerJ] has been accepted for publication and will be published soon.
24. ls. 1236-1243. Ammophila has not been included in this study. These sentences are unnecesary here.
25. 1245-1247. Pimentel et al. (2017) in their 5-genes plastid phylogeny do not recover a sister relationship of Anthoxanthiinae to Agrostidinae+Brizinae but that of Anthoxanthinae to Aveninae-Koeleriinae-Lagurus. These authors have a larger sampling of Agrostidinae, and Aveninae-Koeleriinae than the one presented here. The authors should discuss it and be cautious about their conclusion.
26. ls. 1275-1278. Minaya et al. (2015) included Avenula bromoides (Gouan) H. Scholz in their study (not A. hookeri). It is not surprising to know that the plastome tree does not agree with the ITS (nuclear)+plastid tree of Minaya et al. (2015) for these particular taxa, considering the high reticulation of the groups involved.
27. 1278-1279. The authors do not explain the conflicts of their plastome tree with those of the b-amylase tree of Minaya et al. (2015). They should comment them. Again, it would not be surprising to find differences between the nuclear beta-amylase tree and a plastome tree in highly reticulate groups. The authors do not extract conclusions about the observed differences. Moreover, Minaya et al. (2015) detected incongruent resolutions for some beta-amylase sequences, caused by recombination or selection, and more specifically they explained the cases of Avenula bromoides, Desmazeria rigida, Deschampsia antarctica, Alopecuros arundinaceus, Colpodium drakensbergense, Ammophila arenaria, Vulpia alopecuros, and Festuca ovina. It looks as if the authors have not paid attention to the paper by Minaya et al. (2015), in which they throughly investigated the potential origins of phylogenetic incongruence in cloned copies of the single copy gene beta-amylase.
28. 1279-1282. The sentence is superfluous; it is not currently supported by the data.
29. ls. 1288-1289. This relationship is only supported by 8-9 trees and, as stated by the authors, they haven't sampled other representatives of Airinae (apart from H. hookeri), Holcineae (apart from H. lanatus) and Deschampsia s. s. (apart from D. antarctica). In the 5-genes plastid phylogeny of Pimentel et al. (2017) those relationships are not well supported.
30. ls. 1299-1305. The 5-genes plastid phylogeny of Pimentel et al. (2017) (including matK) does not recover a strong support for the Cynosurinae+Dactylidinae+Parapholiinae+Loliinae clade. A tree based solely in matK might not be an improvement to the resolution of the phylogeny of the group.
31. ls. 1306-1307. 98% in tree X (Fig. 4) for the branch showing the sister relationship of Dactylidinae/Cynorusinae+Parapholiinae to Loliinae. Taxon sampling has increased in Dactylidinae, Cynosurinae and Parapholiinae but not much in other close groups (Airinae, Holcinae, Deschampsia s.s.).
32. ls. 1318-1319. Incomplete sentence.
33. ls. 1467-1469. The authors recognize that their plastome gapped regions could be ambiguously aligned. It could be avoided in part through manual alignment curation.
34. ls. 1478-1479. “lack of support”. Replace with very low support.
35. l. 1511. The authors recognize here the potential influence of nuclear genes in combined nuclear+plastid topologies and their contrasting resolution with respect to plastid or plastome topologies alone, but they haven't done it with respect to Minaya et al. (2017) analyses (see comments above).
36. ls. 1634-1638. Please compare levels of support with sampling sizes.
37. ls. 1653-1656. Confusing sentence. It is not clear which studies show stronger support than others and which studies were considerably less sampled than others.
38. ls. 1656-1661. Please indicate if the Washburn et al. (2015) tree is their only-plastid tree, -which would be congruent with the plastome tree-, and if conflict with the Vicentini et al. (2008) tree is because the latter is a nuclear-based tree (as indicated by Washburn et al. 2015).
39. ls. 1683-1687. Please indicate the ploidy level of W. capillipes. Bidirectional crosses are common in grass allopolyploids (e. g. Brachypodium hybridum, Lopez-Alvarez et al. 2012, 2017; Catalan et al. 2016) and allopolyploidy and bidirectional origin could explain the coexistence of two plastid types within the same taxon (see discussions in Catalan et al. 2016 (Phylogeny and evolution of the genus Brachypodium, book chapter); Lopez-Alvarez et al. 2017, Annals of Botany 119: 545-561.).
40. ls. 1694-1698. The authors should discuss their results regarding Setaria and Paspalidium with respecto to the broadly sampled study of both genera and close allies conducted by Kellogg et al. (2009) using plastid ndhF data. Please specify the two plastome trees that support the monophyly of Setaria.
41. ls. 1816-1817. Speculative assessment. Denser plastome sampling could also reduce the resolution or the support of some evolutionary relationships.
42. ls. 1836-1839. The analysis of perennial Brachypodium spp plastomes is currently underway (Sancho et al. unpub. data). Nonetheless, resolution of Brachypodieae with respect to Diarrheneae and the core Pooideae (Poeae+Bromeae+Triticeae) do not depend on it. Brachypodium is a strongly supported monophyletic lineage in all evolutionary analyses.
43. ls. 2023-2025. The correct reference is as follows: Catalán P, López-Alvarez D, Díaz-Pérez A, Sancho R, López-Herranz ML. 2016. Phylogeny and evolution of the genus Brachypodium. In Vogel J (ed.). Genetics and genomics of Brachypodium. pp. 9-38. Series Plant Genetics and Genomics: Crops Models. Springer. New York.


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 250 PLASTOME PHYLOGENY OF THE GRASS FAMILY (POACEAE): TOPOLOGICAL SUPPORT UNDER DIFFERENT DATA PARTITIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made a substantial and conscientious effort to address the concerns of the previous reviewers.  This version of the manuscript is much improved and appreciably more readable.

The following comments all note trivial editorial changes:

Line 147 – the cited reference here is incorrect.  We used seed from that same accession (not really equivalent to the same individual) in Estep et al. 2014, which I think is cited elsewhere.

Lines 202, 287 – "predominate" (verb) should be "predominant" (adjective)

Line 327 – I'm having trouble understanding the syntax here.  Is a word missing, or an extraneous phrase included?

Lines 319-363 – This section is a narrative report of the data in Table 3 and is very hard to read.  I appreciate the efforts to provide a summary, but it still feels long.  How about starting the paragraph at line 319 as "Excluding positively selected codons had relatively little effect on support values overall, with average support differences ranging from 1 to 4%.  The largest effect of positively selected sites is in comparison B vs. D.  This is not surprising since these are three-gene data sets, with all genes known to have positively selected sites."
	The next paragraph could be:  "Exclusion of gapped sites also had relatively little effect on average support values.  … (two sentences similar to above).

Line 573 – "Panicininae" should be "Panicinae"

Lines 649-651 – There's an arithmetic problem here:  23 clades in the three gene trees differ from those in the plastome coding trees; 13 are only weakly supported, but the remaining 9 are moderately supported.  9 + 13 = 22, so one is missing.

Lines 789-791 – Is the rate of evolution in Olyreae accelerated or is it retarded in the woody bamboos?  Unless there's been a formal test that Olyreae have been speeding up relative to some background rate, it might be better just to state that Olyreae plastomes mutate faster than those in the woody bamboos, and leave open the question of whether it's a speed up in one or a slow down in the other.

Line 864 – move parentheses in Attigala et al. (2016)

Section on Poeae, lines 1056 and following – in a number of places in this section, species are listed as "newly sampled here".  I'm not sure what this means, since I think a number of these taxa are in other studies, just not with complete plastomes.  Also, these "newly sampled" statements appear to be mostly in the Pooideae rather than elsewhere in the manuscript.  I'd suggest either deleting them or making clear why they are particularly important.

