[From Bill Powers (930106.2100)]
Dennis Delprato (930106) --
Hedges takes as examples the Particle Group Data reviews that
examine "stable-particles" and focuses on mass and lifetime
estimates. He argues that the Birge ratio (the accepted index
of determining "how well the data from [a] set of studies agree
(except for sampling error)" is comparable to that obtained
with socio-behavioral research.
Interesting that he had to go to particle physics to find a
parallel -- and even more interesting that the statistical facts
of particle physics are no better than those of the socio-
behavioral sciences! Of course particle physics is strictly about
mass phenomena: there is no such thing as "an" electron. The low
predictivity arises, I should think, in such pursuits as
measuring solar neutrinos or trying to find a new particle, where
the number of events is very small and willy-nilly, the
physicists find themselves trying to apply mass-statistical
measures to single events -- "Was that a real top quark?"
Control theory is more akin to classical physics, which deals
with a continuous macroscopic world. Quantum mechanics shades
into classical physics for large-scale phenomena -- on the scale,
say, of a mitochondrion in a cell or a speck of dust. There have
been numerous psychologists (and physicists) who have speculated
about quantum phenomena in the mind -- less, I suspect, because
of any justification for applying quantum concepts on a scale as
large as a neuron than because the predominance of statistics
gives them familiar ground to walk on.
Hedges would have found a very different picture if he had talked
to physicists in areas not connected with the quantum physics of
rare phenomena, or with engineers.
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Did Skinner ever face the problem of the specificity of the
relationship between deprivation and reinforcement?
I am fairly certain he would invoke evolution. When the
organism is deprived of certain opportunities (to eat,
sometimes exercise...), it is more likely to eat, be active...
when given the opportunity than under conditions of
nondeprivation. "In the evolutionary sense this 'explains' why
water deprivation strengthens all conditioned and unconditioned
behavior concerned with the intake of water"
This is one of those non-explanations, isn't it? If it turned out
that organisms were LESS likely to eat, exercise, and so on under
deprivation, evolution would explain that, too. This is what I
call the "will of God" way of invoking evolution. Saying that the
observed relationship is due to evolution is no more explanatory
than saying that God wanted it that way.
The real question that needs an answer is "What is the
organization that evolved (or that God willed, it makes no difference) such
that we observe this relationship?" A real
explanation would elucidate that organization and not futz around
with evolutionary pseudo-explanations.
I intepret him as taking the position that one way to make an
object or activity reinforcing is by way of deprivation. Thus,
his theory agrees with the statement that something is
reinforcing (functions as a reinforcer) because of deprivation.
This is like explaining how a radio works by saying that one way
to make the music louder is to turn the volume control, and
another is to take the cover off the speaker. I'm reminded of the
quote that Rick (or was it Tom) came up with, in which Skinner
admitted that it would be better to understand how the insides of
the organism work. He was really battling against people who
tossed off glib and question-begging explanations in terms of
traits and tendencies, and of course I'm with him all the way,
there. Unfortunately, he persuaded a lot of people that
successful models of the insides were millenia off, and not worth
thinking about.
He would object to adding that deprivation leads to a want
that in turn enters into the control of behavior. To him,
want is an inner cause that is of no use in predicting
and controlling behavior. He would ask how would we
produce a want, how do we know what the organism wants?
Yes, to him a "want" was forever a fiction, a mentalism, a ghost
in the machine. He had another reason for rejecting "inner
causes," no matter of what kind. He insisted that the only causes
of behavior lay ultimately in the environment; the existence of
even a single inner cause would call all of his explanations, and
his whole philosophy, into doubt.
I wrote him a letter once explaining that control theory could
provide a scientific meaning for terms like wants and goals and
intentions. He wrote a two or three line letter back saying that
there was nothing in this idea that he found useful.
Note the relevance of phylogeny (in Skinner's view) to the
fish case.
Relevance, maybe. Explanation, no.
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Greg Williams (920106 - 2) --
Using the PCT model for the tracking of a particular subject,
which gives a very high correlation between model-predicted
handle positions and actual handle positions during the course
of runs with disturbances other than the disturbance used to
calibrate the model, what is the correlation between model-
predicted cursor positions and actual cursor positions during
the course of such runs?
This depends on the difficulty (how rapidly the disturbance
changes). For low-difficulty tasks, the predicted cursor movements have a low
correlation, maybe only 0.5, with the actual
cursor movements. That's because the cursor hardly moves from its
ideal position, so the noise is large in comparison with
meaningful movements. When the difficulty is much higher, so the
cursor excursions away from ideal amount to 10 or 15 percent or
so of the peak-to-peak handle movements, the correlation improves
considerably; the model cursor correlates as high as 0.8 or 0.9
with the actual cursor movements. That's because the errors are
due to systematic sluggishness of tracking, which the model
reflects faithfully. You would expect the cursor predictions to
be worse than handle predictions because the cursor position is
the difference between two large numbers, handle position and
disturbance magnitude.
