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: DISTRIBUTIONS OF EXTINCTION TIMES FROM FOSSIL AGES AND TREE TOPOLOGIES: THE EXAMPLE OF MID-PERMIAN SYNAPSID EXTINCTIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See comments.
Experimental design: See comments.
Validity of the findings: See comments.
Additional comments: This is an excellent manuscript, presenting a new method for accommodating the incompleteness of the fossil record when trying to estimate time of extinction (and origination).  I have no doubts that it should be published in PeerJ.  The method is able to make better use of the data than current methods, with the sacrifice being the need for assuming constant preservation rate across all lineages (which the standard methods, those based on Strauss and Sadler [1989], (S.S.) do not do).  But as one of the strongest proponents of the S.S. set of methods, I find the method proposed here very appealing.

Below I have a set of suggestions for improvement.   Most are minor, but I think the author need to pay particular attention to:

#10, #12, #46, #47 (what really makes their method perform better than S.S.; I don’t think it is the reason they state in the abstract, or at least that is just part of the reason)
#25 (sensitivity to different tree topologies)
#26, #39b (we need the temporal data to be presented somewhere, and ideally the rational for the age calls and their ranges).
#34–36 (effect of only taking simulations with > 20 taxa on the actual preservation rates simulated)
#39 (increasing the clarity of Figure 3 (and 7).
#41 (we need more data to have confidence in the claim of a no end-Kungurian extinction, given the insidious role of hiatuses in the rock record)
#43 (how to compute extinction density for clades)

And then also I have suggestions for a more balanced introduction (see #5–10).

1.	Line 13. The abstract says that the method is designed for a tree with extinct and extant taxa, but in the end their example has no extant taxa (which is not a problem).  I feel the sentence is a little bit of a ‘mis-direct’, in that red flags go off in my head when I see the inclusion of both extant and extinct taxa, because typically the extant taxa outnumber the extinct in numbers and data completeness, and thus can suffer from data imbalance where the Recent gets undue weight (this is a problem with other methods that incorporate fossils, in that they are still pretty biased, for example).  So, this rather long comment, in the end, amounts to the recommendation that the authors say something like “Given a phylogenetic tree of just extinct, or extinct and extant, or just extant taxa, where at least some fossil data are available, we present [I would not use ‘devise’, but this is largely a matter of taste] ….
2.	Line 16.  Is your method also unusual in that it can incorporate taxa known from just one fossil (this is not unusual for FBD, but it is for confidence intervals).  So maybe this part of the abstract needs to be a little more nuanced (in that ‘previous ones’ include disparate methods that ‘bite down’ on the data in different ways).  Maybe the simple solution is to simply be explicit about what you mean by ‘’previous one” (line 16).
3.	Line 23.  Virtually no one is going to know the Permian stage names (I don’t, and I am a paleontologist), so give us some help here, e.g., say something like Cisuralian (Mid-Permian, or whatever it is), and then, indicate that the next interval is younger in some way (you could also give approximate age in millions of years, that might make all the difference).
4.	Line 29:  Suggested rewording: “ … direct evidence (even if fragmentary) of the ….”
5.	Lines 44-45:  I know opinions differ, but I find Patterson and Smith flawed because it failed to take into account that the extinction of a paraphyletic group, does in the end, often (granted not always) equate the extinction of typically several lower-level taxa – so for example, P&S would have no end-Cretaceous extinction for fish or echinoids, which is just silly.  So, the point about paraphyly is of real concern, I agree, but I would urge the authors to be a little more nuanced here (especially as this issue has no bearing on the method they present).
6.	Lines 52-55.  Again I would urge moderation/nuance – higher taxa often represent group of species with similar morphologies, and thus similar ecological roles, so the diversity dynamics of higher taxa capture a different signal than species-level analyses, and can yield insights not possible with species level data (to take an extreme case, a species-only level analysis would not pick up the Cambrian explosion, or at least only see it as a pretty small burst of speciation, dwarfed by the Ordovician for example).  But the lack of intrinsic comparability for, say families, is real, so I am not disagreeing with the problems the authors identify (and Foote’s Ph.D. was based on trying to circumvent this by developing disparity approaches to deal with the issue).
7.	Lines 56-60.  Again, a little bit of moderation would be good.  For example, Foote (2003, J. Geol. 111:125) and Lu et al. (2006, PNAS 103: 2736) provide analyses of Phanerozoic marine biodiversity dynamics with corrections for the incompleteness of the fossil record.  But the point is well taken.
8.	Lines 61-69.  This paragraph mixes two things that need to be dissected.  First is the problem of low temporal resolution of binned data (typical of compilations), but again Foote has tried to deal with this (see his 2003 paper, referred to above).  Then there is the problem of Signor-Lipps when you actually have ‘section’ data available.  The only paper I know of that deals with the Signor-Lipps effect at the stage level is Lu et al. (2006, PNAS 103: 2736), who argue (and quantify) the effect at the stage level for Sepkoski’s data.  So, there is a (small) literature here on this topic ….

I would add here that my comments 5–8 I think could be accommodated easily, without adding much text – in the end, these points are immaterial to the method presented, but a more balanced set of views might increase acceptance of the method.