Line 1080 – delete "or not"

Line 1248 – I think chloroplast capture is a form of introgression, so these two terms are redundant.

Line 1361 – add a period after "sampled"

Line 1478 – There is a fourth explanation, which is a labeling mix-up or contamination somewhere in the extraction or sequencing process.  The solution (which I’m not recommending for the current paper!) would be to re-extract and sequence both specimens.

Line 1507 – "unisetis" should be "unisetus"

Line 1554-1555 – There is a problem with the sentence beginning "Twenty one five subtribes …."  Probably a typographical error somewhere.

Line 1607 -  I think I know what you mean by "all plastid and plastome trees", but plastid = plastome.  Presumably this is intended to compare few-gene vs. complete plastome trees?

Lines 1664-1665 – I'd be cautious about any biological inferences about Whiteochloa until the possibility of technical error can be ruled out.
Experimental design: Meets all journal standards.  The analyses are careful and detailed.
Validity of the findings: Meets all journal standards.  The conclusions are well supported.
Additional comments: This is a very useful contribution to the literature and I'm looking forward to seeing it in print.


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 250 PLASTOME PHYLOGENY OF THE GRASS FAMILY (POACEAE): TOPOLOGICAL SUPPORT UNDER DIFFERENT DATA PARTITIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: see General comments
Experimental design: see General comments
Validity of the findings: see General comments
Additional comments: This is a resubmission of a manuscript I reviewed before. The authors have satisfactorily addressed most of the issues raised in my first review and have considerably shortened the length of the paper, making it a more readable work.

I have few additional issues about the new version that should be considered as they could help to improving/clarifying the current knowledge on the evolutionary history of some particular grass lineages.

Introduction:

Ls. 78-86: “Recent grass plastome sequences have been variously published …”: Please cite the recent publication by Sancho et al. 2017 (Comparative plastome genomics and phylogenomics of Brachypodium: flowering time signatures, introgression and recombination in recently diverged ecotypes. New Phytologist, early view, doi: 10.1111/nph.14926). This work includes a family-wide plastome-based phylogenomic dating analysis of the main lineages of grasses.

Discussion

BOP clade:

Ls. 766-768: “However, in a recent plastid study Oryzoideae and Pooideae were recovered as sister taxa, although with uneven sampling throughout the family (Pimentel et al., 2017)”: This sentence seems to be out of place here and could be deleted. The study of Pimentel et al (2017) was exclusively focused on Pooideae; sampling outside the subfamily was very scarce and the few non-pooid representatives incorporated into the analyses were used as outgroups.

Pooideae:

Ls. 972-980: “Tribes Brachypodieae, Diarrheneae, Bromeae, Poeae and Triticeae form a maximally supported clade …”: Please cite here the recent plastome-based study of grasses conducted by Sancho et al. (2017). It would be worth mentioning here that these authors found intermediate consecutively diverging positions of Diarrheneae and Brachypodieae between the basal pooid lineages and the recently evolved lineages of the 'core pooids' clade and that their study supports the evolutionary circumscription of the ‘core pooid’ clade to the recently evolved Triticeae+Bromeae/Poeae lineage, as initially suggested by David & Soreng (1993). It could be also mentioned that Sancho et al. (2017) demonstrated through raw pariwise genetic distances and patristic genetic distances (on their ML tree) that Brachypodieae are not closely related to core pooids (Triticeae, Bromeae and Poeae), in fact they are as close to Triticeae-Bromeae as to the basal pooid lineages and even less close to Poeae than to the studied basal pooids.

Ls. 1009-1011: “Evidence does not support an older age for the Brachypodium crown clade than for the Poeae + Triticeae crown clade (Catalán et al.,2012)”: Please mention the recent plastome-based nested dating analysis of the grass family and Brachypodium presented by Sancho et al. (2017). The authors estimated the age of the Brachypodium crown node at 10.1 Ma.

Ls. 1011_1013: “Plastomes of the other species of Brachypodium (Catalán et al., 2012, 2016a, 2016b), once sampled, might break up the long branch and help clarify relationships among Brachypodieae, Diarrheneae and Bromeae–Poeae–Triticeae”: This statement is incorrect. Plastomes of other species of Brachypodium (e. g. the early diverging B. stacei) do not affect the evolutionary position of Brachypodium within the plastome grass tree (cf. Sancho et al. 2017). Relationships of all these tribal taxa have been clearly shown in this study.

Poeae

Ls. 1057-1059: Please cite the plastome-based study of Sancho et al. (2017).

Ls 1070-1071: “In a recent five region plastid study, however, Anthoxanthinae is strongly supported as sister to Aveninae (Pimentel et al., 2017)”: This statement is incorrect. In the study of Pimentel et al (2017) the Anthoxanthinae lineage is sister to a ((Aveninae/Koeleriinae), Lagurus) clade. A similar relationship was also found by Quintanar et al. (2007).

Future directions

Ls 1649-1651: “(4) sample perennial species of Brachypodium (Brachypodieae), which may help resolve problematic relationships among Brachypodieae, Diarrheneae and Poeae + Bromeae + Triticeae in subfamily Pooideae”: This statement is out of place here. Sancho et al. (2017) have clarified the evolutionary relationships of Brachypodieae and the other tribes in their plastome-based study sampling the three annual species of Brachypodium and dating the grass plastome tree. Inclusion of perennial species of Brachypodium will not change the relationships (most Brachypodium perennial species are of more recent origin than the annuals, e. g. those of the core perennial clade (see plastid and nuclear trees in Catalan et al. 2016), and only one short-rhizomatous perennial (B. mexicanum) is approximately as old as the annuals or of intermediate age between the annuals and the core perennial clade (B. retusum) (cf. Catalan et al. 2012, 2016). New plastome data from perennial Brachypodium taxa corroborate these findings (Sancho et al. unp. data).


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: REDESCRIPTION OF CALYPTOSUCHUS (STAGONOLEPIS) WELLESI (ARCHOSAURIA: PSEUDOSUCHIA: AETOSAURIA) FROM THE LATE TRIASSIC OF THE SOUTHWESTERN UNITED STATES WITH A DISCUSSION OF GENERA IN VERTEBRATE PALEONTOLOGY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: This manuscript offers a useful compilation and description of material referred to
Calyptosuchus wellesi, based primarily on the holotype and referred material from the UCMP collections.  The chief deficiency of the analysis is the lack of a clear phylogenetic context. Aetosaur material is notoriously difficult to analyze phylogenetically because so much of the material is fragmentary, and the durable scutes are often the only elements present. Also, there is no clear picture of how individual variation and ontogeny might affect some of the characters used for aetosaur taxonomy, particularly of the vertebrae and scutes. Still, it is important to advance a clear argument as to the systematic arguments put forth. Since the manuscript reverses the recent classification of wellesi as belonging to the genus Stagonolepis, a differential diagnosis should be provided demonstrating the preferred generic assignment of the species based on a differential diagnosis.
Validity of the findings: As described, the specific assignment of C. wellesi is not based on any autapomorphies, but could be supported by a unique combination of synapomorphies present in other taxa. Again, this should be done in the context of a phylogenetic analysis.
Additional comments: One important aspect of this paper is the analysis of the locations of the disarticulated elements that make up Camp’s collection of aetosaur material from the Placerias quarry. These data do offer compelling evidence for the differentiation of material of Desmatosuchus spurensis and C. wellesi from the quarry.