At the highest difficulties the correlation falls off again
because tracking itself begins to break down; the person simply
loses control altogether. I'm speaking of experiments in which
there is a moving target and also a disturbance applied directly
to the cursor. I think this is also true for plain compensatory
"tracking."
I'm giving you these numbers from memory. I think Tom Bourbon may
have some old data in which these numbers were calculated,
although not for varying degrees of difficulty.
I suppose that the latter correlation will not be very
high. Is that true? If so, the COMPLETE model is wrong, isn't
it?
COMPLETE and RIGHT are two different things. A complete model
commits itself to a prediction that is exact within the limits of
measurement error. It says "At time t=120, the equivalent handle
position is 248 pixels above zero." In fact, the real handle
position might be 300 pixels BELOW zero at that time. If that's
the case, the modeler would go back to the drawing board;
something is really wrong with the model. Or, sometimes, the
modeler will look at the real handle trace and see that just at
that time there was an abrupt and very large departure from the
pattern of movement before and after that time, and that the
model fit just fine both before and after. In that case, the
modeler would shrug and say that something happened that the
model can't explain. It's not worthwhile trying to make a model
fit every anomaly. But there had better not be too many of them,
and they had better not occur in the same position in every run.
Somtimes anomalies are meaningful, as in the independent
discovery, by Rick and me, of spontaneous reversals. Even
practiced trackers will occasionally, for no apparent reason,
reverse the sign of the connection between error and action.
There is then a brief period of exponential runaway, followed in
about half a second by a return to normal tracking. Rick
proceeded to put reversals in on purpose, and found that the
model reproduced the exponential runaway extremely well. Of
course we had to put in an ad-hoc higher level that, half a
second later, reverse the output sign of the control system to compensate for
the external reversal. The signature of a
spontaneous reversals is unmistakable, once you've seen a few of
them. So that kind of anomaly is accounted for, if not explained.
The main point of insisting that a model or an explanation be
complete enough to give an exact (even spuriously exact)
prediction is so you can tell when the model is wrong, and by
about how much. You can't do anything systematic to improve a
model that makes predictions so uncertain that you can't tell
whether they match the data or not. If you can measure the
behavior with an accuracy of 1%, then the model should predict
within 1%, no matter how foolish you feel about making such
accurate predictions with a model you know can't be right yet. If
the model predicts to 1%, then at least you know it's complete
enough to test.
I see no reason why a predictive S-R model could not be
developed to predict cursor movement.
Well, I think I do, but if you want to put your model where your
mouth is, I will pay attention. Of course I expect it to be a
real S-R model -- no feedback allowed!
If you don't want to devise the demonstration to prove your
point, then I can only agree with you: you can see no reason why
a predictive S-R model could not be developed.
It seems to me that a large number of models (PCT and S-R, each
differing from the others in parameters and/or basic forms) can
produce equally high correlations between actual handle
position and model-predicted handle position, because the
moment-to-moment differences in the predictions of the various
models get "washed out" in computing those correlations.
In one sense this is certainly true, at least of PCT models. You
could propose that the comparator contains an integrator, and
that the output function is just a linear multiplier. You could
propose that the input function multiplies the perceptual signal
by 25.9923, and that the input where the perceptual signal enters
the comparator weights the perceptual signal by 1/25.9923. Or you
could say that the reference signal is also multiplied by 25.993
and the integration factor of the output is 1/25.993 of the
factor in the canonical model with an input gain of 1. You could
say that the reference signal enters the input function, or the
output function, and there is no comparator. You could say that
there are three reference signals, one entering the input
function, one entering the comparator, and the other entering the
output function.
These variations would be indistinguishable in terms of their
behavior, and could all be adjusted to match the real behavior
equally well. But they would all be convertible to an equivalent
model of the canonical form we use, so these differences are
trivial from the behavioral standpoint. Only through circuit-
tracing can we really decide among them -- and where circuit- tracing has been
done, the canonical model is usually, but not
always, the best geometric fit.
You're actually talking about differences of an even subtler
form, where the model, for example, might contain an instability
that causes oscillations at 100 MHz. Since these oscillations
would never be visible in the behavior, this model would also fit
the data. But there's a principle of parsimony, which recommends
that you put nothing into the model that isn't required to
explain observations. So far, no variation on the model explains
what we see any better than the canonical one.
But I deny that any S-R model will be able to predict the
behavior of the handle and the cursor with any interesting degree
of accuracy. It's up to you to show that I'm wrong, and you're
not going to accomplish that with words.
Sorry about the old demon. I kind of liked him.
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Best to all and goodnight,
Bill P.