9.	Line 75.  You might also want to add Tavaré et al. (2002, Nature 416: 726).
10.	Lines 92-110.  Intuitively, it is not clear to me that the primary advance of the method proposed here is its ability to take into account diversification after the LAD of a lineage prior to its extinction.  Rather it seems to me that its ability to use all the fossil data (i.e., include lineages with just one fossil), and to use all the fossils together (at the cost of assuming a constant preservation rate), is the real strength.  As a test, have the authors tried the sensitivity analysis of turning off speciation after the LADS and seeing if it makes any difference?  Or is it simply that by allowing for post-LAD diversification, the method allows for that fact that the lineage might have lasted longer than one might have thought with the know fossil record.  So, maybe the argument that allowing for post-LAD diversification does have an intuitive basis.  I would encourage the authors to add in that intuition, whatever it turns out to be.
11.	Lines 111-125.  Agreed!  This is an exciting paper!
12.	Lines 126-134.  Agreed!  This is an exciting paper!  I wonder if these two points might be more (or as) important as the possibility of post-LAD diversification, and so I would encourage the authors to think about this, and maybe bring these points up higher in the paper, for example, in the abstract.
13.	Line 136.  Both extinct and extant taxa are mentioned – please see my point #1 above.
14.	Lines 142-146.  Nice distinction.
15.	Line 151.  You say your method assumes ‘fairly homogeneous’ fossilization with time.  It would seem that you actually assume a homogeneous rate, so delete ‘fairly’?
16.	Lines 151–162.  A potential red flag here.  You comment that a relatively homogenous fossil recovery rate for your taxa, globally, seems reasonable.  You then comment that you will not be following Lucas’ (2017) recommendation for a ‘best-basin’ style of analysis.  OK, I can live with that.  So, the big question for me is how did you correlate the sections to provide the resolution provided in your figures.  I have always balked at applying Straus and Sadler on global data for the inability to line up the appropriate sections (but Shaw, or Sadler’s type methods could be used).  So, I am sure hoping you deal with this appropriately – I will read on (but maybe let me know here that you will deal with this).
17.	The review of the extinction scenarios in the literature is a long section, but I think is of value.  However, it was almost too much for me, largely because I don’t know the stratigraphic nomenclature.  Now, in the description of the first proposed extinction ‘event’ you give some absolute ages, which I found very useful.  But then you don’t do so for the subsequent ones.  So, simply, I would add absolute dates in the paragraphs that begin on lines 200, 221, and 241, as you have for the paragraph that begins on line 187, to help keep the reader oriented.
18.	With respect to my comment #17, I wonder if a synoptic figure might help (but I can also see that there are enough variants of each of the proposed extinction scenarios that this might not be possible).
19.	With respect to comments #17 and #18, I find myself wondering how many of the variant hypothesizes of extinction rejected by this paper, where rejected because of the method itself, and how many were simply rejected due to improvements of the correlation scheme which you presumably had to develop to apply the method.  Dissecting out these two components might be useful for those who are interested in the method, and not the taxa (having said this I have now reached the paragraph on line 253, and this does a pretty good job of stepping back, so well done).
20.	Line 272.  Whenever I see cut-off like 95%, but with many taxa, I find myself reflexively wondering about whether a Bonferroni-type correction needs to be applied.  Yes, no?
21.	Line 272.  I don’t know where the Kungurian fits in!  I forget already if it relates the to 1st, or 4th of you reviewed extinction events (and given that you are not going to study them all, maybe you should say so, when you present them).  So, help me, by refering to a synoptic figure (if you decide to add one), or something ….
22.	Line 292.  Valuable note – very good.
23.	Line 300.  Valuable note – very good.
24.	Line 311.  Looking forward to reading about your age assignments (see also comment #16).
25.	Line 312.  Whoa, 15 x 10^6 trees!  And you picked just 100.  Have you performed any sort of sensitivity analysis on the impact of the uncertain tree topology??  You have to deal with the range of potential topologies.
26.	Lines 314-328.  I agree with the reasoning for working with absolute time rather than stratigraphic thicknesses, for several reasons.  So, no push back from me.  However:
a.	Can you add the age model and assigned ages you used in a Supplementary table, or whatever?
b.	More importantly, what is the impact of the uncertainties?
c.	How did you decide on the ages, and their potential ranges?
d.	Did you count fossil horizons at individual localities?  Or just give counts at the Formation level.
e.	We need a proper description of these data.
27.	Lines 330 and following.  FYI, I have not evaluated the maths or description of the FBD model.
28.	Lines 374-377.  Is this what you did to deal with the temporal uncertainties?  If so, please refer the reader when he/she is in lines 314-328 to the fact that they will be given an answer below.
29.	Lines 354-355.  For a paleontologist, this is cool.  I wonder if this capacity should be referred to in the abstract?
30.	Lines 409-410.  The units for these rates?  Be explicit (orig/ext per lineage per million years, what?).
31.	Lines 409-410.  So, you average longevity is 1/0.19 myr = ~5 million years?  Does that make sense with what you know about you taxa.  Maybe just mention the expected lineage duration with this extinction rate, so people can gain an intuitive feel for the nature of the simulations
32.	Line 422 vs. line 424.  I have probably missed something, but line 422 says 5,000 sets of rates, but line 424 says 1,000 simulated trees.  Can you reconcile this (either fix, or explain in the text why they are not the same)?
33.	Table 1.  So, I should be dividing the total number of extinct taxa by 1,000 to get the number/tree?  Maybe say so in the caption, directly.
34.	Table 1 (and Tables 2 and 3).  I think there is something amiss-misleading here.  If I am reading this properly, the preservation rate of 0.005 is giving ~21 taxa/tree, while the preservation rate 1,000x larger (5) is only giving ~36 taxa/tree.  How is this possible (not even double the number of extinct taxa despite the 1,000-fold increase in preservation rate)?!  I think the reason might be simple – on line 412 you state that you only took trees with > 20 fossils.  So, I presume that means that for the lower preservation rates (or most of them) you had to stochastically wait a long time for the very few trees that met your criteria.  In which case, I bet the actual preservation rate (measured retrospectively on the chosen trees) for those few trees was way higher than the numbers presented in Table 1.  Given the closeness of the values from the lowest to highest preservation rates (from 21 to 26 fossils/tree), it looks to me that the realized preservation rates are quite high and relatively uniform (at least in log-space), and that the reported fossilization rates are seriously misleading.  Can you compute the realized fossilization rates?  And if they are way higher than the simulated rates (as I suspect), then change the description in the text and presented data to reflect this point?
35.	Table 1.  Sorry for thinking out loud here ¬– but the %S.S. feasible column does show the expected trend, so I think another metric that would be of value for understanding the simulations is the total number of taxa (on average) in the simulations (or another way of saying this, what is the proportion of extinct taxa to total taxa).  It looks like you go from mostly singletons for the low fossilization rate, to mostly non-singletons for the rate that is 1,000x higher.  With respect to my comment #34, the %S.S. column is the most important, so I don't think the simulations need re-doing.
36.	Lines 425-437.  This may need a little re-writing considering comments #34 and #35.  I think saturation is happening (what else could it be?).  And that tells me that I can guess the size of your trees (because saturation means all taxa have fossils).  But also says that your censoring of the initial simulations also means the reported preservation rate (r) is misleading, and thus the ratio of r to p and q.
37.	Table 2.  Nice demonstration that the method they propose does what it claims to do.  Very good.  As an aside the fact that the italics values are almost always bigger than the non-italics suggests to me that the data amenable to S.S. are biased in some subtle way, which is why those values indicate confidence intervals that are too long (but this is my just thinking through the data presented to see if they make sense, and they do).
38.	Table 3.  This is good.  I think it is enough for this paper, but 95% confidence intervals are very long when you only have two fossils (19x the observed stratigraphic range).  I would be interested to see what the unbiased estimates look like for the true time of extinction (median gap size), or, simpler, the 50% confidence intervals.  The average of these should be 0 million years, roughly, with half above and half below the true times of extinction, if the method was working correctly.  But the Table does the job it needs to, and so while I am curious about the 50% confidence intervals (or in your case, the middle of the density distribution) it is not needed here (BUT, if they want to use their method to actually estimate extinction times, then my suggestion might help).
39.	Figure 3.  Nice.  But I have questions.
a.	Why the various shades of brown on the lineages (i.e., why not just one color?)?"
b.	For fossil occurrences I am expecting dots, but I am seeing ‘sausages’.  Do these indicate the age uncertainties?  If so, does that mean that the taxa with just one ‘sausage’ is only know from one fossil (or one formation, and you have not dissected out the fossils within that section?)?  Do tell!
c.	Pretty obviously the red bits are the extinction probabilities (please say so).
d.	In several cases the peak density for extinction seems to lie well within the ‘sausage’ (for example, for the top taxon Stereorhachis).  This does need some explanation (and may well be answered by your answers to (a)-(b)).
e.	I know the caption says the scaling of the bottom part of has been extended for clarity, but when I first looked at the figure, I had not read the caption, and thought the tree was crazy; how can those nodes be so deep without at least some fossils!?  So, maybe make the lines dashed, or light grey.  Better, why not just use the branch lengths from Figure 7, but leave off the probability densities, given how noisy the figure would be if they were included (and then you can get rid of at least the Devonian part of the figure that serves no purpose).
f.	Put “Million of years ago” on the x-axis, small print, at the lower left.
g.	Given that you are going to talk about three higher level taxa next, why not indicate their membership on Fig. 3?
40.	Figure 4.  Make the lines a little thicker, perhaps.
41.	Results.  Hypothesis 1 (starting line 456):  OK, nice, but a little simplistic in the interpretation.  As we all know you can’t find fossils if there isn’t any rock.  So, if there is a lack of outcrop at the top of the Kungurian, for example, then you can’t say much about the actual time of extinction of those taxa that you have shown disappear from the record before that boundary.  I would like to see two things done before the authors claim a non-Kungurian extinction:
a.	First, to help my own eye, it would be great if the taxa, or perhaps better, their probability density distributions were colored by their (coarse) geographic location.  Why?  Because if an a given region all (or most) of the taxa happened to survive into a time of no rock, then their inferred times of extinction would cluster about the time of the youngest available rock (so for example, I am suspicious about taxa 5, 6, [11], 21, 22, 29, 30, 40, [41], 42, [45], 46, 48, [49] – if they all came from the same geographic area, then the data look consistent with all of them disappearing from the fossil record at about the same time (which is interesting in its own right), and then if there is no younger rock (that goes to the Kungurian boundary) in that region, then you can’t say when they went extinct.
b.	Some sort of statement about what we know about the continuity of the taphonomic window for these taxa across the stratigraphic intervals of interest.
42.	Results.  Hypothesis 2 (starting line 476):  Maybe just say ‘fully extinct”, or something.  I was having trouble with post Kungurian survival given the previous results.  I guess what I am saying is that having the last occurrence of a whole clade much later the time of extinction of most of the constituent lower taxa is uncontroversial, but maybe you need to simply point this out, so a late extinction does not seem to contradict the earlier species-level extinctions.
43.	Results.  Hypothesis 1 (starting line 456):  You need to describe (probably in the methods section) how you compute the extinction density for a clade.  Do you use all the data for the clade (which would seem to severely violate the constant Poisson probability of finding fossils, given that the probability of finding a clade member is presumably proportional to the number of taxa present); or have you simply used the density of the single species with the latest potential extinction time; or have you multiplied the densities somehow?  This needs to be explained (or if it is, give the block of text its own section/title).
44.	Line 480-481.  You say that the Sphe. have a peak density near the K/R boundary, “as for Oph. and Edaph.”  I think this is just a typo – Oph. and Edaph seem to have much earlier peaks.
45.	Line 483.  You could also simply that there is a greater probability that the Sphe. survived the Kungurian than not ….
46.	Line 494. See comment #10.  I am not convinced that this is the reason the method performs better.
47.	Line 506.  Oh golly!  You seem to actually agree with my skepticism expressed in comments #10 and #46!  OK, you really need to change the relevant text throughout!
48.	Paragraph beginning on line 511.  Good!
49.	Sentence beginning line 527.   Marshall (1990, Paleobiology) suggested this (applying it to the platypus fossil record) for times of origin.  And maybe here cite the papers referred to in comment #7.
50.	Appendices.  For the record, I have not worked through the Appendices.


