Weights

James Francis Lyons-Weiler weiler at ERS.UNR.EDU
Sat Mar 1 11:13:53 CST 1997


Like Tom, I apologize for length.  I'm a worse offender, I'm sure...


Tom D. wrote:
>I ask you to let go, just for a moment, from your seemingly firm belief
that phylogenetics should be viewed from the statistical perspective

        This is very point of contention.  If you ask that I give you the
debate, what's the point?

I could just as easily ask that you let go of your obviously firm belief
that phylogenetics should not be viewed from a statistical perspective.

>Perhaps it is this emphasis on homology which sets off a lot of the
subsequent differences. For me, homology is something which is inferred as
well...

        The debate is not about whether or not homology is  hypothetical.
The debate is whether or not probability plays an implicit role in the
assessment of phylogenetic hypotheses, which include trees and homology;
branch lengths and ancestral character states.  This is the critical point
the debate hinges on:

        If probability plays an implicit role in the assessment of
phylogenetic hypotheses, its role should be made explicit.

        If probability does play an implicit role, it follows that  then
that explicit statements of corroboration in terms of probabilities should
be turned to the task of increasing phylogenetic accuracy.  It is
remarkable to me that the  various camps that persist to this day fail to
see that because they are asking the same questions, there must exist a
common set of assumptions.

 The failure to recognize these assumptions (which include  probability)
does a disservice to the field, and that's when people start talking past
each other.  I have outlined the shared assumptions I managed to
recognize; perhaps there are more. To avoid this, I will address your
concerns in the terms of homology testing.

It seems that for you, evidence is comprised of the set of potential
transformations which are indicated by a data-set, with an accompanying
set of probabilities attached, probabilities calculated in light of trends
you may have discerned in transformations of a similar kind, in other
circumstances. For me, evidence consists of the set of distributions which
i have discovered for character-states determined to be homologous, to the
best of my ability.

        No, for me, the character state distributions that might appear to
be homologous might also NOT be homologous, despite the a priori testing
and the use of parsimony.

I gave a particular example of how, when characters are equally weighted
apparent homology may be wrong, and the equal probabilities about
transformation implied by equally weighting differences would be arbitrary
AND wrong.

>The character then may be seen as evidence to support a phylogenetic
hypothesis grouping the taxa.

        The amount of evidence each character (or state) carries is where
probability first sneaks into parsimony.  The second time is the degree of
support afforded the hypothesis by the characters.  Consider that for
decades people have listed synapomorphies supporting clades as evidence in
favor of that hypothesis (and in disfavor of alternatives, which include
the null that all taxa are equally related).  Why are 2 synapomorphies
more convincing than 1? Why are 100 more convincing than 2?  I would
suggest that an intuitive application of probability has persisted
alongside phylogenetic systematics, but that it has not yet been made
explicit.  The fact that the synapomorphies maybe erroneous because of
systematic error in the processes of data sanitizing is dealt with below.

>proto-hypothesis [on homology] has passed all of our initial testing,
analyzing, poking and kicking, and has survived as a tenable hypothesis,
or it has not. If it fails, it gets tossed.

        On the surface, this appears to be a Popperian approach. A
careful reading of Popper tells us that he considered how a hypothesis
was CONSTRUCTED to be trivial, and that all that matters was how one TESTS
the hypothesis.  Second, Popper took time to reject the Popperian
interpretation of parsimonious phylogenetic inference.  Third, Popperian
tests require making (A) explicit the background knowledge one puts into
an hypothesis, (B) some critical test statement upon which that hypothesis
that may be rejected, and (C) some evidence upon which the test statement
is supported or refuted.  "Unweighted" parsimony hides ignores the fact
that the background knowledge includes different levels of corroboration
for the various hypotheses of homology, and simply squashed them to be
equivalent.  I reject the parsimony criterion as a critical test.  A
Popperian hypothesis is "bold"; it is not expected to survived the
critical test, and it aquires support because it has in fact survived the
test. The test is critical only is it does not rely upon ANY of
the background knowledge; to do otherwise would be INDUCTIVE , not
hypothetico-deductive, and circular.

        The fact that the degree of corroboration can fluctuate as one
examines and re-examines the evidence for homology tells me that an
implicit probabilistic interpretation is present, and that these
probabilities fluctuate between 1 and 0, and if they could be made
explicit (i.e., statistical), then the process  would be better justified.
Simply because adequate statistical probabilistic tests have not yet been
fully developed doesn't mean that probability doesn't play a role, or that
the task is impossible, or not worth pursuing.


