[From Bill Powers (951214.1630 MST)]
Bruce Abbott (951214.1635 EST)]
But to look for a "rate-limiting" process is
simply to say "Even if the basic model predicts incorrectly, I choose
to defend it." If all you want is to save the theory, there are
countless ad-hoc assumptions you can make that will do the trick.
Well Bill, how about if I present a control-system model in which
the system is capable of generating infinite output, and then
demonstrate that it incorrectly predicts the behavior of the real
system when a large error is present.
An ad-hoc output limit would have to be assumed. However, it could be
defended quite well, because there are plenty of data to supply the
actual limits of motor performance. Other limits, such as limits on
perceptual signals or error signals can't be so easily defended;
sometimes one just has to bite the bullet and make an ad-hoc assumption.
I said they were ugly; I didn't say we can always avoid them. But as
long as they remain unsupported, they're a nagging imperfection of the
theory, a place where the model is vulnerable.
It's a wonderful debate trick called "poisoning the well." After
the well has been poisoned, any attempt to drink from it (e.g.,
offer changes to the model as _you_ defined it) instantly kills the
argument. Well done.
Now don't be pissed off at me. I play by the same rules. Ad-hoc
assumptions are ALWAYS a weak spot in a theory, mine or anyone else's.
All you have shown, of course, is that the simplest possible
version of reinforcement theory would lead to instability for all
values except maximum output and zero output. This version
includes the highly unlikely assumption that change in behavior
rate and reinforcement rate are linearly coupled.
I took the verbal statement that "an increment in reforcement causes an
increment in behavior (rate)" and turned it into a mathematical
equation. Then I deduced what behavior would result from that statement
in a simple ratio experiment. What's so awful about that? That's how you
have to start to turn any vaguely-stated relationship into something you
can reason about mathematically.
The linearity of the relationship between changes in behavior rate and
reinforcements is, of course, an approximation. But it makes little
difference in the outcome if the nonlinearities leave the function with
the same sign over the range of interest. Suppose you say
dB/dt = k1*f(C) - k2*B,
where f(C) is some nonlinear function. As long as a plot of the value of
f(C) against C remains above some straight line a*C (where _a_ is any
small positive number), the exponent will be positive and runaway will
occur. The details of the function don't matter. To stop the runaway,
the nonlinearity would have to be so extreme that f(C) would go to zero
or become negative for large values of C -- in other words, C would have
to become neutral or aversive and cause zero or negative values of
dB/dt.
Why should I be forced to accept YOUR model of the reinforcement
process, especially when it has been known since DAY 1 that such a
model would not accord with the data?
You don't have to accept my model. But if it has been known since day 1
that such a model doesn't fit the data, why do people still say that an
increment in reinforcement causes an increment in behavior rate?
By offering this ridiculous model and then asserting that any
attempts to change it on my part will convict me of ad hoc-ery, you
poison the well.
Evidently, you want to add some other functions that will make the
result come out right. I was, indeed poisoning the well; putting you on
notice that ad-hoc fixes to the problem are going to meet with heavy
criticisms unless you can offer some serious defense for them. Showing
that they make the theory fit the data is not a defense.
... the application of the "ad hoc" label amounts to an unsupported
assertion that there is no independent evidence for these
assumptions. No matter, they have been poisoned by the accusation;
before they can even be offered, anyone who would do so must fight
an uphill battle just to establish that the ad-hoc label is wrong.
The well has been poisoned.
Yes, it is always an uphill battle to prove that an ad-hoc assumption
can be defended. It should be. All models begin as nothing but ad-hoc
assumptions. We take them seriously only when the evidence has mounted
up that the ad-hoc assumption is probably right. Then it becomes part of
the model.
An ad-hoc assumption is one that corrects the predictions of a model to
make the model's behavior fit the data. Because it is so easy to find
such assumptions, most scientists demand some other evidence that the
assumption is true.
Now we add more poison to the well. If one attempts to offer an
alternative to the simple model you constructed, he or she is a
liar attempting to explain his lie. The other possibility is not
considered. Perhaps the simple model said to be "the"
reinforcement model does not represent any model ever held by
reinforcement theorists. Perhaps the implied assertion that it
does capture the essentials of reinforcement theory is the lie.