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: DISTRIBUTIONS OF EXTINCTION TIMES FROM FOSSIL AGES AND TREE TOPOLOGIES: THE EXAMPLE OF MID-PERMIAN SYNAPSID EXTINCTIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: General Comments: This manuscript presents an extension of the fossilized birth death model that tries to account for potential unseen diversification after the last appearance of a taxon in the fossil record, and applies it to the question of when ‘pelycosaur’-grade synapsids went extinct. The latter topic is of interest because there is on-going debate about the timing of pelycosaur extinctions (i.e., whether there was a tetrapod extinction event near the early-middle Permian boundary) and its potential relationship to the diversification of therapsids. Overall, I found the paper well organized and thought-provoking. The extension of the FBD model seems like it will be of general interest, and I think that the paper makes a positive contribution to our picture of synapsid diversification/extinction dynamics. Most of my comments are pretty minor, but one weakness of the paper concerns citations. There are a number of relevant papers, mostly published in the last 3-5 years, that I think should be cited in various places in the manuscript. As it is, the citations in the paper make it seem like something that could have been written a few years ago, and I think the additional references will help it feel more up-to-date.
Experimental design: see below
Validity of the findings: see below
Additional comments: Line 32: I’m not sure I agree with the statement that changes in rates of cladogenesis and extinction generated evolution radiations and mass extinctions. I suppose in some sense that’s true (i.e., a radiation can’t occur without an increase in speciation rate), but it seems like something that is more associated with those types of events instead of the generating force. The generating force that causes the increases in rate seems like it would be something like environmental change, the emergence of a key innovation, etc.

Line 37: I think spectacularly is a little hyperbolic here. I recommend replacing with greatly.

Line 47: Maybe provide some examples of studies that proved him right.

Line 53: change to lineages

line 56: change to ranges; also change to underestimates in the next sentence

line 60: change to: “...data as if they were the true stratigraphic ranges...”

Line 78: These papers pretty much deal with just the Permo-Triassic extinction, so I recommend adding ‘e.g.’ at the start to indicate they are just some examples given that other extinction events also have received a lot of attention. Also, maybe consider citing Viglietti et al. (2021, PNAS) as the most recent work looking at extinction patterns in the Karoo Basin during the PTME.

Line 87: change to considered

Line 90: I recommend making the sentence starting ‘See’ into a parenthetical citation in the previous sentence.

Fig. 1: I recommend changing the color scheme of this figure to make it more accessible (i.e., avoid using red and green together).

Fig. 1. caption: Change to: “A simulated extinct clade with sampled fossils represented by brown dots. Top: The clade’s complete evolutionary history. Bottom: The portion of the clade’s history observable from the known fossil record. Note that the ‘blue’ and ‘green’ taxa diversify before going extinct, but that these diversification events are not recorded in the known fossil record.”

Line 108: replace this with the

Line 116: change to cladogenetic events

Line 117: Brocklehurst (2020; Proceedings B) might be good to cite here as an example of a study that used a FBD-approach to look at extinction in some sense. His approach and interest to the problem is different than yours, but the anaysis was still partially framed in an extinction context.

Line 124: Maybe cite a couple of Spencer Lucas’ tetrapod biochronology papers here as well, since they are classic examples of using higher taxa this way.

Line 132: change to: “...(see Simulation Study below).”

Line 135: change develop to extending

Line 136: change namely to specifically

Line 155: replace on with to

Line 158: A couple of thoughts here. First, I agree that your method makes the most sense when applied globally instead of locally. However, it seems almost certain that fossilization rates (and sampling rates by paleontologists) will be uneven in such cases. Even in the pelycosaur example you use here, that is very likely. For example, thousands of specimens of your focal taxa have been collected from the south western U.S. during this time interval, but many fewer are known from Europe. Second, I don’t think the Olroyd and Sidor study is really appropriate to justify your assumption of even fossilization rates for a few reasons. First, it deals with a different time interval (middle Permian vs. Pennsylvanian to early Permian). Second, it primarily deals with different geographic areas, given the shift in the main locations of tetrapod fossils from low latitudes to higher latitudes that takes place near the early-middle Permian boundary. Third, Olroyd and Sidor’s review shows that the middle Permian tetrapod record is quite unevenly sampled (e.g., many specimens known from areas such as Russia and South Africa, but very few from Brazil). Something like Brocklehurst et al. (2013) would probably be more relevant to cite, although the message of that paper may conflict with what you’re trying to say here.

Line 164: change to trees

Line 178: Because the epochs of the Permian have formal names (i.e., Cisuralian, Guadalupian, Lopingian), early/middle/late aren’t capitalized when talking about the Permian. This change should be made throughout the paper.

Line 181: I recommend citing Angielczyk and Kammerer (2018) here because that paper includes some discussion of the likely Carboniferous origin of therapsids as well. Spindler (2014) might also be good to cite since he tentatively re-identifies some Pennsylvanian material as representing therapsids.

Line 201: You definitely should cite Sahney and Benton (2008) here because it was really the start of the current discussion of ‘Olson’s extinction’. I also recommend citing Brocklehurst (2018) as well.

Line 220: Although he doesn’t consider Strauss and Sadler-style confidence intervals on stratigraphic ranges specifically, Brocklehurst (2018) is an attempt to address whether Lucas’ (2017) literal reading of the fossil record is likely to produce accurate results.

Line 221: change to event

Line 229: It’s a bit uncertain what you mean here by “about the same time.” Do you mean in Roadian (i.e., in reference to the previous sentence about Ennatosaurus) or the time of the end-Guadalupian extinction in general? More importantly, more recent studies have not found a decrease in therocephalian diversity at this time: see Huttenlocker and Smith (2017) and Grunert et al (2019). They disagree in the exact details of diversity increases at this time, but in general find evidence for increasing diversity across the Guadalupian-Lopingian boundary.

Lines 241-252: I think this paragraph needs to be updated to take into account the large amount of work that has been done on the terrestrial Permo-Triassic extinction (and ideally also work on the marine realm as well). For example, just focusing on work on tetrapods in the Karoo Basin and their geological and paleoenvironmental context, I strongly recommend citing papers like Smith and Botha-Brink (2014), Viglietti et al. (2018), Botha et al. (2020), Viglietti et al. (2021); Gastaldo et al. (2015; 2018, 2019a, 2019b, 2020, 2021). There’s a number of other papers that you could cite dealing with other aspects of the Karoo faunal turnover as well, covering things like changes in bone histology, community structure, etc. Such citations would give a better idea of current thinking on the severity and duration of the extinction, as well as current debates about whether the marine and terrestrial events were synchronous and the degree to which the apparent extinction might be the result of other factors such as lateral facies changes.

Line 270: It would be good to include some citations that lead to the hypothesis that the clades went extinct in this order.

Line 282: insert comma between speciation and extinction

Line 293: change synapside to synapsids

Line 300: This also might be complicated by the geographic shifts in best-sampled areas going from the early to middle Permian (e.g., compare results in Benson and Upchurch 2013 to those in Brocklehurst et al. 2017).

Line 322: Maybe also cite (and use) Schneider et al. (2020), as that is a recent attempt at making global correlations and age estimates for Permo-Carboniferous terrestrial strata.

Figure 2 caption: change to fossil find

Line 342: maybe replace w.r.t. with ‘with regard to’ spelled out

Line 415: I assume here that you are using fossil ages instead of stratigraphic heights to calculate the Strauss and Sadler-style confidence intervals. You should note that in this section to avoid confusion.

Line 418: change since to because

Line 432: This is an interesting observation. Off the top of my head, I’m not aware of studies that have tried to compare the rates of speciation and fossilization in empirical datasets. That might be my ignorance, though. If there are studies that do this, it would be interesting to note how the rates they report compare to what you observed here; i.e., do they have fossilization (or fossil recovery) rates higher than speciation rates?

Line440: change since to because

Table 3 caption: I assume the units of the values presented here are in millions of years. Is that correct? If so, please note that in the caption.

Line 449: change to: “...which we call the mean...”

Figure 3 caption: please specify what the brown ovals represent on branches of the tree. I think these are observed stratigraphic ranges, but it’s not entirely clear whether that’s the case given that some have gaps, and others seem to be made of several overlapping parts.

Line 482: change while to although
Figure 4: The colored sections under the curves are hard to see without really zooming in. I might recommend making this figure into for separate figures (i.e., one for ophiacodontids, one for edaphosaurids, one for sphenacodontids, one for ‘other’ taxa).

Figure 5 caption: change to: “...and Sphenacodontidae base on our dataset.”