In summary, this is a useful description of important aetosaur material from the Triassic of the southwest. However, in its current form, the paper does not provide a compelling systematic argument for the stated systematic assignments, as opposed to differing arguments made in recent papers. I would suggest that a revised analysis of this type would be a necessary prerequisite for publication. There are abundant recent papers covering phylogeny of aetosaurs, most notably Desojo et al 2013 (for which Parker is a co-author), from which the phylogenetic context for the systematic arguments could be derived.

Editorial Comments regarding citations:

Lines 62, 146 Parker 2005a should be Parker 2005

Lines 95, 98, 100, 102. Should be consistent in citing Fiorillo et al (2000) vs listing all three authors.

Line 106. Irmis et al 2011 not in references.

Lines 183, 184 should be Gregory 1953 not 1953a.

I could not find citations for Ludekker 1887, Heckert and Lucas, 2002, and Heckert et al 2005


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: REDESCRIPTION OF CALYPTOSUCHUS (STAGONOLEPIS) WELLESI (ARCHOSAURIA: PSEUDOSUCHIA: AETOSAURIA) FROM THE LATE TRIASSIC OF THE SOUTHWESTERN UNITED STATES WITH A DISCUSSION OF GENERA IN VERTEBRATE PALEONTOLOGY
Review round: 1
Reviewer: 2

Output:
Basic reporting: It is not sufficient to give a map of the bonebed only (Fig. 1).

Fig. 1 may be improved by adding a geological map of the study area showing the fossil locality and a litholog showing stratigraphic position of the fossil-bearing horizon.
Experimental design: Although it is difficult to separate out materials of Calyptosuchus from other aetosaurian remains, the author has done a commendable job of bringing out the morphological distinctiveness of Calyptosuchus remains.

However, a comprehensive phylogenetic analysis to ascertain the position of Calyptosuchus with respect to other aetosaurs would have much improved the manuscript and strengthened the assertion that ‘Calyptosuchus may be distinguished from other aetosaurs based on unique combination of characters’.
Validity of the findings: No comment.
Additional comments: The manuscript redescribes a medium sized desmatosuchian aetosaur Calyptosuchus wellesi collected from a multitaxic fossil locality, which have yielded other aetosaurian remains. The manuscript is well written, thorough, imparts new information regarding the postcrania of Calyptosuchus, and should be published.

Manuscript may be shortened considerably. It may be reduced by removing sections that are imparting no new information. For example, the paragraphs on astragalus and calcaneum may be reduced to one/two sentences as there are no new morphological information.


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: ANTS OF THE MONOMORIUM MONOMORIUM SPECIES-GROUP (HYMENOPTERA: FORMICIDAE) IN THE ARABIAN PENINSULA WITH DESCRIPTION OF A NEW SPECIES FROM SOUTHWESTERN SAUDI ARABIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS is professionally written with just occasional lapses that I have marked with sticky notes. Spelling errors are absent as are most typographical errors. However, the authors should recheck their work for small glitches that are additional to those I have noted. The introduction is adequate, but I suggest that part of the ‘Discussion’ at the end of the article should properly be inserted in the Introduction. The literature is well-referenced and relevant.
In terms of structure, the MS follows conventional formatting as is required in taxonomic articles, with Materials and methods and Measurements and Indices appropriate to the subject matter.
The figures mostly consist of good quality photographs, but I have indicated my preference for white maps and simple line drawings over annotated photographs. For some reason, most of the figures have duplicate captions, and unless this is required by the journal, one of these should be deleted in each instance. Figure 5 and Table 1 appear to me to be duplications of content shown elsewhere and, in my opinion are unnecessary and should be deleted.
The raw data appears to be provided consistent with normal scientific ethics and standards, but it appears that the authors need to include a blurb that covers the erection of new species that are recorded in an online journal. I have noted this fact with a sticky note and this should be checked by the senior author.
Experimental design: The original research is within the scope of the journal. The content is not particularly novel or eye-catching, but the monographing of a small species group within the Myrmicinae is a valuable contribution for this part of the world; especially since the previous literature consists mainly of isolated records and descriptions.
 The investigation has obviously been performed conscientiously, with proper investigation into the availability of type material for comparative purposes and painstaking listing of other, non-type material. In one case the sheer volume of the material examined suggests the record should be presented as a summary rather than in full. I have some qualifications about the diagnosis of the species-group, and indicated how the authors can clarify how they approach this. Other, smaller, qualifications over the taxonomic listing and the taxonomic key to worker ants in the group are also noted with sticky notes. One point I note is that the source of the acronyms used for repositories of material is not the most current and I suggest that the authors use a more modern source (one is suggested).
Validity of the findings: The findings of the authors appear sound, although I raise a query whether one of the species discussed, here described as new, actually belongs to the target group. However, this is a query only based on its odd appearance and not an objection.
 The content of this paper does not include statistics or other quantifiable data, and those figures that do appear, i.e., measurements and indices, are soundly based and conform to established norms.
This type of work does not normally carry concluding remarks. In fact, the authors do provide a summary Discussion and conclusion, but the contents of these segments could be better placed elsewhere (see my comments under ‘Basic Reporting’).
  Apart from a short Introduction and the final discussion and conclusions, the authors provide little in the way of expanded discourse and this is primarily limited to factual observations, so speculation is virtually absent. Some of the species look as though they may be introductions to the region, but the authors do not discuss that possibility.
Additional comments: This paper does not cover new ground or introduce novel techniques but, in general, it is a solid standard taxonomic monograph and suitable for publication in your journal. As mentioned, I have indicated reservations at some points, and trust the authors may consider the specific suggestions I raise before publication. However, these are relatively few.

I have annotated the .pdf with the comments mentioned above, and also where I have noted the usual blemishes and glitches in a paper of this size.


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: ANTS OF THE MONOMORIUM MONOMORIUM SPECIES-GROUP (HYMENOPTERA: FORMICIDAE) IN THE ARABIAN PENINSULA WITH DESCRIPTION OF A NEW SPECIES FROM SOUTHWESTERN SAUDI ARABIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In some parts of the text, some minor problems related to English were detected. See inside the text.

The references used support the structure and development of the research. The background is sufficient to understand the research problem addressed. Despite this, there are problems with some cited literature that are not included in the references section.

The species treated here are relatively well supported under the morphological plane, although in some cases, there are no arguments to support the hypotheses of synonymy. The latter must be reconsidered so that the nomenclatural amendments acquire stability and allow improving the quality of taxonomic information.
Experimental design: This taxonomic revision covers a regional geographic range; however, the information contributes to the formulation of research in systematics and biogeography.

Here, the authors use standard methodologies in the taxonomic treatment of ants, which allows that comparisons between the treated species, allow the evaluation and revalidation of taxonomic hypotheses already proposed.
Validity of the findings: This cannot be considered an underlying conclusion of the work. The authors must present one or several conclusive ideas related to the current diversity of the group's fauna in KAS.
I suggest that the paragraph not be abandoned and then be used to finalize this section.
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: ANTS OF THE MONOMORIUM MONOMORIUM SPECIES-GROUP (HYMENOPTERA: FORMICIDAE) IN THE ARABIAN PENINSULA WITH DESCRIPTION OF A NEW SPECIES FROM SOUTHWESTERN SAUDI ARABIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a response to the amended MS; hence, I am incorporating all my latest comments under one head.

I have examined all the documents, including the revised MS, the original MS with tracked changes and my own comments and those of the other referee. I regret that, in my opinion, substantial changes are still required, and I have come across further glitches that neither I nor my colleague picked up on originally. However, the major issues remain those that were identified but have not been addressed satisfactorily.

The issues raised by the anonymous referee do seem to have been addressed, but not some of my own. These are highlighted with yellow, sticky edits in the present submission. I strongly urge the authors to check on all edits as this does not seem to have been done originally (mainly the figures and figure captions) - at any rate the latter are not mentioned in the letter of rebuttal.