        If one has hypotheses of homology (HH) as background knowledge,
and then uses character congruence (CC) on an MP tree as a test, the fact
that the test statement (the tree) is directed entirely by HH makes the
exercise circular.  To then say that the tree is a phylogeny requires an
inductive step.  In that sense, no probabilistic support can ever exist
for hypotheses of phylogeny; this is in keeping with Popper and Miller's
proof that no degree of corroboration is afforded by inductive reasoning.

That does not mean that probabilistic support for hypotheses of homology
are impossible.

>In a sense, we are adopting a far stricter standard than you are, for a
hypothesis (a column of states in a matrix) is only advanced when we are
convinced that it is homologous, rather than assigning weights to evidence
we are, in some sense, not sure of.

        The standard you are referring to is which character are allowed
to interact in a parsimony analyses.  Those that you have rejected as
homologous are weighted "zero".   The debate is not whether or not the
approach of testing hypotheses of homology is better than other
approaches; let's say for arguments' sake that it does take a logical
priority. The debate is whether or not, in the process of becoming
convinced of a hypothesis of homology, probability plays an implicit role.

>The solution is to apply another test, and we have a handy one; one which
follows directly from generally accepted evolutionary principles, and one
which directly addresses the problem of sorting out contradictory grouping
hypotheses. And that is the expectation, based in evolutionary theory,
that true homologies are congruent; given but one history of life, the
history of homologous characters is congruent with the history of taxa.

        Congruent evidence is hardly corroborative; Correlation is a form
of congruence (variable A rises, variable B rises), but mere correlations
are not accepted as critical tests.  The type of congruence that you
accept as a test is not critical; there are no bold statements; nothing
about congruence goes beyond the background knowledge used to construct
the hypotheses of tree and homology; in fact, there are no test statements.
You get a tree length, and some of your HH appear to be synapomorphies.
Big deal!  The same occurs with random data. Therefore, there is no
Popperian corroboration; we don't know whether the degree of congruence
observed are (to use another Popperian term) "remarkable".  For tree
lengths, this is now an exception; Archie's randomization test, which are
better known as Faith and Cranston's' PTP test (permutation tail
probability test), can afford one a measured degree of corroboration that
in fact the length of the set of the shortest trees is remarkable.


        At best, parsimony provides a summary of whatever congruence
happens to exist among the characters in a given matrix, but it does not
tells us anything more about that congruence.  In fact, parsimony will
result in resolved trees given random data, a result that is apparently
surprising to some practicioner.  If tree length is your test, probability
can assist in the process of making that test critical and allow one to
hold the character state data to a higher standard. If character
congruence is your preferred test, try RASA.

>The evidence is not a set of judgements as to the probability of certain
events, the evidence is a set of characters which we conclude are
homologous

        It is elementary that a tree length of L implies L events
(inferred transformations), and it follows that if each is taken as
providing an equivalent degree of support, they are given equal weights,
which is arbitrary  and really doesn't reflect how well each
proto-hypothesis of homology passed your initial screening test.
Certainly each proto-hypothesis didn't pass the same screen, for the
evidence weighed in favor and against each is different, and some to the
test must have been more critical than others. At the very least, a
practicioner will afford more corroboration (in a diffuse sense) to a
proto-hypothesis of homology that has passed 100 evaluations  than those
that have passed fewer. Your favored methods of inference appear to me to
be steeped in probabilistic thinking, and yet you dismiss it.

>Whether they are probable or not in light of larger trends is not the
issue *in this test*.

        That's just not how it is generally understood.  Generalized
parsimony allows one to incorporate varying degrees of corrorboration one
might think they have into the parsimony procedure, and make (hopefully)
better use of the results of the outcome of the initial testing (if that's
how one decides puts a data matrix together).

>We use the concept "information content" usually to discriminate between
topologies; the most parsimonious topology being the one with the most
information

        To me, this is a particularly poor use of the term "information";
certainly when parsimony trees are misleading, they quite possibly may be
relaying the greatest possible amount of MISinformation.

JLW:
>> Take for instance a nucleotide change (A->T) and a
>> loss of a vertebra; not weighting one over the other implies
>> (hence the implicit assumption) that both have been and are
>> equally probable events.

>Only if you are working in a context of assessing the probability of
events. We are not. Once the two transformations are determined to both
refer to homologous characters, it really doesnt matter how complex one is
relative to the other.