Line 498: I think it would be good to note here that the Strauss and Sadler approach (originally, at least) had somewhat different goals: determining confidence intervals on local stratigraphic ranges based on stratigraphic occurrence data in individual sections. So yes, your method works better for your focal question (i.e., confidence intervals on global stratigraphic ranges, taking possible unseen diversification into account), but it is also designed more specifically for that question than the original approach.

Line 516: particularly given the fact that most middle-late Permian tetrapod localities are in higher latitude areas, away from what seems to be the main geographic center of pelycosaur diversity

Lines 522-530: The initial report of dinocephalians in the lowermost Poortjie Member has recently been incorporated into the official revised version of the Tapiniocephalus Assemblage Zone (see Day and Rubidge 2020). Also note that although dinocephalian taxa play a role in defining the lower boundaries of the two Tapinocephalus AZ subzones, the upper boundary of the upper subzone is defined by the first appearance of Endothiodon. Therefore, the absence of dinocephalians is not strictly part of the AZ’s definition.

Line 534: The discussions of the Carboniferous origin of therapsids in Abdala et al. (2008), Spindler et al. (2015), and Angielczyk and Kammerer (2018) would also be good to cite here.

Line 537: Change to: “...debated (Amson and Laurin, 2011; Spindler, 2020) and beyond the scope of this study.” It would also be good to note and discuss Spindler’s (2014) re-identification of potential therapsid material from the Pennsylvanian.

Line 539: I recommend including some citations for the Roadian first appearance of therapsids.

Line 548: I think it would be good to mention that an apparently slow initial radiation of therapsids stands in contrast to Kemp’s hypothesis of a very rapid therapsid diversification (e.g., Kemp 2006, 2009).

Line 554: change to: “...remained rare at that time.”

Lines 565-569: This paragraph and Figures 6-9 don’t really seem to be fully incorporated into the paper. If you plan to include them in the main text, I think you will need to add some discussion of them in the results and discussion sections of the paper. Alternatively, you could have these figures and the current appendices be supplemental data. The latter option makes more sense to me because I think the current structure of the paper is streamlined and logical, whereas adding in the additional content would make it more complex and harder to follow.


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: DISTRIBUTIONS OF EXTINCTION TIMES FROM FOSSIL AGES AND TREE TOPOLOGIES: THE EXAMPLE OF MID-PERMIAN SYNAPSID EXTINCTIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The text is clear and unambiguous - complex, but professional and thorough.  The literature is very well covered (although they might like to add Wang et al. (2016) (Wang, S. C., Everson, P. J., Zhou, H. J., Park, D., and Chudzicki, D. J. (2016). Adaptive credible intervals on stratigraphic ranges when recovery potential is unknown. Paleobiology 42, 240–25) to their discussion that begins on line 101 – I think it is among the best of the simple Strauss and Sadler-like methods.  The article is well structured and self contained.
Experimental design: The paper represents original research, well-defined, relevant, and meaningful, and its relationship to previous research is particularly well articulated.  The paper is also fully rigorous, performed to an unusually high technical standard.  The methods are well described, with, if anything, too much detail (but what constitutes 'too much' is subjective, and it is better to err on the side of too much rather than too little).
Validity of the findings: The findings appear valid. Simple as that.
Additional comments: The authors have done an outstanding job in dealing with my rather copious comments on an older version of the paper.  The only thing I would say is that I still found the section on the 4 extinction hypotheses hard going.  Maybe right at the outset, just tell us that you are going to start from the oldest to youngest, to give the reader some sort of scaffold to help hold the copious detail, most of which will not be of interest to most readers (unless they are unlucky enough to only have Permian synapsid workers read the paper!).


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: DISTRIBUTIONS OF EXTINCTION TIMES FROM FOSSIL AGES AND TREE TOPOLOGIES: THE EXAMPLE OF MID-PERMIAN SYNAPSID EXTINCTIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: General comments: This is the second time I’ve reviewed this manuscript, and I appreciate the very detailed response to reviewers that the authors provided. They were clearly very conscientious in addressing the issues that were raised in the previous reviews. I feel they have satisfactorily addressed my previous comments. I included a few minor comments and corrections below, but I think the manuscript is basically ready to accept now.

Title: maybe remove ‘some’

Line 33: Kind of a semantic comment, but regularly implies to me an aspect of periodicity, and I’m not sure that’s what you mean to imply here. Maybe it is, given things like the discussion over the years of things like periodicity in mass extinctions, but if it’s not I think ‘frequently’ would be a better choice.

Line 112: change various sizes to differing richnesses; this will prevent readers from mistakenly thinking that you’re talking about scale instead of diversity

Line 114: change to approaches

Figure 1 caption: change green to yellow

Line 203: following reviewer 1’s recommendation to include the code for the analysis in the supplement, you should call out the supplement here (in addition to github).

Line 288: I appreciate you adding the new information about the Viglietti et al. paper. However, it makes the paragraph seem somewhat confusing because you bounce back and forth between talking about the terrestrial extinction being relatively long and relatively short. Maybe start with the ~10 Mya hypothesis (i.e., Erwin, 1990), and then go from there.

Line 503: I think you mean 290.1

line 506: replace is with are

line 507: replace was with were

line 521: may change to ‘...a single relevant taxon...’

Ling 558: change to compute

Line 560: is their a discussion of the full set of methods you used in the supplement? If so, please call that out here (likewise I would recommend adding it if it’s not currently included).

Line 579: change to require

Line 651: I’m not sure what you mean by ‘quite correct’ here. Maybe something like ‘slightly worse’ would be more accurate.

Line 676: I recommend explicitly restating the hypothesis here to remind readers of what it is.

Line 765: capitalize Permo-Carboniferous

Line 810: change to assessing
Experimental design: see above
Validity of the findings: see above
Additional comments: see above


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: PRECLINICAL MODELS OF ACUTE LIVER FAILURE: A COMPREHENSIVE REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Comments to the Author:
This manuscript by Hefler et al. entitled “Preclinical models of acute liver failure - a comprehensive review” comprehensively summarized preclinical animal models of acute liver failure (ALF) induced by surgical, pharmacologic or immunogenic causes. The review is interesting and very informative for the field.
1.	Among surgical, pharmacological or immunogenic approaches to model ALF, which is the most representative of clinical course?
2.	What are the advantages and disadvantages of three categories of models regarding their drug response? Which reflect the response to treatment on clinic?


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: PRECLINICAL MODELS OF ACUTE LIVER FAILURE: A COMPREHENSIVE REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the present Review, the authors discuss the various available preclinical models for studying the acute liver failure disease to better understand the pathophysiology in order to develop more relevant experimental models and therapeutic strategies.
Authors have comprehensively written the review article which is going to be useful for the audience as a single resource rather than pulling out various research articles for studying the experimental models for the disease “Acute liver failure”.
Strengths and drawbacks of every available experimental model has been discussed well.
This field has been reviewed recently and therefore this comprehensive review has a good scope to the research field.
Experimental design: Minor Comments:
1.	Although, the review is written in readable English, throughout the manuscript English needs correction or should be revised.
2.	Throughout the manuscript, text alignment (justified alignment) and inappropriate spacing needs to be correct.
3.	Introduction section requires the reference citations from line 47-56. Citing tables does not qualify for the literature citation, as material explained in the tables have also not been cited in the tables as well.
4.	In Table 1 and Table 2, another column should be made including all the reference citations (all research articles and review articles reviewed to collect the information presented in the tables). Just a suggestion to simplify, may be PMIDs can be given as a separate column.
5.	Line number 74-75, rephrase the sentence, “as previously doing well patient without preexisting liver disease”. (Patient is a term used for a person receiving medical care, so a patient is not well anyways).
6.	Line 76-77 reference citation is missing.
7.	Line 78-84 reference citation is missing.
8.	Line number 85, add “is” after the word council.
9.	Line number 131, its hepatotoxicity not hepatoxicity. Please correct that.
10.	D-Gal or d-Gal, it has to be consistent either lowercase or uppercase, throughout the manuscript.
11.	Remove “to” after judge in line number 438.
12.	Line 562, correct spelling of Wistar Rats.
13.	In figure 1, font size of the time points on the arrows should be increased. It is not clearly visible on a print.
14.	Check the font style for the figure legends, it’s not matching with the tables. It should be consistent throughout.
15.	Reference citation, line number 727-732?
16.	Line number 757, I assume, its MHV not MSV. Please correct that.
17.	Line number 796, use abbreviation of IFNAR in brackets, as IFNAR has been used further after this line.
18.	Line number 821, change where to were.
19.	Line number 834, add “to” after compared.
Validity of the findings: "No comment"
Additional comments: No additional comments


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

Input:
Title: PRECLINICAL MODELS OF ACUTE LIVER FAILURE: A COMPREHENSIVE REVIEW
Review round: 1
Reviewer: 3

Output:
Basic reporting: None
Experimental design: None
Validity of the findings: None
Additional comments: This is well-written reviwe paper on the current state of preclinical models of acute liver failure. The authors have studied on the existing literature on the topic extensively and comprehensively and their presentation of the  major fundings in these studies were accurate and clear. key information has been summarized in figures and table in ways that are concise and memorable to the readers. This reviewer finds this paper quite informative and only has the following suggestions to make:

First, the authors may want to add the disadvantages of the Long-Evans model to talbe 1.