Firstly, I notice the keywords have been omitted, but presume this is due to the requirements of PeerJ. There are a few minor edits in this section of the MS, but I have suggested a clarification of the Diagnosis subheading. The authors seem to have misunderstood my comment on M. exiguum in the Synoptic list, so I have expanded my original statement so as to clarify it. However, the main issue is the taxonomic key, and this part needs to be completely revised: I have suggested how this may be done. Furthermore, Monomorium holothir has 12-segmented antennae, not 11-segmented antennae as mentioned in the key (but correctly mentioned under the description of this species). There are a couple of additional corrections indicated by stickies, but the other main area that should be addressed is figure and figure captions. Figure 5 reproduces the exact same data as Figs 6-11, and should be deleted. I have also suggested Figures 3 and 4 would look better as line drawing and map, respectively, but I leave this to the discretion of the authors. However the map legends and data points need to stand out more.

Brian Heterick
Experimental design: See above.
Validity of the findings: See above.
Additional comments: None.


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: ANTS OF THE MONOMORIUM MONOMORIUM SPECIES-GROUP (HYMENOPTERA: FORMICIDAE) IN THE ARABIAN PENINSULA WITH DESCRIPTION OF A NEW SPECIES FROM SOUTHWESTERN SAUDI ARABIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The suggestions were taken and argued by the authors. The theoretical aspects and results are enough to understand the importance of this taxonomic work.
Experimental design: The authors followed the recommendations and took into account the taxonomic suggestions, making the data and information comparatively useful.
Validity of the findings: The results are substantially important for the understanding of ant biodiversity in relatively studied areas, such as the Arabian Peninsula.
Minor changes that would help in the structure of this section of the manuscript are inserted
Additional comments: Consider the following:
Line 144: Please, you must include information on the distribution of the species or remove "and distribution" since you are only providing the taxonomic synopsis of the species addressed in this study.

You are using two ways to reference the Antweb images. Make the same format for all images taken from www.AntWeb.org.


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 QUASI-RANDOMISED, CONTROLLED, FEASIBILITY TRIAL OF GLITTER (GREEN LIGHT IMAGING INTERPRETATION TO ENHANCE RECOVERY)—A PSYCHOEDUCATIONAL INTERVENTION FOR ADULTS WITH LOW BACK PAIN ATTENDING SECONDARY CARE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing of the manuscript is clear and well written. You have used appropriate references to set the scene for the study and also to support your findings. The article is well structured and the tables are very descriptive. Although I wonder if there is perhaps a too much detail included in Table 1? I think the "Who provided" part can be summarised and included in the methods section rather than in Table 1.
The results clearly address the aims of the study and you have considered reasons for the challenges encountered.
Experimental design: The research is original, important and the question itself is well defined. Reassurance of a favourable outcome is unfortunately not commonly provided to people with LBP, so I commend the authors for developing a strategy to help address this healthcare issue. I think there are some areas of the methods section which are thin and can be improved. Detailed comments in general comments for the authors section. I think the adaptive design was a great idea.
Validity of the findings: I think the findings are encouraging and will certainly help to inform a future RCT in the area. The conclusions are well supported by the results, and link back to the original aims.
Additional comments: This is a well designed feasibility study exploring the acceptability of the GLITtER intervention for people with low back pain attending an outpatient clinic. It’s a shame recruitment rate was slower than you had hoped however I hope that the planned adjustments will be useful for the future RCT. I have a few suggestions for the authors to consider.
1.	I think the paper could be improved by clearly specifying in the methods section what was considered acceptable or not acceptable for each domain being evaluated. For example in the discussion section you mention “We achieved a 3-month participant follow-up rate of only 42%, which failed to meet our feasibility criterion.” However what was acceptable for this criterion? I would suggest that some more description is needed regarding how each criterion was judged as being “met” or requiring “review”.
2.	I think there could be some more description in the methods section on the actual intervention - GLITter, what is meant by “standard care”, and how the proposed intervention differs to standard care in the context of this study. I suggest that the key information from Table 1 be summarised and included in the main text also.
3.	With regards to the outcomes – what is the rationale behind choosing the outcomes? I suggest including just s brief sentence highlighting the importance of  the outcomes selected – this will be particularly useful for readers with a non-physiotherapy or medical background.
4.	You specify that the target population is patients with low back pain however could you please clarify whether this includes both acute and chronic LBP? Evaluation of patients may differ depending on duration of pain and number and nature of prior healthcare visits – was this sort of information considered in the feasibility study?
5.	I like the name of the intervention – GLITtER. Some times however I felt like I needed to be reminded what it stood for – perhaps in sections like the first paragraph of the discussion, the actual name of the intervention could be used to reinforce what it was all about.
I have a few more minor comments:
Results: Where it says an average of 2.1 participants on page 9 line 281 – I recommend just saying 2 participants.
Discussion: Please review the sentence on page 11 line 331.


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 QUASI-RANDOMISED, CONTROLLED, FEASIBILITY TRIAL OF GLITTER (GREEN LIGHT IMAGING INTERPRETATION TO ENHANCE RECOVERY)—A PSYCHOEDUCATIONAL INTERVENTION FOR ADULTS WITH LOW BACK PAIN ATTENDING SECONDARY CARE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language OK
Literature/references OK
Article structure/ tables / figures OK
Relevant results: Discussion and conclusions should be improved, please see below
Experimental design: Relevant for the aims and scope of the journal OK
Research questions well defined OK
Rigorous investigation and technical standards OK
Methods not sufficiently described, please see below
Design may not be optimal, please see below
Validity of the findings: Impact and novelty OK
Data robust and statistically sound OK
but impaired by low follow-up rate
Additional comments: The Introduction is well written and points to an important issue to be addressed.

Methods:
To the present reviewer it is not clear how this lot of information for the patient in the GLITtER intervention arm can be delivered within 40 minutes.
Furthermore, I wonder whether it is possible to deliver a control intervention not including the new knowledge about the pain system and inconsistent associations between findings on spinal imaging and back pain. Most therapists know about this, and I find it difficult to imagine how a therapist can deliver a standard control intervention without involving this knowledge.

Discussion:
The Discussion should be shortened and in stead issues presented below may be considered.
The two main problems were the slow recruitment and the low follow-up rate.

Slow recruitment:
According to the present reviewer, the information sheet for patients was not appropriate.
We know reassurance is important as well as worrying and health anxiety1. However, a patient would not like to be met with "the need for reassurance" as an objective. The patients referred for non-urgent secondary health care usually has a long-lasting pain problem interfering with their life. They want to know: What is the cause of pain and what can be done (and perhaps also: is it dangerous and what about the prognosis?).

Proposal for another wording of the information sheet:
It is well recognized worldwide that relevant information for LBP patients is essential for achieving good results. New knowledge about pain in general and the relation between structural changes on spinal imaging and pain is now available. This research is interested in testing whether a more detailed information package for patients may affect recovery. The participants will receive one of two information packages and follow-up will be arranged. The standard treatment will not differ between groups.

Low follow-up rate:
This is possibly the most difficult problem to solve, and a solution is essential for a large scale study to succeed.
Possible explanations:
The back problem has disappeared or has changed to a minor problem. Usually, it is the younger and less sick patients that do not respond to follow-up.
Another explanation: Patients do not think that the health care delivered was relevant for their problem.

Suggestions:
Securing that the problem is sufficiently severe by demanding some kind of sick-listing as supplemental inclusion criteria. Sick-listing and loss of contact to the labor market are the most important issues in non-specific LBP.
Arrange a control visit after three months indicating that the problem is taken seriously. If the patient does not show up, he or she may be contacted.