        That really undermines your argument that parsimony provides a
test, and that the initial screening  tests are appropriate and adequate.
If the transformations have been "determined to be refer to homologous
characters", and then some are overturned on the basis of correlation,
then obviously some of the initial screening tests were misleading.  How do
you know which are misleading?  It is possible that a set of screening
tests could lead to common SYSTEMATIC ERRORS among those characters
allowed into the parsimony analysis, and a high degree of correlation
could be utterly misleading.  The natural, next consideration is "how
often does that occur"?  There are two ways to approach this question.
The first is to wonder about how often it might occur, say, in a large
number of studies, and if it could be determined that this occurred a very
few number of times, then to pronounce it a rather small, insignificant
source of phylogenetic error.  The second is to wonder about whether it is
occurring in a given, specific, instance, and if it's one's study, my
guess is that should be the preferred tact, because one would like to
know.  Unfortunately, parsimony alone won't tell you anything more about
this possibility for a particular data set.


>We do not calculate event probabilities a priori, thus we do not
incorporate them into the tree calculation, and thus do not suffer from
this circularity.

        In fact, you do.  Take an inferred transformation on a tree, say,
from no bristles to bristles present. In "unweighted" parsimony, for the
term SUML for all c 1 to n, that transformation is given a weight of 1.0,
which implies that the step from state 0 to state 1 carries the same
information as any and all other inferred transformations (say, wings
present to wings absent).  That is, for the calculation of a tree length
L, making all transformations equal to one equates (implicitly) the degree
to which that event is thought to have been probable.  Generalized
parsimony (again, see Swofford et al. in the Hillis, Moritz and Mable book
Molecular Systematics: 2nd edition) simply makes this explicit.

>Probability scores are only indicative of tendencies amongst defined
classes of phenomena.

        I presume this includes your probability scores of 1 and 0?

Now, back to the critical point:

 If probability plays an implicit role in the assessment of phylogenetic
hypotheses, its role should be made explicit.

 Since the practice of phylogenetic inference via parsimony has been
generalized, it is clear that its role has already been made explicit. The
impact of equal weighting can be explored in a any instance.  Take for
instance a sensitivity analysis; if, in an applied instance, different
weighting schemes do not change the result (say, tree topology), then it
can be inferred that weighting is not an issue (IN THAT CASE).  But if
modifications to weighting changes the optimal topology, then it also
changes the outcome of the parsimony congruence "test", and  a weighting
scheme must therefore be justified somehow.

I should take this moment to expound upon some previous points merely
glossed over, lest they be misunderstood:

        First, I am convinced of the limitations of using probabilities of
character state transformation in instances where they may not apply, and
that it is difficult to test various models of evolution in specific
instances, but for sensitivity analyses.  I don't like generalizations; in
fact, I dislike them as much as I dislike NEBULOUS AGGRANDIZATIONS.  The
limitations that exist with respect to maximum likelihood models (calling
upon models of character evolution that may not be accurate, for all
characters, across taxa, and through time) also obtain in an equally
profound way for parsimony.  Most practicioner of maximum likelihood are
honest and up front about assumptions that they know they are relying
upon.  That seems to be point of ML, and at least it's explicit.  Some
practicioner of parsimony are equally explicit, hence, generalized
parsimony.

        Second, probability testing can be applied to patterns in
character state distributions for hypotheses homology without invoking
models of character evolution, or even looking at phylogenetic trees.
This means that there is more to statistical phylogenetic inference than
maximum likelihood, a fact that is generally not appreciated.

        Third, the argument that phylogenetic inference is not statistical
because history is a singular thing is absurd, and demonstrates a clear
misunderstanding of probabilistic inference.  Statistical analyses are
conducted on data collected from experimental treatments AFTER the
experiments have been conducted, not before.  We are no doubt constrained
about what statistical inference can and should be made by what that
history was, but constraints do not hobble. One needs to open one's mind
to the possibility that existing methods of inference can be improved,
and supplemented before one can begin to benefit from making their
probabilistic thinking explicit.

         Based on first principles of evolutionary theory, we can expect
that sometimes the history of life will have produced confounding pattern
in the distribution of character states among taxa that guarantees that
the cladistic algorithm you describe will fail.  Its weakness and
susceptibility to this can be moderated by the incorporation of
considering probabilities of patterns of character state distributions.
Hennig's auxiliary assumption was an ad-hoc procedural necessity that is
no longer necessary, and was never sufficient.  Its antithesis, to first
assume non-homology and try to reject this null hypothesis, is more in
keeping with Popper's approach to hypothesis testing, because critical
tests now exist to reject this null without relying on how characters
interact on a tree, which is confounding because the tree may be
misleading if the hypotheses of homology are.

I'm interested, Tom: would you agree or disagree that your favored set of
methodologies can be improved upon?

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