Non-PCT Research: Irrelevant?

[Abbott_Bruce_Indiana]

(From Bruce Abbott [941007.1240 EST])

      Based on recent postings, it would appear that some advocates of PCT
believe that any research not conducted explicitly within a PCT framework is
worthless, the argument being that such work says more about random
disturbances in the environment than about behavior. I must say that if your
goal were to prevent widespread adoption of the PCT model within the
scientific community, you could hardly do better than to assert the
irrelevance of everyone else's work.

      I would assert that much of the work done in the behavioral sciences
does not suddenly become irrelevant nonsense after adoption of the PCT model.
As evidence I offer the following two examples:

1. A researcher sets out to investigate "freezing" in rats--a total
inhibition of movement that follows exposure to an aversive stimulus such as
brief footshock. Rats are exposed to a series of three brief shocks spaced 30
seconds apart and are then observed for several minutes immediately after the
last shock. The study reveals that freezing follows a specific time course
and that the proportion of time spent freezing depends strongly on the
intensity of the shocks. Further research discloses that freezing is NOT
elicited directly by the shocks themselves, but by the stimuli defining the
context in which the shocks were received: reintroduced to the shock chamber a
day later, the rat immediately re-freezes; exposed to a different chamber
immediately after receiving shock in the first one, the rat does not freeze.

The research just described investigates a phenomenon (freezing) with the
purpose of showing its time course and identifying situational variables
(contextual stimuli, shock intensity) of which it is a function. In what way
does viewing the research from a PCT perspective invalidate these studies?

2. Students are tested to determine the size of the "inverted-t" illusion.
They are shown a large inverted T and are asked to adjust, by means of a
crank, the length of the vertical segment until it appears to be the same
length as the horizontal segment. The "error" between the actual equality
point and the adjustment point is computed on each trial over a large number
of trials; the errors of a given student are then averaged and their standard
deviation computed. Stimulus variables such as the position of the vertical
line relative to the horizontal are subsequently varied in order to determine
their influence on the size of the error.

Again we have an investigation of a phenomenon to define its magnitude and
identify some of the variables that influence it. Do we scrap these results
when we subsequently adopt a PCT perspective?

Clearly the findings of these two research projects remain important and
interesting regardless of the theoretical orientations of the investigators
who conducted them. This is not to say that a PCTer would have conducted
these projects in the same way. I can easily imagine how, for example, the
inverted-t study might have been changed to allow continuous adjustment
(perhaps via a joystick) of vertical line length while a computer randomly and
continuously perturbed the end-position of the line, but this only transforms
a discrete-trials task into a continuous one and would probably generate
similar results.

If PCT is ever to become "mainstream" science, its enthusiasts must be able to
demonstrate to non-PCT researchers how adopting a PCT framework and
methodology will help them to investigate and understand the phenomena with
which THEY grapple. For many research problems the truth or falsity of PCT is
simply irrelevant.

It IS true that SOME research findings become trivial side-effects when viewed
from the PCT perspective, but this conclusion in no way applies to ALL
research not designed with PCT in mind. Many of these findings will in fact
have direct relevance to PCT (perceptual studies, for example). To gain
acceptance of PCT as a general theory of behavior, we need to show, wherever
possible, how previous work "fits into" the PCT framework. To assert
otherwise--that all non-PCT research is misguided nonsense--will be
interpreted by the research community for what it is: sheer arrogance.

In making this argument my purpose has not been to chastise any specific
individuals (whose statements I may have misinterpreted) but to raise what I
see as an important problem having implications for the future of PCT.

regards,

Bruce

[Marken_Richard_S1]

[From Rick Marken (941007.1400)]

Bruce Abbott (941007.1240 EST) --

Based on recent postings, it would appear that some advocates of PCT

That would be me:-)

believe that any research not conducted explicitly within a PCT framework is
worthless,

Yep. Almost completely worthless for understanding control (it might be quite
worthwhile for obtaining publications, tenure and fame, however). Non-PCT
research can provide hints about what kinds of controlled variables to look
for in PCT research; that's about it. In fact, you can get the same quality
of hints (usually) by just watching people behave; conventional research
methods don't help reveal much in particular that might be of interest to
PCT.

the argument being that such work says more about random disturbances in the
environment than about behavior.

Depends on the research. If it is research based on averaging over subjects,
it tells us about nothing at all (except subject averages). If it is single
subject research it can hint at quite a bit that is worthwhile -- such as
possible controlled variables.

I must say that if your goal were to prevent widespread adoption of the PCT
model within the scientific community, you could hardly do better than to
assert the irrelevance of everyone else's work.