Second, the authors may want to add overall mortality for both clinical and preclinical models in figure 1.


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

Input:
Title: CHANGE IN ALCOHOL CONSUMPTION AND PHYSICAL ACTIVITY DURING THE COVID-19 PANDEMIC AMONGST 76 MEDICAL STUDENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Although the authors have tried to present an important topic, there are certain limitations in the study and these need to be improved significantly for submitting in such a reputable journal.

The introduction, methods, results, and discussion sections are too much thin for an original article. Overall, the smaller population size limits the scope of the manuscript to a wider number of readers.
Experimental design: As I have mentioned that  76  is a smaller number, I would suggest later on to circulate the survey to other Finnish universities also to make a  multicenter data presentation. Even in 76 persons, the male-female ratio is not equal. The ethical committee's study approval number has to be mentioned in the methods section. This original primary research doesn't fall within Aims and Scope of the journal.
Validity of the findings: The lower number of participants arise the question of the statistical significance of the study findings and I would recommend increasing the number of participants. It would give a heterogeneous distribution of the participants, even some international students' experience would strengthen the study if available. As I mentioned the limited results and discussion section must be improved. In the later versions please include a section on "Strengths and limitations" of the study.
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: CHANGE IN ALCOHOL CONSUMPTION AND PHYSICAL ACTIVITY DURING THE COVID-19 PANDEMIC AMONGST 76 MEDICAL STUDENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Title of the article is improper as it is mentioned university pre-graduate as target population. Rather it should be mentioned medical students, as there are significance difference between general university pre-graduate and medical students in terms of stress, workload and health awareness level.

2. Your introduction needs more details. At lines 45-63 different studies among students is reported regarding alcohol consumption and physical activity during COVID-19 pandemic, however, other relevant studies among medical students should be reported here additionally.
Experimental design: 1. In the line 67, it is mentioned that this study was a cross-sectional cohort study. It is only a cross-sectional online survey which has to be mentioned instead.

2. Background information( at lines 86-91) which were collected during study have not been reflected in the results related to main outcome variables(alcohol consumption and physical activity).

3. Table-1 lacks the data regarding association between alcohol consumption, physical activity and men and single living arrangements.
Validity of the findings: 1. No data regarding social contacts had been collected in this study, therefore, it is improper to mention in the conclusion (line 156-157) that alcohol consumption is reduced due to reduced social contacts.

2. This study lacks the data which may confound the alcohol consumption and physical activities before and during COVID-19 pandemic.
Additional comments: No comment


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

Input:
Title: THE CARBON AND NITROGEN BUDGET OF DESMOPHYLLUM DIANTHUS—A VORACIOUS COLD-WATER CORAL THRIVING IN AN ACIDIFIED PATAGONIAN FJORD
Review round: 1
Reviewer: 1

Output:
Basic reporting: - This article uses clear and unambiguous, professional English throughout.
- There is sufficient field background/context provided in literature references.
- This article has a  professional article structure, figures, tables. Raw data are shared.
- It is self-contained with relevant results to hypotheses
Experimental design: This article meets the Peer J criterias for publication regarding experimental design, see all comments in Section 4.
Validity of the findings: This article meets the Peer J criterias for publication regarding the validity of the findings, see all comments in Section 4.
Additional comments: In this manuscript, the authors investigate the carbon and nitrogen budget of a solitary cold water coral species living in environments that are usually undersaturated with respect to aragonite. These questions are of general relevance to the marine scientific community, in particular regarding the ability of these organisms to maintain themselves in future acidifying waters. This paper represents an impressive body of work and adds meaningful and needed data to the current literature regarding an azooxanthellate corals C and N metabolism.

- Introduction: The problematic is clearly presented and the introduction contains the background information necessary to understand the rationale for this study. I would however like to see explicit pH and omega values encountered in the fjords these corals live in.

- Material and methods: The methods are a bit difficult to read and follow, however the figures help greatly at understanding the design. I have added a few comments directly in the text regarding that section for things I did not feel were very clear. I think the authors should proofread this part as if they were an external reader that doesn't know this experiment to check that this part is easily understood.

- I did not understand in what the two coral batches were different? Unfortunately, I am not sure I understood if the corals were re-used for different treatments, and if that was the case, how much time there was between these feeding/incubation treatments.

- I think the material and methods would be much easier to read as a whole if there was a starting paragraph on the overall design of the experiment. Something that would go something like:
"To understand our problematic (...) we designed an experiment in two (?) parts. Firstly, we performed a 1-3h feeding experiment where we used a subset of the corals we collected in Huinay fjord and fed them with either live zooplankton collected in the area or live zooplantkon combined with thawed krill (while another subset of corals were incubated without food for comparison). By measuring POC and PON at the start and end of the feeding, we calculated the particulate C and N fluxes. In a second part, we performed 9-11h incubations without food, to calculate respiration and particulate and dissovled C and N fluxes.... " An overview first would really be great before the detailed information. I for example had problems following after how much time the incubations experiments took place after feeding?

- One figure that ties the three Figures 3 together instead would be great. (for example adding arrows from Collection in Figure 2 to Figure 3A annotated with "1 week", and then -- 12-24h --> Figure 3B). This could also use different gray shadowing for different coral batches if necessary...

- It would be good that the explanatory figures are used in the text as many times as necessary to allow the reader to follow the design. For example, Line179 mentions Fig. 3a but I guess this is Figure 3B we should look at? Similar with Line 204.
- In Figure 3B, I would recommend a change from t0 and t1 to h0 and h+2 instead so that it is cleared what the (same with Figure C with h0 and h+10). It also would lift the doubt that t0 of the feeding experiment is the same as t0 of the incubation experiment.

- Line 299-300: Is this true that a good approximation of the O2:C respiration coefficient is =1? Isn't there some metabolic DIC that should be retained for calcification? Or some created by carbonate dissolution? Reading the article cited, it seems to me that the authors should have chosen the night rate of 1.5 instead? (nights are likely more representative of what happens in a coral without photosynthetic symbionths? But not exactly of course since night and day omega conditions aren't similar...). I understand it must be difficult to get a proper respiratory coefficient, however, I think the authors should add a mention that 1) the citation refers to a tropical colonial/symbiothic (?) corals and 2) there is a deviation margin around the 1 (more or less 1) depending on night/day in these and 3) there is a margin of error in these calculations of the C respiration rate, and thus the SfGc is also subject to a margin of error (maybe quantify how much the SfGc would change if they took an alternative plausible scenario of the respiratory coefficient O2:C, maybe it wouldn't change so much if C respiration does not represent a big part of the C uptake?).

- The statistic methods used seem appropriate regarding the design of this experiment.

- Results are well written and the figures presented are of high quality. I have left some small comments directly in the pdf file.

- While Figure 4 was easy to read and follow, the figure 5 was slightly confusing, as it shifts colors from the previous figure (but uses the same data). It would be best if the main blue used for Batch I was the same as the one used for Figure 4 to improve consistency.

- Discussion is well written and informative. I have very little comments on that part, they can be found in the pdf file.


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

Input:
Title: THE CARBON AND NITROGEN BUDGET OF DESMOPHYLLUM DIANTHUS—A VORACIOUS COLD-WATER CORAL THRIVING IN AN ACIDIFIED PATAGONIAN FJORD
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript “The carbon and nitrogen budget of Desmophyllum dianthus – a voracious cold-water coral thriving in an acidified Patagonian fjord” by Sandra Maier, Carin Jantzen, Jürgen Laudien, Vreni Häussermann, Günter Försterra, Astrid Cornils, Jutta Niggemann, Thorsten Dittmar, and Claudio Richter is an excellent, interesting, well performed and well written study determining the C and N budgets for the CWC Desmophyllum dianthus.

I have just three major comments on the experimental design, and a very few minor additional comments, that I hope can help authors to further improve their already very good manuscript.
Experimental design: (1) The study suffers for a lack of proper replication since only two batches were established, one for fed and one for unfed corals. This means that corals inside the same batch were really not as independent as compared to those in the other batch. However, this is a limitation often occurring in experiments, especially when specific conditions need to be maintained (such as for CWC). I do not think this was really affecting the results obtained (it is my personal opinion), but I think authors should at least briefly discuss this point.

(2) It is not fully clear to me if enough time was given to corals to adjust their metabolism to the two different feeding treatments before to measure their C and N budgets. May this explain the reduced respiration in the krill-fed corals? May authors comments on this?

