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Re: Stratigraphy, biogeography & cladograms



Here's a reply to a couple of posts.  




John V Jackson wrote:
> 

> 
> Modern insects and birds are not a good analogy for this reason:  early
> flightless dino/birds went from one form to another and then back to the
> earlier one:
>     flightless -> flying -> flightless
> 
> modern flightless birds and insects effectively just do this:
>     flying -> flightless


> 
> The confusion in early birds/dinos is between the first and the second
> flightless stages, and since the time difference might be
> 10mys..5mys...0.1mys, little divergence need have arisen.  In modern
> birds/insects, the comparisons would have to be between flightless forms all
> to the right of the arrow.  We seldom confuse such groups since, in the case
> of birds at least, they split say 60-80 mys ago.


You seem to be saying that living birds are diverged enough to avoid
what is implicitly a long-branch problem that might arise in nonavian
theropods.  This is actually very unlikely, as a long-branch problem is
much, much likelier when lineages are long separate.  Several simulation
studies show this, and I would expect that the changes seen in
flightless birds would be much more dramatic, since they're more
derived, than in barely-derived nonavians.

Aside from that there are ways of quantitatively testing your
assertion.  Compare your preferred nonavian phylogeny with those
recovered by someone else - Tom, Chiappe, Sereno, Forster, anyone. 
Since you're dealing with discrete character data in a parsimony
environment, apply the Wilcoxon signed-rank test first used in this
context by Templeton, and now lovingly referred by systematists
everywhere as the "Templeton test," to your comparisons.  This would
tell you whether your tree is *significantly* longer or not.  If not,
you'd have a good case that your alternative topology (i.e. one in which
secondary flightlessness arose among nonavians) is not significantly
longer than the set of MPTs and should be considered alongside them. 
The best reference on these kinds of comparisons is this:

Larson, A. 1994.  The comparison of morphological and molecular data in
phylogenetic systematics.  pp. 371-390 in B. Schierwater, B. Streit,
G.P. Wagner and R. DeSalle (ed.), Molecular Ecology and Evolution: 
Approaches and Applications, Birkhduser Verlag, Basel, Switzerland. 

It was written from a neontological perspective, but his approach is
valid regardless of the kind of comparison being made, and it should be
required reading for all systematists.  

Another means was published in Syst. Biol.'s most recent issue, and
though I have some real reservations about its taxon-sampling
sensitivity, it does seem to tease out secondary signals - and if you're
saying that current parsimony analyses are being misled by convergence,
then surely a real phylogenetic signal lurks underneat it.  Trueman's
short paper argues that one can delete NONhomoplastic characters from
the analysis, rerun it, and see what secondary signal emerges. It's
entirely possible that this secondary signal is the real phylogeny. 
Don't forget to test for internal robustness.


Yet another way of testing your hypothesis - identify those characters
you think are correlated with secondary flightlessness, delete or
downweight them, and rerun the parsimony analysis.  This is similar to
the reversed successive weighting test described above.  If  you get a
different tree, you may have something.  

There are all sorts of ways to test your idea without abandoning modern
phylogenetics.



> 
> However, if we did - how would we know?  (Especially if we are placing most
> of our trust in one method.) 

Well, we're not, at least not those of us who consider multiple data
sets. But that's another matter.



 When a cladistics result is obviously wrong,
> people usually aren't keen to publish it - especially if the problem can be
> solved
> by adjusting the input data. 

I seriously disagree with this.  Try reading some of the molecular
journals some time.  Are you familiar with the "guinea pig" problem? 
Not that bizarre trees don't show up in the morphological literature as
well, mind you - but I've seen some genuinely amusing molecular trees.


And what do you mean by "adjusting the input data?"  Most of the time, a
wierd result goes away if problems of character or taxon sampling are
dealt with - this is different from applying some sort of differential
weight within an existing data set, or plucking out a problematical
taxon, or a posteriori recoding when a taxon doesn't behave. 




 And when it's actually wrong but there is no
> way of telling for sure - well, that can't be used as an example of a
> mistake either.
> 
> >  Otherwise your claim is extraordinarily weak, and it just sounds
> >like your upset because no current analysis of theropods favors your
> >particular phylogeny.
> 
> No analysis based solely on current cladistic methods, maybe.  But why
> concentrate on that and throw everything else out the window?  Stratigraphy
> of course doesn't offer fine resolution, but it tells a story with a
> different drift, as does much of the circumstantial evidence.