My goal is to prevent more of what is already going on; adoption of PCT by
those who want to fit it into the existing psychological paradigm. This
results in PCT that is not PCT. The major purveyors of this approach are
Carver and Scheier, Locke, Lord, Hyland and a few others who Tom Bourbon can
tell you about.

I would assert that much of the work done in the behavioral sciences does
not suddenly become irrelevant nonsense after adoption of the PCT model.

Well, it would be nice if this assertion were true. Unfortunately, it's not.
If you want to see why it's not true, the "proof" is in Powers'
"Quantitiative analysis of purposive systems" in the 1978 issue of Psych
Review. I also recommend my paper called "The blind men and the elephant" and
Bourbon and Powers "Models and their world", both of which are available in
an issue of Closed Loop, which can be ordered from Greg Williams, a member of
CSG-L. All of these papers show why PCT makes conventinal behavioral science
irrelevant. The short answer is because PCT is about a phenomenon that
conventional behavioral science doesn't even know exists -- the phenomenon of
control. PCT is not a theoretical alternative to existing behavioral
theories; PCT is a theory of a phenomenon that is not explained (or
recognized) by existing behavioral theories -- control. PCT starts with the
observation that control is a fact of life; control theory explains how
control occurs. So PCT is irrelevant to conventional psychology and vice
versa.

The first thing to learn about PCT is the nature of the phenomenon it
explains - - CONTROL.

As evidence I offer the following two examples:

The research just described investigates a phenomenon (freezing) with the
purpose of showing its time course and identifying situational variables
(contextual stimuli, shock intensity) of which it is a function. In what way
does viewing the research from a PCT perspective invalidate these studies?

PCT doesn't really "invalidate" these studies; these are just irrelevant
to PCT because they are not addressing questions about control. However,
there are suggestions about the kind of controlling that might be going on
here; for example, the rat is probably controlling for the perception of pain
that results from shock, trying to keep it at zero. The "freezing" suggests a
conflict between systems using the limbs to control perceptions of direction;
if there is no way to control the shock, many different higher level systems
may be setting references for the direction control systems, telling them to
perceive going in several different directions at once. So your studies can
provide hints about what variables the rat is controlling -- but you have to
test to determine which variables are actually under control. The study
provides some hints, but here are also problems that occur when studying
control of intrinsic perceptual variables like pain; disturbances like shocks
probably set off reorganization, resulting in continuous changes in the
parameters of control.

Stimulus variables such as the position of the vertical line relative to the
horizontal are subsequently varied in order to determine their influence on
the size of the error.

This is getting closer to a study of what and how people control. As it sits,
however, it is just an S-R study that can only provide hints about the
variables any individual might be controlling. One problem with studies like
this, by the way, is that they assume that certain stimulus variables (like
the position of the vertical line relative to the horizontal) always "have an
effect" on the perception (as measured by the responses). Besides the fact
that the subject's responses are not actually an indication of the perceptual
variable (see my post, Bill P's post and all of Tom's posts on
psychophysics), it is not necessarily true that particular "stimulus
variables" have the same "effect" on a perception each time. In PCT, stimulus
variables are really just disturbances to perceptual variables; the "effect"
of these disturbances depends on the perception the the subject is
controlling -- and the subject can often voluntarily change the perception
under control. To see what I mean, look at my chapter called "Behavior in the
first degree" in Hershberger's "Volitional Action" collection. At the end of
the chapter I describe an experiment where a subject controls the "size" of a
quadrilateral object. The effect of a disturbance (change in the length of a
side) is different depending on whether the subject is controlling area or
perimeter. It turns out that a subject can control either variable, leading
to very different conclusions about the effect of the disturbance ("stimulus
variable") on perception.

Clearly the findings of these two research projects remain important and
interesting regardless of the theoretical orientations of the investigators
who conducted them.

I hope it's clear now that this is not "clearly" true. The findings of these
two research projects remain important only as long as you neglect the fact
that the subject's in these studies were controlling. If the subject's in
these experiments are control systems, then the results of these studies are,
largely, irrelevant to PCT.

If PCT is ever to become "mainstream" science, its enthusiasts must be able
to demonstrate to non-PCT researchers how adopting a PCT framework and
methodology will help them to investigate and understand the phenomena with
which THEY grapple.

And that is precisely why PCT has NOT become mainstream science. We cannot
demonstrate how adopting PCT will help non-PCTers investigate the phenomena
with which they grapple because PCT CANNOT help them grapple with these
phenomena. From a PCT perspective, the phenomena with which non-PCTers
grapple are NON-PHENOMENA. This is what my "Blind men" paper is about. This
is a big problem for PCT. I see two possible ways to deal with it: 1) be
straight about it (and be unpopular) or 2) lie about it (and be Carver,
Scheier, Lord, et al). Guess which one I pick.