Consideration on ethics:
Is it ethically sound not to inform a patient about the present knowledge about the pain system and the poor association between findings on spinal images and pain as well as prognosis?
Suggestion for design solving this problem: Arranging a follow-up visit after 3 (or 6) months. The patients not receiving the new package in the first place will have the information package in the second place.
Considerations on design:                                                                                The low rate of follow-up makes it difficult to conclude anything regarding differences in outcome between intervention groups. However, the present reviewer think that there would be a high risk for a randomized trial to show no differences in outcome between the two interventions, especially because of the considerations mentioned in the Methods section above.
Is the proposed randomized design the optimal design? Another kind of randomized design would  be to deliver a standard intervention, and then contacting the patients for inclusion in a randomized study delivering a supplemental intervention by another organization, a study design used elsewhere2. A population intervention comprising two lectures on the workplace was effective in reducing sick-listing due to LBP the following year3. Hence, that study showed how important relevant knowledge about back pain is for appropriate back pain behavior. Would a population strategy be more relevant?
Minor issues:
In Figure 2 it looked like every patient receiving two clinical interventions, not one. Why?
What were the "pragmatic reasons" for stopping inclusion after 4 months?
Should available MRI also be one of the inclusion criteria?

References
1. Jensen OK, Nielsen CV and Stengaard-Pedersen K. One-year prognosis in sick-listed low back pain patients with and without radiculopathy. Prognostic factors influencing pain and disability. Spine J 2010; 10: 659-675.
2. Lambeek LC, van Mechelen W, Knol DL, et al. Randomised controlled trial of integrated care to reduce disability from chronic low back pain in working and private life. BMJ 2010; 340: c1035.
3. Frederiksen P, Indahl A, Andersen LL, et al. Can group-based reassuring information alter low back pain behavior? A cluster-randomized controlled trial. PLoS One 2017; 12: e0172003.


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 QUASI-RANDOMISED, CONTROLLED, FEASIBILITY TRIAL OF GLITTER (GREEN LIGHT IMAGING INTERPRETATION TO ENHANCE RECOVERY)—A PSYCHOEDUCATIONAL INTERVENTION FOR ADULTS WITH LOW BACK PAIN ATTENDING SECONDARY CARE
Review round: 2
Reviewer: 1

Output:
Basic reporting: All domains acceptable
Experimental design: All domains acceptable
Validity of the findings: All domains acceptable
Additional comments: You have adequately addressed my comments, thank you.


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 QUASI-RANDOMISED, CONTROLLED, FEASIBILITY TRIAL OF GLITTER (GREEN LIGHT IMAGING INTERPRETATION TO ENHANCE RECOVERY)—A PSYCHOEDUCATIONAL INTERVENTION FOR ADULTS WITH LOW BACK PAIN ATTENDING SECONDARY CARE
Review round: 2
Reviewer: 2

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: Although major revisions have not been performed in the manuscript, I am satisfied with the adjustments in the manuscript, and I am glad that the authors seem to have taken into account my critical points and will include these considerations in the planning of a randomized controlled trial. I am not able to see my references at the end of their answer, but apparently the authors have seen the references.
It is very important that the design of a future randomized trial is optimal, so that the study will show a realistic picture of the importance of the information package for LBP patients. To the present reviewer there is a high risk of finding no difference in outcome between the two interventions as they are described at present. A negative result will have great negative impact of the whole discussion regarding LBP patients´ need for relevant information.


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: SPATIAL AND TEMPORAL PATTERNS OF HUMAN PUUMALA VIRUS (PUUV) INFECTIONS IN GERMANY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. The title is a bit misleading since it’s not clear if it’s human or bank vole infections with PUUV the authors refer to. Also, PUUV should be given directly after Puumala virus. Therefore, I suggest to change the title to either “Spatial and temporal patterns of human Puumala virus (PUUV) infections in Germany” or to avoid any confusion: “Spatial and temporal patterns of nephropathia epidemica (NE) incidence in Germany”.

2. The manuscript (as also indicated by the title) deals with PUUV. Why are other pathogens included in the manuscript? This inclusion is not motivated in the introduction and does not get sufficient attention in the analyses/results and discussion. In my opinion, the authors should exclude the other pathogens completely. They can be the topic of another and completely different manuscript. Focusing on PUUV, the manuscript is sufficiently interesting. For PUUV, the bank vole is the only reservoir host. For the other diseases/pathogens, other mammals are involved and even vectors. This aspect (apart from many other issues) requires much more attention than given right now. Also, other mechanisms are probably involved in disease transmission to humans.

3. L. 16 but also l. 54-55. To my knowledge, the bank vole is the only competent reservoir host, i.e. not only the main host as stated by the authors. References: Klingström, J. et al. Rodent host specificity of European hantaviruses: Evidence of Puumala virus interspecific spillover. J. Med. Virol. 68, 581–588 (2002). Brummer-Korvenkontio, M. et al. Nephropathia Epidemica: Detection of Antigen in Bank Voles and Serologic Diagnosis of Human
Infection. J. Infect. Dis. 141, 131–134 (1980).

4. L. 30. There is no need to include the German word “Meldepflicht”. In English, such a disease is called a notifiable disease and the sentence should be changed accordingly. The authors actually use the term in the manuscript (l. 108) and should do so also in the abstract.

5. The authors refer in the introduction to the ecology of bank voles and mention transmission risk among bank voles, but don’t explain how humans contract NE. Where and when is PUUV transmitted to humans? What is the main contact zone? This is shown in Figure 1, but should also be explained in the text. In fact, the authors need to discuss different aspects of the contact zone in much more detail. In the discussion, it’s only mentioned in one section (l. 319-322). It’s interesting that the authors found a significant relationship with forest cover in their analyses. However, this relationship just reflects potential hotspots of the bank vole as a forest dwelling species. HOW do people get infected? In the forest? In the discussion, the authors refer to outdoor activities in Northern Europe (l. 314-315). But it’s hardly walking in the woods that is a human risk behaviour. Also with reference to Vaheri et al. 2013, the authors should be more specific in terms of which activities that increase transmission risk in northern Europe. More important though: What are the high-risk activities in Germany? Are they the same as in northern Europe? How does this fit with the temporal peaks of human PUUV infection in northern Europe and Germany. It’s this kind of discussion that would be really interesting and improve the manuscript.

6. L. 98. What kind of spread do the authors mean?

7. L. 110. Explain TBE and not only refer to the German term. But see my general comment to delete other pathogens/diseases.
Experimental design: 1. L. 114. PUUV is a notifiable disease in Germany since 2001 (l. 86). The authors use human PUUV data since 2001. There is hence a risk that at least in 2001 human PUUV cases are not as frequently reported (due to unawareness). Have the authors considered this potential bias in their analysis? It’s mentioned in the discussion, l. 293-295, but what are the implications for their study? Should the authors for example exclude data for the first and even second year from their analyses?

2. L. 121. Mention that ArcGIS is a software for analysis of GIS-data. ArcGIS is mentioned at three places in the methods. It should be sufficient to mention once that you did all spatial analyses with this software.

3. L. 152. What is “Hesse”? A state? Clarify.

4. General aspect in Methods. For some datasets, the authors give the spatial resolution of their data (forest data). But what is the spatial resolution of all other spatial data that were used and at what spatial resolution were the analyses finally performed?

