Disclaimer: Apparently Carlsberg don’t write my titles..
Back in May 2011, a study was published in Science describing the application of sclerotic ring and orbital morphology in determining daily activity (diel) patterns in extinct archosaurs. Recently, a comment and counter-comment have been published, both with pretty critical rhetoric. I figured that as it appears to be causing a fuss, I’d try and summarise the discussion, and add a few comments here (you know, for the masses of people that read this blog..)
The initial study provides “concrete evidence” of Mesozoic “temporal niche partitioning”, a pretty important find, if indeed valid. Combined with data from extant analogues, the authors infer that the visual ecology of Mesozoic archosaurs was a critical driver in the evolution of diel activity patterns.
Now, seeing as the geological record doesn’t really go down to intra-daily resolution, to infer short-term ecological patterns in extinct archosaurs, we must rely on extrapolating signals from modern analogues, formally known as the ‘extant phylogenetic bracket’ approach. This has been used successfully in many aspects of palaeobiology, ranging from sauropodomorph feeding styles to flight evolution in avian theropods, and is an increasingly useful concept in reconstructing extinct ecological parameters based on the intrinsic link between form and function. This concept is rigorously applied by Schmitz and Motani (2011a) on a range of extinct archosaurs to track the link between orbital and scleral form, and visual function.
The basis of this study relies on the fact that in extant amniotes (avians, squamates and mammals), sclerotic and orbital morphology is adequate to discriminate between various functional guilds pertaining to diel activity patterns. Proxies used to describe total morphology are orbital length and the diameter of scleral ring. This is my first issue – based on these proxies, it becomes an assessment of size-function, not form-function (form is the total dimensionality resulting from size and shape). Given the fact that these are relatively simple shapes (ellipses, in two dimensions), it would not have been difficult to use a simple semi-landmark outline profile as a faithful basis for reconstruction, and then run the subsequent discriminant analyses with these data (i.e., a geometric morphometric approach). This would be much more informative in terms of the overall geometry of both the orbit and sclerotic ring.
As in all studies of functional ecomorphology, the ability to distinguish between genuine functional signals, and morphological similarity due to relatedness from common ancestry (i.e., phylogenetic covariance) is critical. The authors state that they compensate for this second factor using a time-calibrated phylogeny. This is fine, as the proxy they use for branch lengths (i.e., chronostratigraphic time) is currently almost the only metric for estimating phylogenetic distance, until someone formally publishes a phylogeny of extinct amniotes using, for example Bayesian methods (which provides estimations of phylogenetic distance), and including all of the species mentioned in the study. Thumbs up.
The only thing I really HATED about this study, is the following assertion: “Ecological niches previously occupied by non-avian dinosaurs are now filled by mammals”. Now, take the following definition of the ‘ecological niche’ from Wikipedia, “the relational position of a species…in its ecosystem to each other”. This implies that the ‘ecological niche’ is a relative spatio-temporal concept, and is firstly, flexible as a lineage develops, and secondly not something that can simply be switched between lineages, especially those as temporally disparate as extant mammals and extinct Mesozoic archosaurs.
Most of the rest of the article is taken up by describing similarities and differences between the extant and extinct species analysed, a summary of which is not required here. It is however, worth mentioning the other ecological parameters which the authors touch on, such as foraging time and metabolic rates. This is a nice touch, discussing how diel activity is a critical factor in assessing overall energy budgets in extinct archosaurs.
Ok, so on to the first response, or ‘technical comment’. This is mainly a critique of the novel discrimination method employed by Schmitz and Motani (2011a), with additional comments on the data and interpretation of the results. Hall et al. (2011) use the same data as the original study, and conduct a simpler method of analysis (a linear discriminant function analysis), which, actually doesn’t make a lot of sense. In the supplementary material provided with original study, all of the code is provided for meta-analysis or replication of the study, and was written explicitly for the data set used. So why not use it? The results of their analysis revealed a lot of ambiguity, with a lot of organisms (up to 80% in one group) being incorrectly classified within their a priori assigned groups. A total of 21% of the species were “misclassified” by the model employed. This is fair enough, but doesn’t really make sense when the method of analysis is effectively a simpler and less appropriate one than the one which is being questioned.
