[From Chris Cherpas (951206.1006 PT)]
[re: Rick Marken (951206.0930)]
I don't have time to respond to the details of your proposed experiment
yet, Rick, but I think it's a very interesting idea. I'm not sanguine
about ratio schedules, though. Without thinking about it, I'd like to
propose concurrent VIs. Anyway, I've just found a choice procedure to
be more sensitive to parameters of reinforcement. More later...
Best regards,
cc
Rick Marken's proposal is a good idea, and I think it should pursued. I
think pitting PCT and reinforcement is the wrong way to go. Rick says he
wants to "keep things clean and simple." I just tried to show that the
reinforcement response to a PCT "disturbance" experiment would likely also
be "why can't they keep it simple?" Chris Cherpas has already suggested
CONC VIVI, which is simple from an EAB standpoint (since a lot of
complications appear to 'cancel out' in the relative measure), but has been
previously characterized as excessively complex by Bill Powers on several
occasions. Instead of trying to bring PCT and reinforcement head to head,
why not just show good PCT in a context that reinforcement devotees would
find interesting?
I recall that there were some studies using a computer display and mouse
published in JEAB a few years ago. I have only a dim recall, and don't
have the references handy, so it may take a while for me to dig them out.
They could form a basis for the proposed experiments; what better than
building on a procedure already published in the journal of record. As a
recall, the work had to do with choice and number of response alternatives,
and also that there was some controversy over the interpretation of the
results.
//----------------------------------------------------------------------------
//Samuel Spence Saunders,Ph.D.
[From Bruce Abbott (951206.1750 EST)]
Rick Marken (951206.0930)
What I propose is that we build our own operant conditioning experiment; one
that uses a human subject and can be easily run on a computer (PC and Mac).
It would, of course, have to be one that reinforcement mavens (like Abbott,
Cherpas, and Saunders) agree is a "real" operant conditioning experiment.
I like the general idea but have a number of concerns about whether it can
do the job you set for it.
We've already done a demonstration of this type, on stimulus control. The
participants did just what was expected (qualitatively) under reinforcement
theory, and a nice quantitative model based on an assumed control structure
did a beautiful job of fitting the data, once the right parameters were
found. Reinforcement theory offered an account of both acquisition and
performance; the PCT model assumed that control had been established without
stating how this was achieved. Hardly a basis for rejecting either view.
Finally, we can report our results at the Behavior Analysis (or whatever it
is) meeting in SF this summer. If the reinforcement model does better than
the control model then there we jolly well are, aren't we? We will have to
reject control theory as a model of operant behavior. If, on the other hand,
the control model does better than the reinforcement model, then there they
jolly well are, aren't they? They will have to reject the reinforcement model
of operant behavior.
It probably won't work that way. "Reinforcement theory" is still evolving
as new data become avaliable. Which reinforcement theory do you propose we
use for making predictions? The ol' Skinnerian version isn't quantitative.
There is a variety of quantitative descriptive models out there for
specific, restricted situations, which make different assumptions about what
the relevant factors are in those situations and how they enter into the
computations. If there's more experimental error than you are used to in a
typical tracking study, will it be possible to distinguish the PCT and
reinforcement models on the basis of fit alone?
If you developed a PCT model that didn't fit the data very well, would you
reject PCT on that basis, or your particular model? Would it be fair to
expect EABers to reject reinforcement theory under similar conditions,
rather than the particular model proposed for the situation tested?
As for the predictions based on PCT, how would these be derived? By
constructing a model beforehand? How will you know what controlled
variables are involved so that you can construct the model?
These questions need to be addressed before we can get any further with your
proposal.
Regards,
Bruce
[From Rick Marken (951206.1815)]
Rick Marken's proposal is a good idea, and I think it should pursued.
Cool. Did it seem like I described a reasonable operant conditioning
experiment?
I think pitting PCT and reinforcement is the wrong way to go.
Why? I really don't understand this.
Rick says he wants to "keep things clean and simple." I just tried to show
that the reinforcement response to a PCT "disturbance" experiment would
likely also be "why can't they keep it simple?"
But you (and Abbott and Cherpas) are supposed to know what the reinforcement
"response" will be. That's the idea. With your help (and that of the other
ex-reinforcement theorists) we can design a study that will pit reinforcement
against control theory; and it will do so in a way that reinforcement
theorists will agree is a fair test of both theories. This really shouldn't
be hard. Just a simple operant conditioning experiment -- like the one's
Skinner did when he first "discovered" reinforcement.
Chris Cherpas has already suggested CONC VIVI, which is simple from an EAB
standpoint (since a lot of complications appear to 'cancel out' in the
relative measure), but has been previously characterized as excessively
complex by Bill Powers on several occasions.