5. L. 131 and 156. The authors performed generalized linear modelling. More details on these analyses need to be given. Any data transformations? Which distribution was used and which link function was used? Table S1 gives some details, but not all. All details need to be given in the Methods.
Validity of the findings: 1. Figure 2. For readers, not familiar with German geography, mentioning the different states does not help to understand the maps. Either the authors should refer to geography in terms of NSEW or the authors should include a separate map of Germany where they indicate the states they refer to. Since data from 2016 are not included in the analyses, the authors could for example delete the map for 2016 and use this panel for the suggested map, instead. In the legend: What does RKI refer to? I don’t think it’s necessary to give the projection type in the legend.

2. Also with reference to my comment to Fig. 2, the authors mention several regions and cities in the manuscript (Northeim, Dessau-Rosslau). Sorry, but these places don’t mean anything to readers outside Germany. The authors need to find a better way to relate to geographic locations.

3. L. 177. Do the authors really want to refer to Fig. 3? Shouldn’t it be Fig. 2? Otherwise, I don’t understand this sentence.

4. L. 178-179. Isn’t this contradictory to what is mentioned in l. 168-170? If there is an increase in infection numbers in some areas, but not the country level, this should be clarified in the text. How was the trend tested? There seems to be cyclicity in the data. Was that considered?

5. Figure 3. Sorry, but I don’t understand the x-1 . x-3. To increase readability, the authors should use the same time scale for all panels. How is summer defined (which months)? In the lowermost panel, the authors refer to “HV infections”. Do you mean human PUUV infections? Should be explained in the legend. HV infections and PUUV infections are used in parallel. To not confuse the reader, please use only PUUV infections.

6. L. 180-187. The x-1 x-2 aspect is not easy to understand (see also my comment to Fig. 3). If lags are used, this should be mentioned in the methods. Also the value of the lag-phases needs to be motivated.

7. Figure 4. Please change the colour or pattern of the black or blue line. Even with a version printed in colour, it’s not possible to see the difference between the two.

8. Results related to Fig. 5/Table S1. Table S1 includes the actual interesting results, whereas Fig. 5 just illustrates the results with a map. Table S1 should be moved to the result section.

9. Please check citations in the text. Parentheses are sometimes put at strange places (e.g. Reil reference l. 236 and Jacob reference l. 247.

10. L. 284-286. Statement should be supported by references.

11. L. 333-334. Sorry, I don’t understand what the authors mean with this sentence in relation to the previous sentence.
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: ON THE MORPHOLOGICAL VARIABILITY OF ICHNIOTHERIUM TRACKS AND EVOLUTION OF LOCOMOTION IN THE SISTERGROUP OF AMNIOTES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Dear Editor
I reviewed the manuscript entitled “On the morphological variability of Ichniotherium tracks and locomotion upgrading in the sistergroup of amniotes” by Michael Buchwitz and Sebastian Voigt. The manuscript represents an interesting quantitative approach to a very well-known ichnotaxon from the Late Carboniferous to Early Permian ichnological record. However, some weaknesses in the methods used may have a greater impact on the interpretations and conclusion of the work. Below some indications and discussions are reported that must be carefully considered before the manuscript can be considered for publication. I'm not a native speaker, but English seems correct and very fluent.
Below, some methodological considerations and other more theoretical ones are reported, which I hope can improve the manuscript and the conclusions obtained and presented.
Experimental design: -Concerning the Principal Component Analysis, from the dataset results, as usual, the presence of several missing entries. It would be useful to specify how the missing values were handled in the analysis. In PAST the default modality to replace missing entries is the ‘mean value imputation’: however it is largely preferable to use the ‘iterative imputation’ algorithm (Hammer 2013). For the iterative imputation the missing values are replaced by their column average in a first stage; a PCA analysis is then run and used to compute regression values for the missing data, and this procedure is simply iterated to reach convergence (see Hammer 2013). If this algorithm was not used, it is strongly recommended to try to redo some analyses to see if significant different results are obtained.

-In the same way, if the raw data were not log-transformed before the analysis, misleading results can be obtained. Transformation into logarithm is strongly recommended to fit linear models and for the correspondence of the log-transform to an isometric null hypothesis (see Chinnery, 2004; Cheng et al., 2009; Romano and Citton, 2015, 2016; Romano, 2017). Again it is recommended then to perform the analysis only after having log-transformed the raw data.

-It would be useful to show the loadings of the single principal components, and describe briefly to what the greatest variance in each component is linked. If, for example, the length of digit IV contributes consistently to the variance (for convention loadings values greater than 0.3 and lower than -0,3) the use of this length to normalize the others results in a both methodological and conceptual error.
It might also be useful to show the scatter plot of components 2 vs 3 (and all other components with significant variance), which very likely are more related to morphometry of the footprints and trackways parameters rather to absolute dimensions. Usually is fine to show only the first two principal components if they describe more than 95% of the detected variance. However, in the submitted work the first two components describe on average only 80% of the variance; thus is there an additional 20% of variance in other components which might be useful to show, and perhaps lead to different discussions and conclusions. In the case of PCA performed on the six trackway parameters, the two first principal components account for only about 63% of the variance. It is therefore necessary to show how the remaining 40% is distributed and if the scatter plots considering the other components provide different result.
An analysis of PCAs using digit lengths in manus and pes of Ichniotherium has already been conducted recently, and described in detail in Romano and Citton (2015). It might be worth mentioning briefly this work and comparing the results with the new results.

-One element that can bring to weak results is the choice of the homologue points for digit measurements. In the manuscript, the free digits length is used, a fairly weak character that can change consistently even within the same trackway (pers. obs.), due to factors both directly related to the mode of locomotion and interaction between substrate and autopods and of a purely taphonomic nature (substrate conditions and relative footprint preservational type). It is recommended otherwise to use the phalangeal length of the digit (see, Leonardi, 1987; Romano and Citton, 2015, Fig. 1). In fact, the most useful method to obtain anatomical information about the trackmaker is the measure of the digit phalangeal portion length, concerning ‘…the measure of the segment that joins the distal extremity of the digit with the corresponding mid-point of the metapodial-phalangeal pad’ (Leonardi, 1987, p. 47), which is more closely related to the real anatomical length of the digit. If the metatarsal-phalangeal pad is not visible or preserved, it is advisable not to consider such footprints in the analysis. In fact, is better to have fewer footprints but definitely linked to a real osteological pattern and structure, rather than many tracks where digit lengths are extremely variant, and not depending on the trackmaker's anatomy. It is likely that, by decreasing the number of tracks to the best and anatomically significant footprints, the distance between the three recognized morphotypes in I. cottae reduces or totally disappears.

-Another possible problem is that the PCAs were performed not on linear measures, but on ratios between measures (in particular the various lengths normalized for digit IV). First of all, it is strongly advised to not use ratios at all in principal component analyzes (see Hammer and Harper, 2006); ratios are best indicated, differently, for classical cluster analyses. By dividing all the measures by the length of digit IV (or by other lengths), the necessary independence of the different variables is lost (a fundamental requirement for classical PCA), with the possible obtainment of misleading trends or clusters (especially if the digit chosen as reference is variant or peculiar). In fact, normalizing the same measure can lead to more uniform and separate groups, but nevertheless artificial. The same methodological problem applies to track parameters included as a ratio, and normalized for the length of digit IV (or other lengths). According to Hammer and Harper (2006) “Compositional data (relative proportions) must be analyzed with a special form of PCA (Aitchison 1986, Reyment & Savazzi 1999), because we need to correct for spurious correlations between the variables”. The biggest problem is indeed the “spurious correlations”, with detection of artificial clusters due to normalization, and to the non-independence of variables.