(3) Do authors think bacteria could have played a role in the respiration of particulate and dissolved matter, so reducing the measured outputs? May authors comments on this?
Validity of the findings: no comment
Additional comments: Line 109 I suggest removing “important foundation” from this sentence. The solitary nature of Desmophyllum dianthus allow to create a dense and complex benthic community, however with limited 3D extension (as it can be seen in figure 6). Moreover, is there any evidence that the presence of Desmophyllum dianthus is strictly required for the other species in the benthic community to grow (i.e., is a foundation species)?

Line 137 A density of 2.78 is reported in Movilla et al. 2015. What is the criterium followed to choose one instead of the other?

Lines 1676-168 Was the volume 0.5 or 0.8 L? It is unclear to me.

Line 171-172 Please, specify how was the 1 cm/s flow measured.

Line 225 Should not be 0.45 filters to be used for DIC and DIN?

Line 240 I suggest changing “enumerated” to “counted”.


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: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: In my opinion, it is a very well written,  novel, relevant paper.  Introduction section provides sufficient details although I suggest expanding information on nomogram in the last paragraph, and briefly describe if nomogram has been used for this condition before, if yes, what were the problems? How this study is better?
In discussion section, authors may want to comment on the short median length of follow up, if this is another limitation, also will it be to conduct a prospective study?
Experimental design: This part is also well written, within the aims and scope of this journal. the research question has been clearly defined and its relevant to the field. Methods are robust and meet the ethical standards. Also, there is sufficient detail to replicate the experiments.

I have a minor comment here, would it be possible to elaborate on was there any history of smoking in patients with lung cancer or any other collateral history that may be a risk factor for respective malignancy?
Validity of the findings: The underlying data have been provided, which proves study to be novel, statistically sound, and controlled.
Conclusions address the original research question and support results.
Additional comments: No additional comments


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

Input:
Title: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Recommend hiring an English language service to assist with academic prose. The term "periochia" is not a generally accepted term in the English literature - recommend use of the term "periungual" instead.

Background, structure, raw data, hypotheses are all acceptable.
Experimental design: Research question well defined and investigation performed to technical and ethical standards. Methods sufficiently described.
Validity of the findings: Use of CXR alone may be underdiagnosing ILD in DM patients – could have much higher rates among both cohorts (malignancy-associated and non-malignancy-associated) which could affect model.

Usually build multivariable analysis from univariable analyses where p<0.1 rather than p<0.05; a variable which may not be important in univariable analysis may occasionally become important in multivariable analyses, thus larger p-values than the traditional p<0.05 are typically used. Correcting this in univariable analysis could introduce factors such as sex (as has been found in previous studies) and poikiloderma, both of which have 0.05<p<0.1.
Additional comments: In addition to its current form, would consider an alternative figure/table depicting the points assigned to each criterion in the nomogram, so the point total can be more easily calculated without the need for a straightedge.


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: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have provided answer to my previous question  in a satisfactory manner.
Experimental design: Methods are robust and meet the ethical standards. Also, there is sufficient detail to replicate the experiments. In addition. authors have addressed the issues raised in previous review.
Validity of the findings: The underlying data supports notion that study is novel, statistically sound, and controlled.
Conclusions  support results.
Additional comments: From my perspective, study has been improved  substantially and its suitable 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: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: Recommend English language service for assistance with grammar. There are instances in the introduction (lines 40-42, 52-54, 59-61, 64-68), methods (lines 84-85, 93-94, 104 [the plural of index is indices]), and results (lines 134-135,153-154) that do not use acceptable English grammar.

Added background is appreciated and adds to the manuscript.
Experimental design: Appreciate corrections to statistical modeling methodology.
Validity of the findings: Conclusions are well-stated and supported by statistical analysis.
Additional comments: Appreciate the hard work the authors put into making revisions to this manuscript. However there are a few grammatical issues that should be addressed prior to 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: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 3
Reviewer: 1

Output:
Basic reporting: The current version is a substantially improved version of the original manuscript.
Experimental design: Methods are well reported with sufficient amount of details.
Validity of the findings: All underlying data has been provided and conclusion supports the results.
Additional comments: In my opinion, in the current revised version, a substantial amount of improvement can be noticed.  Authors seems to have work hard to make all the necessary changes. Writing style is much better and it facilitates reading.


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: DEVELOPMENT AND VALIDATION OF A NOMOGRAM RISK PREDICTION MODEL FOR MALIGNANCY IN DERMATOMYOSITIS PATIENTS: A RETROSPECTIVE STUDY
Review round: 3
Reviewer: 2

Output:
Basic reporting: Appreciate use of an English language service and corrections to grammar. No other concerns.
Experimental design: No additional comments
Validity of the findings: No additional comments
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: DINOPHILIFORMIA EARLY NEUROGENESIS SUGGESTS THE EVOLUTION OF CONSERVATIVE NEURAL STRUCTURES ACROSS THE ANNELIDA PHYLOGENETIC TREE
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Basic reporting: The manuscript is devoted to development of the nervous system of tiny dinophilid annelids. The organization and development of the nervous system are traditionally used for reconstruction of phylogeny. Therefore results of this report are important for future comparative analysis.
Experimental design: 2. Experimental design: All experiments are correct and are consistent with methods of immunocytochemistry and confocal laser scanning microscopy.
Validity of the findings: 3. Validity of the findings: All new results are correct and supported by original figures.
Additional comments: 4. General comments:
Authors represent very interesting new results, which are well illustrated. These results are worth to be published. At the same time, the manuscript has to be improved and some corrections are necessary.
Major comments:
I kindly ask authors to discard the misunderstanding concerning one or two pioneer neurons in two different dinophilid species. I also ask authors to explain the term “scaffold”. And the third important note concerns the Figures. The combination of red and green colors in one figure is impoliteness to people who have problems with vision. I recommend authors to avoid such a combination of colors.
I recommend to invite native speaker to edit the English.

Minor comments:
Abstract: Using ICH and LSCM, we revealed that in both species, the first neurons appear at the most anterior and posterior regions of the embryo and revealed positive reaction with anti-alpha-acetylated tubulin antibodies only (no positive signal with anti-serotonin (a5-HT) or antiFMRFamide (aFMRFa) antibodies were detected).
--- I recommend authors to escape the use of unexplained abbreviations and repetitions.
--- Accordingly to text, Dimorphilus gyrociliatus lacks posterior perikarya (perikaryon). Thus, this phrase is incorrect and has to be rewritten.
Abstract: On the contrary, both anterior and posterior early cells in D. gyrociliatus maintain during the whole life, which probably reflects the progenetic trait of this species.
---- It sounds wrong. It means that life reflects progenetic trait. It is incorrect.
---- I did not understand this phrase, because Dimorphilus gyrociliatus lacks posterior perikarya (perikaryon). Thus, it is impossible to maintain both posterior and anterior cells if posterior cells are absent.
Abstract: The nervous system develops in the rostrocaudal direction in both species.
---- This state contradicts the early information in the abstract “Long neurites of early neurons grow towards each other…..”, I did not understand, how posterior neuron is able to give rise to neurites in rostrocaudal direction.
Abstract: Based on our data, we infer how the evolutionary history of dinophilids may have affected the early neurogenesis of these extraordinary animals.
----I recommend authors to briefly describe exactly conclusion instead of this phrase.
Introduction: In polychaetes and nemerteans, pioneer neurons demonstrate a positive reaction to serotonin antibodies (5-HT-IR) (Voronezhskaya and Elekes, 2003; Voronezhskaya and Khabarova, 2003; Voronezhskaya, Tsitrin and Nezlin, 2003; Chernyshev and Magarlamov, 2010; Fischer, Henrich, Arendt, 2010)
---- The citation of this paper (Heibert, Maslakova, 2015: EvoDevo) has to be added
Introduction: The apical organ consists of a group of flask-shaped cells whith short processes reaching surface of epithelium and bearing cilia on their apices.
--- Incorrect word
Introduction: Our results demonstrate that the early neurogenesis is similar in twodinophilid species but significantly different from that of other Lophotrochozoa.
--- I recommend delete this phrase from the Introduction.
Mwthods: ………..with diatom Phaeodactylum sp. and ………….
---- Use Italian
Methods: Both dinophilidspecies laid cocoons regularly.
----- Add space
Methods: ……..and six-well plates at 10°C in filtered seawater…………
--- I did not understand this
Methods: Immunocytochemistry
----Please indicate whether you blocked nonspecific staining. If yes, please describe how you processed
Methods: D. vorticoides at different developmental stages were incubated in 10-5 M 5-HT and 5-HTP (Sigma-Aldrich, USA) for 3 hours.
---Please explain all abbreviations before using.
Results: Line-249 Long processes of these cells construct the scaffold of the definitive nervous system. Line-254-255: As the number of this cell's processes increases, they spread farther and establish the scaffold of the definitive central nervous system.
---- Please delete repetitions.
Results: By the end of the prototroch stage, a pair of additional neurons differentiate at the…….
----Replace to differentiates
Results: Their processes extend along the scaffold formed by the first cell (Fig. 2 b, e). Thus, the entire nervous system's scaffold is built by the processes of the first single cell (Fig 2. b, e, d).
---- I do not see the “scaffold’ in Figures 2b, e, d. What do you mean as “scaffold” ? The same question concerns D. vorticoides
----Point has to be deleted
Discussion: Then establishes the larval nervous system, and after that the definitive nervous system differentiates
---Please check this phrase. It seems to be wrong
Discussion: Our results show that two first cells (the anterior and posterior ones) emerging at the early trochophore stage in two dinophilids (Fig. 9-14)
---- Dimorphilus gyrociliatus lacks posterior perikarya (perikaryon).
Discussion: The first neuron in D. gyrociliatus appears at the early trochophore stage at the anterior extreme of the embryo at the midline above the prototroch and is visualized with anti-tubulin antibodies only. The cell has a short apical neurite and several cilia…..
---This description has to be placed in Results. I recommend to indicate apical neurite and cilia by arrows in the Figure. I did not find any cilia in Figure 2a, b, which is devoted exactly to this neuron.
Discussion: The cell has a short apical neurite and several cilia (Fig. 3, Fig. 8, Fig. 10-13), and thus can be considered a sensory cell…..
--- as?
Conclusion: The early anterior neuron in D. vorticoides is transient, while it is detectable through the whole life in D. gyrociliatus, suggesting a paedomorphic trait of the later.
---This phrase means that only D. gyrociliatus, but not D. vorticoides  has paedomorphic trait. I recommend rephrase.