I liked Tom's critique of stratigraphic evidence, but would add another
criticism - stratigraphy and biogeography are not heritable.  Parsimony
analyses, whether based on morphology, molecules, or behavior,
explicitly assume that the characters under study are heritable.  (And
yes, there are potential problems with this, such as phenotypic
plasticity.  With living groups, we can test heritability; with fossils,
our confidence that we're not seeing something pathological increases
with histological examination or the collection of a population.)  This
is why we can never, ever, combine stratigraphic and character
information in a single matrix, and why stratocladistics has serious
problems.

On the other hand, I do agree that stratigraphy and biogeography should,
at some level, preserve a phylogenetic signal, and that they can be used
as external comparative criteria.  But for stratigraphy to be used, we
must try one of two things:  either calculate error margins on the
ranges of our taxa (and for dinosaurs, a great many species are known
from a single occurrence and will have infinite error margins - hence,
we will be unable to reject any hypothesis on stratigraphic grounds) or
calculate tree-wide comparative metrics, such as SCI, SMIG, or MSM. 
Mark Norell and I did this at SVP, and as it turns out, moving birds
outside of Theropoda usually makes these stats worse.  

What it all boils down to - what you're not allowed to do is simply say,
"I don't like your tree," and leave it at that.  You have to specify and
*quantify* the source of not liking it, and as listed above, the current
literature provides you with a fairly diverse toolbox to use against us.


[shortened]
> 
> However, neither BAMM nor 2F has yet been disproved. 

Birds, pterosaurs, and bats springing from dragonflies hasn't been
disproved, either.  I wouldn't be surprised if some gene out there
supports it when aligned just right.  But I consider it highly unlikely,
based on the common signal extracted from all available information. 
Ditto for the others.




 With regard to levels
> of "proof" for circumstantially supported theories, the evidence need only
> differ by the estimation of a hair in a person's mind for them to support
> one side or the other.


Not in modern phylogenetics.  Really.  Have a look at the literature on
internal global support to see how carefully most systematists qualify
their trees and go out of their way to consider alternatives.


[shortened - here's another post]




> > I hope we can take it that the points dealing with the unacceptability of
> > dependent characters, the value of circumstantial evidence, and Peter W's
> > view that "parsimony often underestimates actual evolution" are valid, and
> > that 2F can now be accepted.

Uh --- no. 

First - I think you're confusing character correlation and character
dependence.  Two characters can be correlated (and even causally linked
in a functional sense), and yet still be treated as phylogenetically
independent.  They need only arise on different nodes.

Which leads us to the concept of testing the hypothesis that characters
are dependent.  We can test character correlations on a tree very
simply, both for continuous and discrete data.  Lots of papers out there
on this - again, the most recent Syst Biol. has an article on it.  

(You may get the impression I'm pushing Syst Bio on everyone.  I'm not
on the editorial board or everything, but I do think that every
paleontologist interested in phylogeny reconstruction should subscribe. 
I  think more paleontologists should submit papers to it.  It's also a
heck of a lot cheaper than JVP.  You can visit SSB and join at
http://www.utexas.edu/ftp/depts/systbiol/).


About Peter Wagner's points - although I agree, in principle, that
parsimony can underestimate real change, one has to understand that Pete
is approaching the issue as an expert on Paleozoic gastropods - taxa
with very few characters and lots of time with which to evolve and
reevolve them.  He and I have discussed several times the differences
between those who work with simple organisms and those who work on the
complex - and I'm not convinced that the "character saturation"
phenomenon he's recovering is not a sampling issue driven by observer
bias and the nonrandom selection of hard-part-based matrices.  Moreover,
several studies have shown that simple levels of homoplasy are tightly
linked with data set size, and the amount of homoplasy by itself is a
very poor indicator of reliability between data sets.


That aside, some of Pete's work on likelihood-based approaches to
stratigraphy in phylogenetics are a promising start, as are those by
Huelsenbeck and Rannala, though I am extremely skeptical of their
applicability to vertebrate studies because the fossil record is simply
not dense enough, and we cannot adequately model the sampling.

chris