I used the example of Michael Palin the liar mostly to show how easily
ad-hoc statements can be cooked up to support any proposition, without
regard to its truth. A scientist offering an ad-hoc explanation is not,
of course deliberately lying to anyone, except perhaps himself or
herself. But the principle is the same: manipulate the assumptions to
make the conclusion appear true.
What is in dispute is whether any change to the simple model of the
reinforcement process that you invented would constitute "an
embarrassing excuse." If we're going to play the game this way,
then please give me a few minutes to whip up a simple PCT model
that does not include any limits and, perhaps, doesn't even
identify the right controlled variable. After I have shown that
this model contradicts the observations, I will offer for your
amusement a series of what I will term "ad-hoc patches" to the PCT
model that will "save the theory." I will state that anyone
offering such patches is only a good liar trying to explain his
lie.
It depends on whether you make a change to the model that can be
defended independently of the corrected predictions. If you can show
that the patch is in accord with first principles, or that there is
experimental evidence saying that this patch is in accord with
independent data, you have a good chance that it will be accepted into
the model.
Actually, the PCT model used to explain tracking behavior doesn't have
any limits. The disturbances are smooth and slow enough, and limited
enough in magnitude, that the question of limits doesn't arise. I would
be very surprised if this model continued to work in an experiment where
the control handle was mounted on a very stiff spring, or if the mouse
ran off the mouse-pad, or if any other limiting condition occurred. We
specify the conditions under which the model is supposed to work.
Outside those conditions we don't guarantee anything.
···
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I'm with Sam on this one. Your challenge was to demonstrate
_empirically_ that the contingency built into the apparatus was
really there. I think we both took this to mean that we should
specify an empirical procedure for proving that the apparatus works
as designed.
I guess you have a more restrictive definition of "empirical" than I do.
I would count printing out the program as an empirical approach, as well
as taking the apparatus apart to see how it works.
In natural settings, contingencies exist that were not programmed
by an experimenter. The procedures Sam and I outlined work just as
well to identify and characterize these "natural" contingencies as
they do for "artificial" ones.
Right, but since contingencies are imposed by physical relationship
connecting actions to consequences, why restrict yourself to just
manipulating one variable and seeing how another changes? You have all
of physics and engineering at your disposal; you have identified the
input variable and the output variable. If you can, why not do the full
physical analysis? I know there may be times when you can't, but if you
can look at the physics of the situation, why not do it?
-----------------------------------
Some problems for the proposed PCT model:
1. The model proposes that reinforcement rate is controlled, and
that the reference level is under normal circumstances within reach
of the system. This needs to be demonstrated. Alternative model:
the rat is controlling for food presence, and against too high a
level of effort.
Yes, I tried that in modelling the Staddon-Motheral data. But it was an
ad-hoc model and I wouldn't dream of publishing it.
Actually, the control-system model doesn't require that the reference
level be reachable. You can fit a model to the data and derive the
reference level even though the controlled quantity never gets to the
reference level.
2. It does not account for acquisition and extinction. Even the
flawed bistable reinforcement model at least did this much, without
requiring (guess what) an _ad-hoc_ assumption about the "resetting"
of the ref.level for the CV.
I made note of that ad-hoc assumption. Actually, the reinforcement model
requires the assumption of a decay term, specifically to make the
behavior return to zero when there is no reinforcement. Without it, the
behavior would simply stay constant when reinforcement ceased. The PCT
model requires an assumption about resetting the reference level, but no
assumption about a decay term. The reinforcement model is the other way
around.
It was my intention to work on those problems, but you evidently
think that it was my intention to demonstrate that reinforcement
theory can be patched up so as to compete with PCT. That would
explain the strong response to a small disturbance.
Why not go ahead and try anyway? I'm sure that you will be highly
sensitive to making assumptions for the sole purpose of matching the
model to the data, and will pay attention to independent justifications
for the assumptions. If you have to make assumptions, so be it. I have
to make them, too. Let us both make sure that any claims about the model
that results are appropriately limited.
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Best,
Bill P.