Most people who have commented on the blog about Nicholson et al. 2012 have focused on whether is it really necessary to name all these inferred clades as genera. I agree with those who state it is completely unnecessary and disruptive, and that there are alternative ways (e.g., assigning names to relevant clades independent of the genus rank) to describe the diversity of Anolis. That said, I would like to direct the discussion towards the methodology used. Yes, there are a lot of missing ND2 data in their dataset (e.g., all of the new data presented in Castañeda and de Queiroz 2011 is missing), but I think it is more relevant to consider how they treated the data they did include. First, the molecular partition of their DNA: the protein coding gene ND2 was not partitioned into codon positions, which has been shown to be the best strategy (e.g., Schulte and de Queiroz, 2008; Torres-Carvajal and de Queiroz, 2009; Castañeda and de Queiroz, 2011), and instead, they chose to set a different partition for each of the tRNAs included (five) and one more for the origin for the light strand replication piece (which is ~30 bases long). As the Bayesian analysis requires a large-enough number of characters to estimate the parameter values for the model selected, I thought it was recommended to have partitions of more than ~300 bases (and I can’t think from the top of my head for a specific citation here). Neither the OL nor any of the tRNAs is close to this size (and the AICc, the corrected Akaike Information Criterion, intended for small sample sizes should have been used to select the best fitting model here instead of the regular AIC).(For more on partition selection and consequences of under– or overparameterization, check Brown and Lemmon, 2007 and Li et al. 2007). This should raise an eyebrow about the thoroughness of the analyses. However, in reality, I think this would have little effect on the actual phylogeny. Those clades that are strongly supported would be robust enough to withstand model and partition misspecifications.
On the other hand, the treatment of the morphological characters might have more serious effects on the resulting topology. Nicholson et al. explain that they used Poe’s 2004 morphological data as is, but without the complex coding system he used for continuous and polymorphic characters, and instead considering all possible characters to be equally weighted. (To be fair, Poe did use equal weighting for characters in his analyses; the cost of changes between states within a single character is what is different). Poe coded continuous characters using a gap-weighting method, which divides the range of a continuous character into discrete segments, maintaining information on the order of the character states and the magnitude of the difference between them, and he coded polymorphic characters using a frequency method, which keeps track of the fraction of individuals within the sample that shows a given state. From what I understood, Nicholson et al. considered all changes to be of equal cost, so transitioning from the smallest head to the largest head, or from having all individuals showing condition x to all individuals showing condition y (where some taxa exhibit both conditions), will cost 26 steps, which is the cost of changing from state a to state z (as recognized by Poe). This means, in the combined parsimony analysis, a transition between the two extreme states in a continuous or polymorphic morphological character is equivalent to [single] DNA substitutions at 26 different positions [characters]. Moreover, changes in those morphological characters that were not continuous or polymorphic would cost only a few steps. This weighting scheme (in the parsimony context) will actually give a higher weight to some morphological characters, which is exactly the opposite of what the authors were aiming for (i.e., equal weights). The effects of this unbalanced weighting on the resulting topology? Not sure, but I’m going to guess not insignificant!
One last thing. Several of their proposed genera (Dactyloa, Deiroptyx, Chamaelinorops and Xiphosurus) are not monophyletic on their combined data tree, the one that supposedly serves as the basis for their taxonomy…
KIRSTEN E. NICHOLSON, BRIAN I. CROTHER, CRAIG GUYER & JAY M. SAVAGE (2012). It is time for a new classification of anoles (Squamata: Dactyloidae) Zootaxa, 3477, 1-108
- More On Nicholson et al. 2012: Let’s Look At Their Methodology - September 20, 2012
Skip Lazell
Wonderful! Thank you so much!
Kirsten Nicholson
The analyses we conducted in this paper served several purposes and showed results of analyzing data alternatively to how they had been previously analyzed. Nevertheless what we showed and wrote about in the paper is what amounts to a REVIEW of all the anole literature which shows that the same, large clades come out again and again and in our analyses, like others, those clades are solid and well supported. Also, I keep hearing again and again from folks that say that some or many of our genera are not monophyletic. All of them are monophyletic and if you read the paper, there are a very few taxa that are not stable, and we discuss these in detail in the text of our paper and how we decided to treat them (so just looking at figures is not enough). Thus, it requires a reading of the text combined with the figures and the appendices to actually understand the classification we are proposing.