For many research problems the truth or falsity of PCT is simply irrelevant.

Agreed. It's the existence vs non-existence of control that is relevant.

Many of these findings will in fact have direct relevance to PCT
(perceptual studies, for example).

It depends on what you mean by "relevance". Many are indeed relevant because
they point to perceptual variables that might be controllable. But, by and
large, the best we can hope for from non-PCT research (relevance-wise)is
HINTS about what kinds of variables might be controlled. That is, they can be
the START of ITERATIVE PCT TESTS and MODELLING to determine the variables
under control. But the phenomena that the conventional research was
addressing (reinforcement, freezing, stimulus effects, etc) can be safely
ignored; thay MAY be intresting side effects of controlling (as is likely
with freezing) but they need no longer the focus of testing; the focus of
testing (and modelling) is on controlled variables.

To gain acceptance of PCT as a general theory of behavior, we need to show,
wherever possible, how previous work "fits into" the PCT framework.

I think this is a good goal and I believe we have tried to do this, where
possible (it is often impossible because the "previous work" is just
generalizations based on statistical averages over many people). For example,
we have pointed out that "reinforcements" are just disturbances to
controlled perceptual variables. Of course, this means that there is nothing
"reinforcing" (strengthening) about reinforcement -- in other words, the
concept of reinforcement is just a mistaken view of what is happening when
an organism controls its perceptual input. Reinforcement "fits in" to PCT
so well that it disappears; the concept is no longer needed (just as
the concept of "phlogeston" is no longer needed in chemistry).

To assert otherwise--that all non-PCT research is misguided nonsense--will be
interpreted by the research community for what it is: sheer arrogance.

It is being interpreted as "sheer arrogance", I agree. But we are in kind of
a bind. If we try to make it seem like PCT is basically compatible with what
conventional behavioral scientists are doing, then we risk getting more
people (like Carver & Scheier) who end up believing it, and not doing PCT. On
the other hand, if we try to draw a clear distinction between PCT and
conventional behavioral science, we are seen as extremist lunatics or
arrogant assholes (both correct perceptions in my case, but Tom and Bill
are sane, nice people). I don't know if there is a middle ground that is both
effective and honest. I think, like Copernicus and Galileo, we are just stuck
with having to be honest. Of course, Copernicus was only honest posthumously
and Galileo had no friends. But my cat likes me;-)

Best

Rick

[Tom_BOURBON3]

Tom Bourbon [941010.1700]

Rick Marken and Martin Taylor have already replied to Bruce's post. This is
my first opportunity.

(From Bruce Abbott [941007.1240 EST])

     Based on recent postings, it would appear that some advocates of PCT
believe that any research not conducted explicitly within a PCT framework is
worthless, the argument being that such work says more about random
disturbances in the environment than about behavior.

I believe you have overstated the case, Bruce, although your phrase, "some
advocates," leaves a little uncertainty as to your target(s).

The first major complaint we have with much of the traditional literature is
over things, not directly related to the phenomenon of control, that should
concern _all_ behavioral scientists. In the majority of traditional research
by psychologists (and by researchers who borrow their experimental methods
from psychologists), experimenters intend to learn about and talk about why
individuals behave as they do. The problem is that most experimental methods
and statistical analyses used in traditional research are suitable, not for
the study of individuals (idiographic research), but for determining
statistical features of numbers in distributions (nomothetic research) --
measures of central tendency and dispersion, counts of frequencies, estimates
of probabilities and proportions, and so on.

If traditional research is nomothetic by design, and if it is conducted
properly, and if the interpretation is limited to a discussion of groups,
then there are no reasons for a PCT scientist to challenge or question the
work; the experimenters use the nomothetic procedures properly and obtain
meaningful descriptions of collective data. However, in most published
psychological research the collective methods are abused. The general case
has the experimenter(s) using nomothetic procedures in ways that violate the
prerequisites for such methods, and then compounding their felonies by using
the resulting data as though they support idiographic claims about how and
why individuals act as they do. There is no justification for those
practices. On csg-l, many criticisms of traditional research are directed at
this general failing and not at anything that has to do with PCT per se.

     I must say that if your
goal were to prevent widespread adoption of the PCT model within the
scientific community, you could hardly do better than to assert the
irrelevance of everyone else's work.

To the degree that our assertion derives from the nomothetic-idiographic
confusion and the experimental-statistical crimes in behavioral science that
I described above, we have little choice. There is no other way to say it:
They use the wrong methods and draw unjustifiable conclusions from their
data. That assertion is true whether or not there is PCT in the world. For
decades, mainstream behavioral scientists have ignored many non-PCT critics
who tried to sound alarms over the nomothetic-idiographic confusions and the
experimental-statistical failings of traditionalists.