The second major point the authors make is that the theoretical and empirical basis is flawed, due to the assumption that “Mesozoic amniote activity patterns should conform to those of extant amniotes”, and due to the nature of taxon sampling “cannot be construed to represent a typical Mesozoic world and cannot be apportioned based on modern taxa”. Firstly, this second point is irrelevant, as it is the fact that the taxa used contain the relevant morphological structures that is of concern, not whether or not they represent a contiguous sample. Secondly, they question the use of extant analogues to infer ecological conditions in the past. Why not just say that the whole concept of comparative anatomy between extinct and extant organisms is flawed? They basically imply that the entire phylogenetic extant bracket approach is inappropriate here, as amniotes might not be comparable through time. This is not only a ridiculous statement to make (it’s employed in hundreds or thousands of other studies rather successfully), and again is irrelevant – the point is that the orbit and sclerotic rings are still present (and homologous) in all specimens analysed, and that its function is well understood.
Irrespective of these errors mentioned above, the article does have a couple of redeeming points. They concur with my earlier point that orbital diameter is a poor proxy (for axial eye diameter), due to the non-spherical nature of the structure, but fail to mention an alternative as suggested above. Secondly, they correctly point out that in the discriminant function ordination (in the supplementary data), many of the extinct organisms analysed fall outside the groupings in discriminant space (not “morphospace” as used), and thus may not be analogous in terms of activity patterns. Most of these species are actually the herbivorous archosaurs (such as ornithischians and non-theropod saurischians), which is an interesting point in itself. There may also a second meaning, that these exclusive species may represent more complex morphologies than any extant amniote, and are possibly more ecologically advanced. Maybe.
The counter-response (Schmitz and Motani, 2011b) offers no compromise in terms of what Hall et al. (2011) claim about the initial study. The authors respond with a rather messy discussion of discriminant analysis. They fail to mention what is probably the most important point however, in that group classification is assigned a priori to analysis, and it is this which controls the group dispersion structures. The various statistics mentioned simply measure the probability (or likelihood) of whether these group distributions are random or if there is some extrinsic underlying control. However, I have personally never conducted a discriminant analysis including prior probabilities, so cannot confidently comment further.
The authors respond to Hall et al. (2011)’s criticisms of the theoretical basis, by re-iterating that the concept of uniformitarianism is a sound logic for extrapolating ecological factors in extinct organisms. They then become a little hypocritical, stating that it is logical for themselves to use prior probabilities as a basis, but not for Hall et al. (2011) as it forces constraints on their analysis.
With regards to the herbivorous archosaurs that plot outside the extant amniote discriminant space (not “morphospace” again), the authors simply state that despite that Mesozoic archosaurs having larger eyes, they were able to be interpreted functionally still. Well, no not really. By definition there is nothing to compare them to. This is a pretty big issue with the main result of the study. I had a similar issue in my recent thesis, regarding comparative ‘traits’ in ornithopods and ruminants; the way to resolve it wasn’t to disregard different discriminant space occupations, but to consider the implications that in the terms of the particular features analysed, there was some temporal discontinuity that represented a distinct change in ecological function.
As the penultimate point, it is worth discussing the final paragraph of the counter-response: “Discriminant analysis of continuous morphological traits with explicit functional relevance provides a testable, quantitative model of ecomorphological inference” (my emphasis). In this context, how much sense does it make to take something that is by definition continuous, and attempt to place boundaries on it, that may or may not represent some functional category. Observe Figure S1 in the supplementary information: given the scatter of data, what is the purpose of trying to recover discrete categories, when clearly none exist? The nature of the data is continuous, therefore let the nature of the data interpretation be continuous. Any threshold designation between putative groupings will be arbitrary, and counter-intuitive. As well as bad practise.
As usual, I’m going to finish on a tangent. A lot of people are currently quite openly and very strongly questioning the relative value of peer-reviewed publication. These articles were all published in Science, which is one of the top journals in terms of impact factor. Now, with this strong discussion that is occurring post-publication, questioning both the theoretical and methodological basis and the strength of the data, what was the point in the pre-publication peer-review stage? Clearly, ‘they’ did not pick up on any of the discrepancies or flaws discussed above, and these were only highlighted once the study reached the attention of the academic public, who can and have contributed meaningfully to the study. Since initial publication, the value of this study has increased through the open critical discussion, not the publishers or the initial reviewers. This is how science should be conducted, and how scientific progression is optimised. Accordingly, it will be interesting to follow the progression of this study in terms of both study and reviewer success.
Merry Christmas in the mean time, and a Happy New Year to all
three of my readers!