I don't care how complicated the experiment is; I just want to be sure that
any complications are really necessary in order to appropriately test the
models. Complications are NOT necessary to test the control model; I can't
understand why they would be necessary in order to test the reinforcement
model. But I can be convinced that such complications are necessary; you can
convince me by illustrating their necessity using the reinforcement model. No
hand waving: the working reinforcement model!
You and Cherpas make reinforcement theorists sound like the OJ defense
team -- more interested in obfuscation and evasion than in understanding
what's actually going on in operant situations. This really should be easy.
Bruce Abbott says that reinforcement theory and control theory explain
operant behavior -- but control theory does it better. Well, can't we TEST
that, can't we? Or should I call the pope and ask for an ex cathedra on it;-)
Surely reinforcement theory is up to handling the operant behavior taught
first in every introductory psych text -- reinforced bar-pressing. Isn't
it??
Instead of trying to bring PCT and reinforcement head to head, why not just
show good PCT in a context that reinforcement devotees would find
interesting?
I haven't a clue what they would find interesting. I thought a demonstration
that there is no such thing as reinforcement might capture their interest -
- but nooo. Aren't reinforcement theorists interested in whether or not they
have the right theory of behavior? Geez, even the Catholic Church cared about
whether or not it had the right theory of the universe; at least they cared
enough to imprison Galileo (in a villa, true; but at least they were showing
some INTEREST. Can't we expect the same from those big, smart reinforcement
theorists;-))
I recall that there were some studies using a computer display and mouse
published in JEAB a few years ago...They could form a basis for the proposed
experiments; building on a procedure already published in the journal of
record.
YES!! This would be VERY valuable. Please try to find it!
Martin Taylor (951206 17:40) --
I would have thought that you would want the new operant data to be useable
in testing models. To do that, you have to have some idea of the structure
of plausible models, don't you?
Absolutely. But we already know what the control model of operant behavior
is. What we don't know is the reinforcement model -- the _working_
reinforcement model; not crap like Killeen's "systems analysis". That's why
we need the reinforcement mavens; they can help us design research that will
really TEST the reinforcement model. Presumably, the reinforcement maven's
know what the reinforcement model really is. Nobody seems to think WE do.
Bruce Abbott (951206.1750 EST) --
I like the general idea but have a number of concerns about whether it can
do the job you set for it.
How could it NOT do the job? Tell me, and then tell me how to MAKE it
DO the job!
We're doing an experiment to test the predictions of two theories. If we
design it correctly (with your help), one theory will predict the results
better than the other. What's your concern? Is there no way to remove
your concern? I'm asking YOU (and the other reinforcement experts) to
design the experiment so that YOU know that it will do the job (test
reinforcment and control theories of operant behavior).
We've already done a demonstration of this type, on stimulus control. The
participants did just what was expected (qualitatively) under reinforcement
theory, and a nice quantitative model based on an assumed control structure
did a beautiful job of fitting the data, once the right parameters were
found. Reinforcement theory offered an account of both acquisition and
performance; the PCT model assumed that control had been established without
stating how this was achieved. Hardly a basis for rejecting either view.
Reinforcement theory was never used to predict the results of this experiment
(except "qualitatively", as you say; that is verbally; and it even failed
qualitatively becuase we showed that the actual actions that produced the
results were NOT related to the stimuli that were presumably controlling
them). If you thought that this "stimulus control" demo didn't reject
reinforcement theory, why didn't you tell us how to design it so that it
COULD reject it (or, at least, show QUANTITATIVELY that reinforcement theory
could not account for the results as well as control theory).
You seem to spend a lot more time explaining why everything we do to
test reinforcement theory is no challenge to the theory than you do
explaining what we could do to TEST the theory. Do you really wonder
why Bill and I often think you might be on the reinforcement
theorists' payroll?
Which reinforcement theory do you propose we use for making predictions?
Any one that can actually be implemented as a working model; all of
them, hopefully. Surely they can all handle the simplest case of
operant behavior.
If there's more experimental error than you are used to in a typical
tracking study, will it be possible to distinguish the PCT and reinforcement
models on the basis of fit alone?
Let's design the study so that the experimental error is low enough to allow
discimination of teh models.
Come on, Bruce. What is this crap? You seem to be saying that it is
impossible to compare the predictions of reinforcement and control theory
models of behavior. I seem to recall that your goal is to show that
the control theory model of behavior is superior to the reinforcement model.
How are you going to show that if you can't compare the two models' ability
to predict experimental data?