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: DINOPHILIFORMIA EARLY NEUROGENESIS SUGGESTS THE EVOLUTION OF CONSERVATIVE NEURAL STRUCTURES ACROSS THE ANNELIDA PHYLOGENETIC TREE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript cited above is a through description of the neurogenesis in two dinophilid species, one dimorphic with dwarf males and a monomorphic species: Dimorphilus gyrociliatus, and Dinophilus vorticoides. The study is well done and the authors provide a wealth of new data. On first sight, it appears astonishing to have another paper on these animals since they belong to the best studied within annelids fascinating researchers since their first discovery in the19th Century. There may be several reasons for a still ongoing scientific interest in these animals. One reason might be that one of the species is sexually extreme dimorphic possessing dwarf males, which exhibit an organization very different from that of the females. Other reasons might be that they formerly were regarded to exhibit ancient annelid structures (the Archiannelida concept) and D. gyrociliatus is very easy to culture, has short generation times making the species suitable for various kinds of experiments and last not least the adults are microscopic and can be studied as whole mounts under the microscope. Nevertheless, this study nicely complements our knowledge on early development in these creatures and allows some deductions to annelids and lophotrochozoans in general. The manuscript cites the relevant literature on the topic some minor problems are indicated below. Figures are necessary are well-balanced and well organized. However, I think the English definitely needs some revision by a native speaker.
Experimental design: The experimental design is clear; data are obtained using immune labeling of selected structures and confocal laser scanning microscopy, standard methods to address such scientific problems. However, I think the methods should be described more precisely. E.g., we don’t know the supplier or its place of the biochemicals, especially the antibodies, which might be crucial for repetition. Also giving two references for the protocol may not be the best solution rather than giving incubation times etc. This will not occupy too much space and the reference to previous work may still be justified. Giving the coordinates of the locality like it is done is useless because it is too imprecisely.
Validity of the findings: The title and certain phrases in the abstract and introduction may suggest that the authors doubt the placement of Dinophilidae and suggest some principle results for Lophotrochzoa in general but this leaves the reader somehow disappointed, because no such interpretations are given. In general certain points are just statements and should be explained by adding further information, references etc. This will be specified below.
I have some problems with identifying of the pioneer neurons by staining against acetylated tubulin only: As the authors know tubulin signal mainly comes from the neurites and some spherical staining is usually interpreted as soma without providing a counterstain that a nucleus is involved. As for instance shown in the paper by Kuma et al. (cited in the MS) the area of the nucleus is always recognizable by a spherical region without any immune-signal, which would be another proof for a nucleus. From the figures provided, I cannot follow the authors by their interpretation. They may be correct but evidence should be given by the data shown. Likewise, I cannot follow the author’s interpretation of the fate of the pioneer neurons. The authors provide a relative staging of the development in the two species in order to make the different speed of development comparable. These stages are given more neutral names but later on the author speak about a trochophore stage which is misleading in two points. First, the reader does not exactly know which stage is meant and, second and more importantly, this naming implies that this stage represent s a trochophore larva rather than an embryo, which it is really is since there is no larva (line 455 “is similar in two dinophilid trochophores” “other polychaete larvae”).
The findings should be discussed more properly and especially the paper of Kumar et al (2020) and Meyer and Seaver (2009) should be discussed and compared more carefully in order to determine common traits in annelids. Moreover, other studies used gene expression patterns to identify clearly pioneer neurons rather than by pure tubulin staining. Therefore, the authors should discuss their findings with care since some evidence is not provided. In addition, some findings are not properly documented by the authors; however, I am sure that the authors are able to provide missing evidence by their figures.
Additional comments: 1.	The title should express to which group of lophotrochzoans the animals of the present stud y belong.
2.	In the abstract, the first two sentences say: “Despite the increasing data about neurogenesis in various Lophotrochozoa groups, the basal principles of the organization of their nervous system are still underestimated. Comparative data about the early developmental events from previously neglected taxa, non-model species, and rare groups are necessary to complete our knowledge.” For the abstract this is ok but in the text I am looking for justification for these statements I would like to know why we ned these data; do we have indications that the picture is more diverse than it would appear using only model organisms? Then it should be given.
3.	In the abstract it is said that dinophilids are unique in combining “traits of different Lophotrochozoan taxa”. Without mentioning these traits and taxa this does not tell us much.
4.	ICH and LSCM are not explained, neither in the abstract nor in the main text. I think LSCM means confocal laser scanning microscopy and to my knowledge CLSM is the abbreviation which is in common use.
5.	Reading the introduction leaves somewhat helpless and puzzled. The first paragraphs appear to be rather long but mainly comprise references. The first sentence in lines 48/49 ist followed by more than 10 lines with references validating a mild context: “Over the past decades the research of lophotrochozoan neurogenesis and functions of early larval neurons has made considerable progress.” I wonder whether it might be better to cite a selection of these papers in order to make it readable. Alternatively more information may be provided telling us which refrence refers to which lophotrochzoan group. Moreover, I am not sure whether Struck 2006 and Richter et al. 2010 are cited in the correct context here. The next sentence almost tells us the same and again provides us with numerous references some of which appear for the second time.
6.	Line 62: Polychaeta has been not to represent a taxon and as such the affiliation Polychaeta should be avoided. In case the authors do not agree with this grouping this should be justified and expressed.
7.	In line 88 the authors introduce the apical organ without explaining its context: “The apical organ consists of a group of flask-shaped cells”. Information is lacking what an apical organ is and that it is developed in larvae of lophotrochozoans. Here also information is lacking that the species under study do not have such a larva.
8.	Inline 111/12 the following statemante is given” for example, some structures might be completely lost or highly elaborated.” For me these examples are not given and I have to look for them myself in the literature. I think these should be added.
9.	Line 115ff.: “For example, the nervous system of Phoronida and Brachiopoda demonstrate similarities with deuterostome neural systems (Nielsen, 2002; Nielsen, 2004; Nielsen, 2005; Temereva and Wanninger, 2012), doubting the molecular phylogeny view, which considers phoronids and brachiopods as Protostomia (Nielsen, 2002).” I think phylogenetic analyses of molecular data helped to resolve many open questions in metazoan phylogeny and this sebntences requires a statement what the authors think about this. On the one hand they apply the name Lophotrochozoa which originates from molecular systematics and if they question this they should express and explain this.
10.	Line 127: “…Dinophilidae family (Archiannelida, Polychaeta) …” For many years now most annelid researches follow the hypothesis that a taxon Archiannlida is artificial and does not exist. If the authors want to re-introduce it here, this has to be justified and discussed. Currently there two hypothesis discussed, both of which place this group among typical polychaetes and without other former archiannelids.
11.	Lines 132ff.: “Further investigations confirmed an unusual morphology of dinophilids: they combine characteristics of different lophotrochozoan. For example, they are similar to Polychaeta due to segmented epithelial structures, though have no chaeta [sic: chaetae]; parenchymatous organization and protonephridia make them similar to Platyhelminthes; they utilize gliding ciliary locomotion like mollusks …” This shall explain that dinophilids show traits of other lophotrochzoans. I see it as an assemblage of some outdated statements on invertebrate morphology and phylogeny. For instance, it is known for quite a long time that a number of annelids don’t possess coelomic cavities. Nevertheless their relationship has not been doubted. Moreover if one excepts that Annelids have a biphasic life cycle comprising a planktonic trochophore larva and a benthic adult it is clear that both types of body cavity organization belong to the ground pattern of Annelida: the larva is acoelomate and the adult is coelomate. Since body cavities and nephridia are functionally related to one another protonephridia are to be expected, if there is no coelom and blood vascular system. So this character may also occur in free-living Platyhelminthes, but if a relationship should be exist, the protonephridia of Dinophilidae should show the same apomorphies than those of Platyhelminthes, which is not the case. Ciliary gliding by means of ciliated epithelia is rather common in meiobenthic invertebrates and as such not all a character giving a hint to mollusk similarity. This assemblage looks like creating scientific questions were they don’t exist.
12.	Line 154/5: “immunochemical staining with a pan-neural marker (anti-acetylated α-tubulin antibodies)” I wonder whether the authors are aware of the fact that all stabilized microtubules are stained with this antibody which may be more than nerve cells. This should be mentioned.
13.	Line 164/5: “Water was changed every day to collect all developmental stages of embryos.” For me it is not clear why exchange of water makes sure to collect all embryos. To my knowledge the so called cocoons are laid on the substrate and thus one must either collect the cocoons or the adult animals and put them into fresh vials.
14.	Line 261: “Their processes extend along the scaffold formed by the first cell (Fig. 2 b, e). Thus, the entire nervous system's scaffold is built by the processes of the first single cell (Fig 2. b, e, d). I cannot follow the description here why is it formed by the first cell when it is followed by two additional neurons? Please reword.
15.	Line 278: “pan-neural marker“ this has been mentioned and explained in the introduction but should be mentioned in the M & M section as well to avoid confusion.
16.	Line 282: “however, no neurons are detectable in the neuropil region …” Why do you use “however”? With some basic knowledge in annelid neuroanatomy you should know that neuropil and somata are always separated – if not the nervous system is medullary (see Richter et al. 2010!!).
17.	Line 286: “In the caudal region, …” I think one should use morphological terms properly. To my knowledge, Dinophilidae do not possess a cauda rather than any tagmata. Strictly speaking, it is the locomotory organ of chordate and especially a primary aquatic vertebrate. So please use anterior or posterior, for instance. Likewise “head” may be better replaced by “prostomium”.
18.	Line 298: “…and bearing a tuft of cilia … “ I could not see the cilia, please provide a figure.
19.	Line 300/01: “The neuropile becomes larger; it is constituted by the neural processes only …” Again neuropil means that it only comprises neurites and synapses so the second part of the sentence is superfluous.
20.	Line 308/9: “These neurons do not have cilia (Fig. 3 k).” Why should they have cilia?
21.	Discussion, first paragraph: This si a repetition of the results and contains only extremely generalized statements which do not help to learn something new. This paragraph should be rewritten.
22.	Line 439: Did Purschke (2005) show the nervous system of Dinophilidae in that paper?
23.	Line 447ff.: “Therefore, the main differences between neurogeneses [sic: neurogenesis] in dinophilids and other lophotrochozoans lie at the very early events of neural development: appearance of pioneer neurons, which do not contain5HT and FMRFamide and in case of D. gyrociliatus are not transient (see below).” Some sentences above the authors say that this has also been observed in another annelid (Malacoceros). Is Malacoceros not an annelid and a lophotrochozoan? And Dinophilus? What are other lophotrochozoans? So, you have found a character common for Annelida which by the way are representatives of Lophotrochozoa. Where is the problem?
24.	Line 475: “.he cell has a short apical neurite and several cilia (Fig. 3, Fig. 8, Fig. 10-13), …” Ok but I failed to find the cilia on the figures cited.
25.	Reference 53 should not be in revision any more, please provide current data.
26.	References in the text should be given without initials of authors (e.g. line 90/91)
27.	Reference Hessling and westheid should read Hessling and Westheide (Line 126)
28.	Line 132: I doubt whether Richter et al is cited correctly here;, please check.
29.	Line 157 space missing: “twodinophilid”
30.	Line 172: “Phaeodactylum” in italics
31.	Line 175: space missing “dinophilidspecies“
32.	Line 228: typo: „mouse“
33.	Line 379: typo: “Paulat” should be “Paululat”
34.	The list of reference should be reworked thoroughly, species names are frequently not in italics and there are several typos; e.g.: line 588 “gastropodIlyanassa obsolete (space missing, no italics).


