This manuscript addresses a very important question about mandibular development in rodents, and one that would be of interest to many groups of researchers. However, at the moment, I have significant concerns about several aspects of the manuscript that preclude me recommending it for publication in its current form:

1. My biggest concern is that you have reduced mandibular development to a single linear trajectory running between a juvenile of unspecified developmental stage and the adult. It is clear from Swiderski & Zelditch (2013) amongst others, that mandibular morphological development in mice at the very least (but likely in other rodents as well) follows a highly complex non-linear trajectory. So, you could produce a very large variation in linear developmental trajectory simply by choosing juveniles of different ages. This is of enormous significance in your analysis because many of your species are represented by a single juvenile specimen. I fail to see how you can have any confidence in the orientation of your trajectories at all. This affects all other parts of the analysis and discussion and is thus a major flaw in the study.

2. Related to the above point, you don’t seem to have taken into account the impact of body size in your analysis at all. Your hystricomorph specimens are all much larger species than your myomorph specimens. Therefore, I wonder if you are likely to find a wider age range of juvenile hystricomorphs in museum specimens, simply because the individual animals are larger and easier to collect. This could lead to the greater variation in trajectories in hystricomorphs compared to myomorphs.

3. There is a tendency to over extrapolate the results and their interpretation. You frequently describe the results as showing that myomorphs do this and hystricomorphs do that (e.g. line 428). Given your very small sample relative to the number of species in these groups, you simply can’t make those claims. Your myomorph sample includes 2 of the 6 muroid families and completely excludes the Dipodoidea. Your hystricomorph sample includes 6 families, but excludes the Ctenodactyloidea and, as mentioned above, is focused on large members of the group.

4. Similarly you often make claims for other papers that are extrapolations of what they actually say by conflating group members with whole groups. For example, line 183 – the Zelditch et al paper doesn’t make any claims for Sciuromorpha as a whole, it is a study on squirrels (Sciuridae) – and line 186 – the papers by Fabre et al and Steppan and Schenk do not state that divergence times in Myomorpha are short, they state this for Muroidea (and I think Fabre et al show that the Dipodoidea have much longer divergence times).

5. In terms of nomenclature, I think you need to be a bit clearer. On line 56 you state ‘The intricate interconnection between mandible and muscle anatomy is used to classify rodents into three main suborders’. This is not true and only one of the four references cited here actually supports this claim (Simpson, 1945). The muscle anatomy was originally used to classify rodents, but it has been clear for a long time now that the muscle morphotypes do not correspond with rodent phylogeny. Thus the clades ‘Sciuromorpha’, ‘Myomorpha’ and ‘Hystricomorpha’ do not align with muscle architecture, and the anatomical conditions of ‘sciuromorphy’, ‘myomorphy’ and ‘hystricomorphy’ are distributed across these three clades. (I have argued that we should stop using these terms as clade names but I appear to be fighting a losing battle). For example, in your dataset you have Muscardinus in the Sciuromorpha, but in terms of its anatomy it is myomorphic. Chapter 10 in the Cox & Hautier book that you cite explains this in more detail.

In terms of your manuscript, you don’t need to change the clade names that you’ve used, but be aware of the distinction and avoid sentences like line 56 which imply the anatomy and taxonomy are consistent. Also, it was never the interconnection between the muscles and the mandible that was used for classification, it was how the muscles attach to the cranium.

1. In the following sentence, Renaud et al 2007 doesn’t support the claim that the ‘mandible presents a wide variety of forms across these suborders’. That study only considers muroids, so it can’t possibly say anything about the suborders. A more relevant reference would be Hautier et al (2011; PLoS ONE 6: e18698). If you read this paper, you’ll also see that there was a second, competing method of classifying rodents (also flawed), based on the mandible, which is obviously relevant to your study here. This was the work of Tullberg (1899) who split rodents into Hystricognathi and Sciurognathi based on the shape of the mandible. Sciurognathi is now thought to be paraphyletic, but the morphological differentiation between these two groups may explain why you have found your sciuromorphs and myomorphs grouped together on one side of the morphospace – they represent the sciurognathic taxa in your analysis.

2. I’m confused about the status of the Sciuromorpha in your analysis. You state on line 164 that lagomorph and sciuromorph species were ‘aligned only as supplementary data’. However, sciuromorphs are then discussed and form part of figures 6 and 8. Are they relevant or not here?

3. Your landmark set seems rather focused on the posterior part of the mandible, and I don’t think it’s adequate for some of the claims you’re making. In particular, there are a few references to enlargement of the masseteric fossa during development. However, you don’t have any landmarks on the fossa, so you can’t possibly know how it changes. I think you’ve inferred it from the surface warps, but that’s based on extrapolation and not robust in the slightest.

4. On a more minor note, I found it quite difficult to interpret the coloured deformation pictures and think I would have found it easier to see the shape changes if you had presented a mean juvenile mandible next to a mean adult.

Philip Cox
University of York

I thank the authors for having taken the time to attend my comments on the original version of this manuscript. On the whole, I am satisfied with the changes they have made. There are just a couple of outstanding issues – these can be resolved with just a bit more clarity in the text and do not necessitate any further analyses.

I appreciate the extra detail the authors have provided around the age of the juvenile specimens and I can see that the trajectory analyses are more robust than I originally thought. However, I think this requires explaining in greater detail in the methods:

1. I think you should note that the Myomorpha juveniles were sampled at 7 days old. You say this in the author responses, but not the paper itself.
2. Can you be clearer about the aging of the juvenile museum specimens? Your criteria are “molar and incisor eruptions” – which teeth were erupted? All of them? – and “ossification of the skull” – do you mean complete ossification of the cranium? Are these criteria also seen in the 7 day old Myomorpha?
3. Whilst I appreciate the extra analyses you have undertaken using subadult Myomorpha, I think you ignore the results of those analyses somewhat. On line 361, you suggest that the impact of non-linear post-natal trajectories has “negligable effect here (Table S2)”. I beg to differ – the change in angle (theta) is between 4.9 and 18 degrees. 18 degrees seems like quite a big change to me. I think you need to explain in much more detail why this is not a concern for your analysis.
4. I still think the non-linear trajectories could be affecting your results, specifically your claim that Myomorpha largely follow a common post-natal trajectory whereas Hystricomorpha are more genus-specific in this regard. It is certainly possible that this is true. However, all your Myomorpha juveniles were of known age (7 days old) and you also had several specimens of each. The Hystricomorpha juveniles came from museum specimens and, understandably, you only have 1 or 2 specimens of each. Even with your careful assessment of dental eruption and ossification status, there is a much greater potential for variation in post-natal age in the hystricomorphs than there is in the myomorphs. I would like you to at least acknowledge that possibility in the discussion.

I hope my comments should be fairly straightforward to deal with.

Philip Cox
University of York