If you developed a PCT model that didn't fit the data very well, would you
reject PCT on that basis, or your particular model?
I would try to find a way to patch up my model to make it work. If I
couldn't do that in a sensible, simple way, I would have to consider
adopting the model that did work.
Would it be fair to expect EABers to reject reinforcement theory under
similar conditions, rather than the particular model proposed for the
situation tested?
No. I would expect them to try to patch up their model so that it at
least works in the simplest case. If they can fix it up, then we
continue with other test comparisons; if not, they might want to
consider switching to the model that workds; control theory.
But why worry about what the reinforcemnt theorists will do if their
model fails? Let's just test the model and (hopefully) show that it does
fail; let THEM worry about what to do next. I'd personally welcome them
onto the PCT team if they wanted to join.
As for the predictions based on PCT, how would these be derived? By
constructing a model beforehand? How will you know what controlled
variables are involved so that you can construct the model?
We will develop the model based on our assumption about what variable is
controlled (probably the rate of picture presentation); the fit of the
model will be an indication of how well we guess; we can try other guesses to
improve the fit. Reinforcement theorists are free to determine the
reinforcer in any way they like -- and they are also free to determine
any other needed parameters in order to make a prediction. I'd give
reinforcement theory all the breaks (except for violating what we
already know about the world from physics and chemistry). But you're the
ex-reinforcement theorist; you tell me what the reinforcement theorists
need to make them think it's a fair test; as far as I'm concerned, they can
have anything they like except the results in advance;-)
These questions need to be addressed before we can get any further with your
proposal.
Yes. And they are the questions I was hoping you could answer.
Again, this does not have to be complex; it should be simple so everyone
can understand it. The operant experiment I described is VERY simple.
Reinforcement theory should be able to handle it, no problems. I'm looking to
you to tell me how to make this experiment as clear a test of reinforcement
and control theory as possible.
If you're a fan of PCT (as you claim) I would imagine that you would love
to try to find way to prove the superiority of PCT over reinforcement theory.
So, is the operant experiment I described OK? Can you write a reinforcement
model to account for the expected results?
Best
Rick
[From Samuel Saunders (951207:21:59:36)]
In looking through recent issues of JEAB for information that might be
usefully for the proposed experiments, I ran into something which may pose
serious problems. I was aware that human FI performance tends to be
different from that of most non-human subjects. Apparently that is true of
most schedules. The following is the first paragraph from Horne, P.J., and
Lowe, C.F. (1993) Determinants of human performance on concurrent
schedules, JEAB, 59, 29-60:
There have been numerous reports in the literature of marked differences
between the performances of adult humans and other animal species on
schedules of reinforcement. This is true on fixed-interval (FI) and
fixed ratio (FR) schedules, and is evident both in response patterning
and in sensitivity to the schedule parameters. The evidence also
suggests that the occurrence of rule-governed behavior in humans may give
rise to some of these differences.
The article then cites some reviews on this topic, which I will look at and
report on. The article was addressed to the question of whether human CONC
schedule performance conforms to matching law formulations. In the paper,
6 experiments with a total of 30 subjects were performed. The result,
quoting from the abstract:
The performance of only 13 of the 30 subjects could be described by the
generalized matching equation and were within the range of values
typical of those reported in the animal literature.
The authors suggest in their discussion that it may be necessary to
disguise the contingensies to avoid the influence of rule-governed
behavior. Regardless, this is likely to be a problem, because most of the
quantitative models that I am aware of, which might be adapted for our
comparison, are designed with data from non-human subjects in mind and are
not likely to be easily adapted for use with human subjects, given the
above.
I will post additional information when I have a chance to look at some of
the references in the Horne and Lowe paper, and to look at some of the
other papers with human subjects my search of the JEAB cumulative index
produced.
//----------------------------------------------------------------------------
//Samuel Spence Saunders,Ph.D.
[From Rick Marken (951209.1610)]
Samuel Saunders (951209:18:25:07 EST) --
While Rick Marken is no doubt having a fun time with this topic, I
still think the experiment is a good idea.
I _am_ having a fun time; but, don't worry; I'm feeling pretty
guity about it;-)
And I still do think the experiment's a good idea -- and I'm
glad you do too.
To do it correctly, I think it is necessary to review recent EAB work
with adult humans, and to review canditate reinforcment theories. I
will provide a model and a critique of procedures based on a review of
the published work by the middle of the week...From now to mid-
week, I will avoid being drawn into more discussion so I can
concentrate on the task I have set myself.
How does this sound, Rick?
Music to my ears.
I look forward to seeing the results of your work. Thanks in advance
for doing it.
Best
Rick