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: DINOPHILIFORMIA EARLY NEUROGENESIS SUGGESTS THE EVOLUTION OF CONSERVATIVE NEURAL STRUCTURES ACROSS THE ANNELIDA PHYLOGENETIC TREE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is considerably improved and is about ready for publication. Authors have processed all my comments and corrected the text and figures.
Experimental design: Experimental design is correct
Validity of the findings: Findings are interesting and valid.
Additional comments: Although the paper is greatly improved, I strongly recommend to make the figure legends more friendly for reader. In general, the figure with legend should be absolutely self-sufficient. Thus, I recommend authors to use full name of all species, which are mentioned in the figure legend. The full manes should be used at least in the title of the figure legend.
There are some typos in the text and figure legends. For example, Figure 14 "Phylogeny is base on....". I recommend authors to reread the text and correct the typos.


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: DINOPHILIFORMIA EARLY NEUROGENESIS SUGGESTS THE EVOLUTION OF CONSERVATIVE NEURAL STRUCTURES ACROSS THE ANNELIDA PHYLOGENETIC TREE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The MS under consideration is the reviesed version of a previous manuscript. Both reviewer raised a number of points which have been adressed by the authors.
My focus was on those points raised by me (reviewer #2).
Since the general evaluation of the mansucript was positive in spite of several points for improvement, I don't want to repeat the everything of this first evaluation.
Experimental design: The points raised for the experimental design have been sufficiently addressed.
Validity of the findings: The points raised in this part  have been sufficiently addressed by the authors as well.
Additional comments: I don't see any points for further revsion.


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 SHORT SCALE FOR MEASURING ATTITUDES TOWARDS THE DOCTOR-PATIENT RELATIONSHIP: PSYCHOMETRIC PROPERTIES AND MEASUREMENT INVARIANCE OF THE GERMAN PATIENT-PRACTITIONER-ORIENTATION SCALE (PPOS-D6)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Literature reference (line 100 ..): Please add reference to the  seminal contributio of Meredith (e.g., 1993)
Meredith, W. (1993). Measurement invariance, factor analysis and factorial invariance. Psychometrika, 58, 525-543.

Literature reference (line 110): Partial scalar is not a level of invariance per se. You may have partial metric, partial scalar, or partial strict. Please add strict invariance. Please add a short paragraph explaining what is the meaning of invariance testing and what are the allowed across-groups comparisons according to the different invariance levels reached.
Experimental design: Research question: It is not clear to me why medical experience would moderate Patient-Practitioner orientation. Please elaborate more on this and give a better rationale for why medical experience is a moderator.
Validity of the findings: Testing for partial scalar invariance (lines 213-220): It is not clear to me what you did. Once you established that delta-chi or delta-cfi evidenced a worsening of fit, please check for significant Modification Indices (MI) associated to each of the constrained intercept. Signigicant MI give evidence of non-tenable constraint. Then you have to relax the non-tenable constraints at once, untile the remaining constraints are all tenable. Please better clarify the approach you followed

Comparisons of observed total scores across medical experience: Partial scalar invariance allows for comparison of latent means. In order to compare observed means through a statistical test like you did you have to provide evidence of at list partial strict invariance, that implies testing equality of residual variances (DeShon, 2004, Psychology Science, Volume 46, 2004 (1), p. 137-149). If residual variances are difference, you may different variability in scale variance across groups and this may influence the results of the t-test.

Gender comparisons (lines 223-224): Why doing gender comparison when you did  not test for gender invariance ? Following your premises you have to test to gender scalar invariance before doing this comparison. Anyway, the same reasoning I did for comparison of observed total scores related to medical experience applies here: so, provide evidence of at least partial strict invariance across gender before comparing males and females. If strict invariance does not hold, then provide evidence of scalar invariance but compare latent means.
Additional comments: The paper is well written but presents relevant flaws in the data analytical approach. There are also imporant references to the literature that are lacking.
I suggest the authors to better clarify the rational of the study, and in particular why medical expertise is relevant as far as the difference in PPOS psychometric properties.