-Since in the work a sort of evolution in posture and in trackways parameters is described, with Ichniotherium preaesidentis as outgroup, followed by I. sphaerodactylum, I am surprised that these taxa have not been included in the PCA analyses and in the other graphs of figures 10 and 12. Such an analysis (by using linear measures, as already indicated, and not ratios) it could show how the three recognized morphotypes for I. cottae result closer to each other than to I. praesidentis and I. spaherodactylum. If that is not the case, it means that the length of the fifth digit is not a solid and sufficient character for the division of ichnotaxa. Since the authors speak of phylogeny, it is good to remember how the use a single character is typical of the nineteenth-century pre-cladistic typological philosophy. Starting with Hennig, if one want to talk about phylogeny, is necessary to consider the congruence tests of a complex set of characters (for example under the principle of parsimony or other principles), and not of individual characters (see Romano and Nicosia, 2015).
Validity of the findings: -An important element to be discussed is the ichnotaxonomic consequences of the study. According to the authors, within the specimens referred to Ichniotherium cotte (on the basis of a relatively short digit V) three distinct morphotypes are recognizable, in particular the 'Birkheide-Gottlob type', the 'Bromacker type' and Hainesi-Willsi type'. Again according to the authors, each of the morphotypes shows a functionality and locomotion substantially different, therefore attributable to three different trackmakers (or evolutionary degrees in the conclusions). A first crucial point on the philosophical level is the problem to include three different recognized biological trackmakers under the same ichnospecies; especially if sufficient characters are available to even distinguish evolutionary degrees in locomotion and functionality from trackways parameters. The question could be as follows: if such a high number of track parameters to distinguish three morphotypes and different functionalities are available, why not set up three separate ichnotaxa? From what has been reported and discussed in the paper, seems that the fundamental feature (the “synaphomorphy”) characterizing Ichnotherium cottae is simply a relatively short digit V. However, the length of a single digit, even at the level of genetic plasticity, is an extremely variant element in evolution, with loss and addition of phalanxes in repeated and paraphyletic ways. It seems that this character on which all the I. cottae “box” is founded, results weaker than a large number of trackways parameters, best referable to different trackmakers. If the ichnotaxonomy, in a new illuminated vision, must be based on natural biological taxa (i.e. zoological trackmaker and their unique combination of synapomorphyc, plesiomorphyc and autapomorphyc characters; see Olsen, 1995; Carrano and Wilson, 2001; Romano et al., 2016), it is difficult to imagine that different degrees of evolution in locomotion an functionality (referable to different trackmakers as found in the work) are hierarchically subordinate to the number of phalanxes on a single digit, within the framework of the hierarchic enkaptic system founded by Willi Hennig.
Secondly, one may wonder if having such conservative autopod structures in all morphotypes, we are dealing just with a same kind of biological trackmakers in different ontogenetic conditions, and under different types of locomotion. Simply changing the speed, trackways parameters (as experimentally observed) change accordingly, with trackway light that narrows, stride that increases, axes of autopods more parallel to the direction of advancement and so on. If the various track parameters change together (strong covariance) from a morphotype to another (what seems to happen), it would be more parsimonious to imagine a change in the locomotion and speed of the same trackmaker type. After having seen the tremendous difference between a normal sprawling crocodile and the same individual under a galloping locomotion, I think that the simple trackway parameters must be taken with extreme caution in obtaining greater conclusions in the macro-evolutionary field.
Another element that could be taken into consideration is the differential depth of the different portions of the footprints, as an evidence to infer the trackmaker biomechanics. In fact, as shown in some analyses performed also on Ichnotherium material (see Romano et al. 2016), such a study can shed light on the various functional axes active from time to time during stroke progression, and highlight synapomorphyc characters of a particular vertebrate clade, mirrored in the preserved tracks. So, it would be interesting to know whether in the three recognized morphotypes within Ichniotherium cottae, the differential depth of various footprint portions is uniform during the three main phases (‘touch-down’, ‘weight-bearing’ and ‘kick-off’ phases), or if substantial changes in the distribution of pressures are observed (and therefore in biomechanics and functionality that can be inferred).

The authors are free to contact me for any points raised on this review
kind regards
Marco Romano
Berlin
11/10/2017

Literature mentioned
Aitchison, J. 1986. The Statistical Analysis of Compositional Data. Chapman & Hall, New York.
Carrano, M.T., Wilson, J.A., 2001. Taxon distributions and the tetrapod track record. Paleobiology. 27, 564‒582.
Cheng, Y.N., Holmes, R., Wu, X.C., Alfonso, N., 2009. Sexual dimorphism and life history of Keichosaurus hui (Reptilia: Sauropterygia). J. Vertebrate Paleontology
29, 401e408.
Chinnery, B., 2004. Morphometric analysis of evolutionary trends in the ceratopsian postcranial skeleton. J. Vertebrate Paleontology 24, 591e609.
Hammer Ø. 2013. PAST Paleontological Statistics Version 3.0: Reference Manual. University of Oslo.
Hammer, Ø.& Harper, D.A. T. 2006. Paleontological Data Analysis. Oxford: Blackwell Publishing Ltd, 351 pp.
Liu, J., & Bever, G. S. 2015. The last diadectomorph sheds light on Late Palaeozoic tetrapod biogeography. Biology letters, 11(5), 20150100.
Olsen, P.E. 1995. A new approach for recognizing track makers. Geol. Soc. Am. Abs. Prog., 27, 86.
Reyment, R.A. & E. Savazzi. 1999. Aspects of Multivariate Statistical Analysis in Geology. Elsevier, Amsterdam.
Romano, M., 2017. Long bone scaling of caseid synapsids: a combined morphometric and cladistic approach. Lethaia. http://dx.doi.org/10.1111/let.12207.
Romano, M., & Citton, P. 2015. Reliability of digit length impression as a character of tetrapod ichnotaxobase: considerations from the Carboniferous–Permian ichnogenus Ichniotherium. Geological Journal, 50(6), 827-838.
Romano, M., & Nicosia, U. 2015. Cladistic analysis of Caseidae (Caseasauria, Synapsida): using the gap‐weighting method to include taxa based on incomplete specimens. Palaeontology, 58(6), 1109-1130.
Romano, M., Citton, P., & Nicosia, U. 2016. Corroborating trackmaker identification through footprint functional analysis: the case study of Ichniotherium and Dimetropus. Lethaia, 49(1), 102-116.
Additional comments: -In Figure 1C the last occurrence of diadectids is made to correspond to the Kungurian. However, the new diadectid Alveusdectes fenestralis has been recently described from the Upper Permian of China (Liu and Bever, 2015). It may be useful to update the scheme using the new cladogram provided by Liu and Bever (2015, fig.2, p. 4), and extending the ‘Diadects and allies’ branch up to the Wuchiapingian.

-In the text is highlighted “a surprising difference between the Bromacker sample and older trackways from the Birkheide and Gottlob localities”. However, two of the three specimens from Gottlob in Figure 10 C fall completely into the morphospace of Bromacker. Moreover, an overlap is also present with the Birkheide specimens in Figure 10 D and again with the ones from Gottlob in Figure 10 E.