     I would assert that much of the work done in the behavioral sciences
does not suddenly become irrelevant nonsense after adoption of the PCT

model.

Here, we come to another matter: the possibility that PCT renders much
traditional research inadequate. Rick already commented on this subject, but
here is my offering. We can dismiss _all_ _conclusions_ drawn from
traditional research that suffers from the contaminations I discussed above
and we invite all other behavioral non-PCT scientists to join us in our act
of rejection. Scattered here and there through that vast traditional
literature, we _might_ find data that give us clues about control, but we
would be dealing with low-grade ore -- very little return for the effort.
The problem is the research was not set up to take into account the
phenomenon of control; in fact, most traditional research is carefully
designed to eliminate even a hint of active control _by_ the subject.

The most likely places in the traditional literature where a PCT person
_might_ find hints about control are in the areas where researchers have
studied individual subjects -- parts of psychophysics, parts of the
literature on conditioning, some of the literature on clinical case studies,
and so on. Even though the researchers did not study their subjects as
controllers, they did study them as individuals. _Perhaps_ some of their
data will give us hints about variables controlled by individual subjects.

I say "might," and "perhaps." There is no assurance that a traditional
study, or a body of traditional literature, will reveal _anything_ about the
phenomenon of control, in general, or about the specific variables a
particular subject controlled, in particular. Even studies in which certain
stimulus-response associations repeat with very high reliability may tell us
about the reliability of irrelevant side effects of behavior, and not about
whether a subject is controlling, and if so, what is controlled. Those
questions can only be answered by research specifically designed to test for
controlled variables.
. . .

If PCT is ever to become "mainstream" science, its enthusiasts must be able
to demonstrate to non-PCT researchers how adopting a PCT framework and
methodology will help them to investigate and understand the phenomena with
which THEY grapple. For many research problems the truth or falsity of PCT
is simply irrelevant.

Perhaps so, but I am inclined to think that in this case the mouse must
swallow the elephant. To the extent that the present mainstream science is
misguided (nomothetic-idiographic confusion, experimental-statistical
felonies), we need not try to move into it, for it is inadequate by any
standard, for any purpose. As for the phenomenon of control, we must
demonstrate that it occurs, that it is ubiquitous, and that it is not
addressed by mainstream science. After that, it is up to "the other guys" to
get in line; _we_ must absorb _them_. No one ever said this would be easy.

. . .

It IS true that SOME research findings become trivial side-effects when
viewed from the PCT perspective, but this conclusion in no way applies to
ALL research not designed with PCT in mind.

Perhaps not to "all" non-PCT research, but I would say to practically all of
it, insofar as we are trying to document and explain the ubiquitous
phenomenon of control. I believe most data are irrelevant to understanding
control, if they are gathered on groups in research aimed at discovering how
stimuli, or neuro-cognitive commands, control behavior. At best, the data
probably reveal irrelevant (to the subject) side effects of what the subject
was controlling.

Many of these findings will in fact have direct relevance to PCT
(perceptual studies, for example).

The truth of this claim will be determined empirically. I do not assume that
the results of _all_ perceptual studies will be relevant to PCT. In fact, I
believe many of them will be irrelevant.

To gain acceptance of PCT as a general theory of behavior, we need to show,
wherever possible, how previous work "fits into" the PCT framework.

Wherever possible, yes; everywhere, no -- and the distinction must be drawn
rigorously. "Seeing relevance everywhere" is the path followed by some of
our more successful control theory "colleagues" -- the popularizers who have
bastardized the theory beyond all recognition and thereby achieved
publication, acceptance, and fame. Almost without exception, the titles of
their articles, chapters and books present control theory as a "framework,"
a "perspective," or a "viewpoint" on traditional topics. They have easily
made old ideas, even old fictions, "fit into" PCT.

Our job is to show people how to know control when they see it, how to test
for it when they think it might be present, and how to explain it when they
find it. There are too few of us to make traditional science over for its
adherents. Am I arrogant if I say that the multitudes on "the other side"
must do most of that work? If they get the point, they will do the work. If
they don't get the point, someone else will, eventually, and those new people
will do the work. It will happen some day. I am in no hurry. In spite of
general neglect from the mainstream, insights into the phenomenon of
intentional behavior have survived for millennia, nurtured by a few deluded
(and arrogant?) souls. During our turn on watch, we have two new resources:
Bill Powers's elegant insights, which have turned the old idea into a formal
model, and personal computers, which a few of us pretend we can afford to
buy out of our household budgets. No earlier keepers of the flame had those
two advantages (or spouses who reminded them that, even though it is all
for PCT, the previous computer was supposed to be "the last one I will
ever need to buy"). Come join the club.

Later,

Tom