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: ON THE MORPHOLOGICAL VARIABILITY OF ICHNIOTHERIUM TRACKS AND EVOLUTION OF LOCOMOTION IN THE SISTERGROUP OF AMNIOTES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language is generally good, but there are a few instances that should be fixed. Some examples where the language could be improved include:
-Title: What is ‘locomotion upgrading’ ? This is an awkward statement that is used repeatedly in the manuscript. Maybe change it to be an increase in efficiency? A suggestion for the title is: “on the morphological variability of Ichniotherium tracks and the evolution of locomotion in the sistergroup of amniotes”
-“number of couples” appears throughout text and in supplementary data… does this mean imprint pairs?
-Line 102: group of all yet undocumented Ichniotherium…
-Line 163: orientations towards walking direction… change to orientations in direction of movement
-Line 249: PC 1 and 2, not pr 1 and 2
-Line 255: Its more inward orientation… Change to The more inward
-Line 264: …distinction of THE Maroon sample…
-Lines 278-282 unclear phrasing. They are not distinct from each other? Or the rest of the sample?
-Line 290: …That does never fall below… not fall below
-Line 295: …causes much of overlap with the Birkheide… The overlap
-Line 297: ‘curve walk’ is awkward
-Line 304: direction of movement, not walk
-Line 333: ‘morphologically close’ change to morphologically similar.
-Lines 427-430: This sentence is very long and awkward.
-Line 455: hypothetical
-Line 542-3: …of the skull towards higher ability of processing plant material…
-Line 562-564: awkward sentence
-Throughout the manuscript: Ichinotherium is abbreviated to I. inconsistently.

Line 544: add this more recent reference: Reisz, R.R., and Fröbisch, J. 2014. The Oldest Caseid Synapsid from the Late Pennsylvanian of Kansas, and the Evolution of Herbivory in Terrestrial Vertebrates. PLoS ONE 9(4): e94518.
Experimental design: The rationale for the study is not clearly stated. The abstract says: 'Here we document variation of digit proportions and trackway parameters….' Why? Lines 104-123 state the steps that were taken to perform the study, but lines 104-105 should state the question/problem being addressed. Is to document if all tracks attributed to I. cottae are in fact I. cottae? Is it to see if all tracks of I. cottae can be attributed to the same trackmaker? Are you only focusing on I. cottae because I. sphaerodactyulm and I. praesidentis are less variable, or have a smaller sample size? Why would you expect I. cottae to belong to separate trackmakers? I think the paper would be much stronger with a directed rationale for the study and a justification for the focus on I. cottae.

I have one concern with the statistical analyses. The inclusion of angle measurements and linear measurements together in the PC analyses might be problematic, as the angles are circular and the other measurements are linear data. I am unsure if both types of data (with different units) can be combined in a PCA. It is possible that transforming the angle measurements, or a separation of angle and linear measurements for the PC analyses will avoid any potential problems. There are many books that discuss combining linear and circular data in descriptive statistical analyses, for example:
Batschelet, E., 1981. Circular statistics in biology. ACADEMIC PRESS, 111 FIFTH AVE., NEW YORK, NY 10003, 1981, 388.
Berens, P., 2009. CircStat: a MATLAB toolbox for circular statistics. J Stat Softw, 31(10), pp.1-21
Jammalamadaka, S.R. and Sengupta, A., 2001. Topics in circular statistics (Vol. 5). World Scientific.
Mardia, K.V., 2014. Statistics of directional data. Academic press.
Validity of the findings: The findings are valid. Detail should be added to the figure caption for Fig. 16 explaining what is occuring at each 'evolutionary step' (1–5). It is described in-text but would be much clearer if the changes occuring at each step could be described in the figure caption. Is the phylogeny based on a previously published phylogeny for diadectids? Do nodes a-d correspond to any specifically named groups?

The findings should relate back to the question/problem being addressed (which is not clear in this paper).
Additional comments: Overall, the paper is very interesting. I like that the trackway record can be used to infer the evolution of locomotion in diadectids. The figures are nice and clear. With a few minor changes, the manuscript will be ready for publication.


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

Input:
Title: ON THE MORPHOLOGICAL VARIABILITY OF ICHNIOTHERIUM TRACKS AND EVOLUTION OF LOCOMOTION IN THE SISTERGROUP OF AMNIOTES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Please see attached PDF
Experimental design: Please see attached PDF
Validity of the findings: Please see attached PDF
Additional comments: Please see attached PDF


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: ON THE MORPHOLOGICAL VARIABILITY OF ICHNIOTHERIUM TRACKS AND EVOLUTION OF LOCOMOTION IN THE SISTERGROUP OF AMNIOTES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Good
Experimental design: Good
Validity of the findings: Good
Additional comments: I think that all reviewer comments have been addressed appropriately and the paper is improved. My only suggestion is to include the rationale for the study in the abstract, and see attached file for other small corrections.


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: ON THE MORPHOLOGICAL VARIABILITY OF ICHNIOTHERIUM TRACKS AND EVOLUTION OF LOCOMOTION IN THE SISTERGROUP OF AMNIOTES
Review round: 3
Reviewer: 1

Output:
Basic reporting: The text is professional, albeit extremely dense and likely impenetrable for many readers.  The same can be said of some of the figures (esp. 1, 13, 15), which are crowded to the point of being difficult to read.  While they could be made more accessible, to do so would require a significant re-write that I do not feel is necessary.
Experimental design: My main worry is that so many of the tracks figured have a very ambiguous morphology between digits and the rest of the foot, which makes reliable measures of digit length somewhat difficult.  The authors do address this in the text (ln 203), but still many figured tracks do not show connected digits and 'palm/sole'.  Perhaps my concerns could be addressed with a figure showing the measurements as taken on some of the more disconnected tracks.
Validity of the findings: The authors make a case for locomotor evolution observed in these tracks.  Their conclusions are slightly cautious: "Since they have mainly been inferred based on European 625 trackways records, these changes might either represent a local signal...".  I would like to see a little caution in the abstract too.  While their conclusions are supported by their data, I think the vagaries of sample size and track morphology warrant more tentativeness.
Additional comments: Whilst I think it would be unreasonable to suggest a re-write to make the manuscript more accessible, there are places where sentences can be tidied up a little.  For instance, lines 112-117 are a single sentence paragraph.

Ln 141, 230; It's not clear what the authors mean by 'true trackway'.  Given that current ichnological terminology (Marty et al 2016) defines a 'true track' as the foot-sediment interface, or a direct track, it seems that this is not what the authors are referring to with 'true trackways'.  If they are, it means all other tracks they measured are transmitted tracks or overprints, in which case measures of digit length loose meaning.  If 'True trackway' refers to a specific sequence of footfalls, then the authors may wish to use a different term, e.g. 'complete step cycle'

ln 601:  after 'functional traits' the authors should add "providing trackmaker ID can be made with confidence"


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

Input:
Title: THE ASSOCIATION BETWEEN CHRONIC BULLYING VICTIMIZATION WITH WEIGHT STATUS AND BODY SELF-IMAGE: A CROSS-NATIONAL STUDY IN 39 COUNTRIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper explores the association between objective weight status (BMI), subjective weight status (self-image) and being bullied using a large cross-national open data.

The language is clear and professional, but with minor type or grammar errors. I suggest the authors go through the manuscript again carefully.

This manuscript examined the correlation between weight status and being bullied. So, according my understanding, the logic should be that overweight or underweight could "cause" being bullied. Thus, the literature (introduction section), especially the second paragraph should include the influencing factors of being bullied, rather than the consequence of being bullied. A brief review of the influencing factors of being bullied (as the variables the authors used in the analysis, the school climate, family structure, SES, demographic etc.) with a focus on weigh status would make the logic more smooth.

The manuscript's structure is clear and well presented.
Experimental design: The data used in this analysis is a secondhand open data, so the experimental design should not applicable.

Research question is clear and well defined, and can contribute to current knowledge gap.

For the measures section, I suggest the authors grouped the measures in to dependent variable (school bullying victimization), weight status (predicting variable), and controlled variables ( SES, family structure, classmate support). So the structure would be much clearer.
Validity of the findings: The statistical methods adopted are appropriate.  Data is robust. Discussions and Conclusion are well stated.

For the regression tables, it is suggested that the authors can add a note to every regression table, covering the information such as the controlled variables in the regression.
Additional comments: no comment.