starting from scratch

[William_T_Powers4]

[From Bill Powers (951010.0130 MDT)]

Bruce Abbott (951011.2350 EST) --

Bill Leach said it well but I want to repeat the idea. Why do
psychologists measure things like distances and speeds and directions,
and then use them to explain metaphors like imprinting and attachment?

     Output variables in chicks: peeping, movement. Peeping affects
     proximity through the action of the mother hen's control system,
     movement by closing the distance between visual representation of
     mother and (I believe) her sounds; pathways: visual, auditory.
     Additional inputs: sensation of warmth, physical contact with
     mother or others in brood (speeds restoration of error to zero):
     pathways: somatosensory.

That's what you would say now. Were those observations reported when the
study was published? Were any measurements made of the relationships
among these variables? Were disturbances applied in all possible
directions to identify these controlled variables, to prove that they
were actually under control? Or are you just offering plausible general-
idea interpretations?

     As I recall, the study examined the following behavior of chicks or
     ducklings or goslings (I don't remember which) that had been
     imprinted on an object whose motion could be readily controlled by
     the investigator. (It was mounted on an arm extending from a
     central pivot, which moved the object in a circular path through a
     circular corridore.) The imprinted birds followed the object as
     they would have followed their natural mother under normal
     circumstances.

Well, that's interesting. Was this study really done with multiple
chicks, or with one chick at a time? The way chicks follow their natural
mother, as I have observed many times (including pictures of goslings
following Konrad Lorenz), is in a line. That is, the first chick follows
the mother, the second chick follows the first chick, and so on, as in
the CROWD demo called "oneline." So it looks as if only the first chick
need imprint on the object; the others imprint on another chick. The
observer, however, who is hung up on the idea that the chicks imprint on
the mother, may have seen only the relationship between each chick and
the mother, and may not have tested to see what, in fact, each chick was
following. If all the chicks were following the mother, they would
cluster around at roughly the same distance from the mother (as in the
"guru" demo). If they were simply following a familiar moving object,
they would follow in a line. One way to test this would be to pull one
chick aside slightly with a thread; if the chick behind it followed the
deflected chick, the chick behind was following another chick, not the
mother.

Control of distance implies obstacle avoidance as well. Were the chicks
controlling for preventing collisions as well as for maintaining
distances? Were distances or velocities under control? Was direction
under control as well?

If chicks imprint on any large moving object that is seen at the right
time, then presumably they will thereafter follow "any large moving
object." In other words, the controlled perception is the distance from
some large object that is moving. So the next question is whether a
different large moving object can be substituted. If not, the controlled
quantity has been misidentified: the chicks are maintaining something
else constant, not just the largeness or the relative distance.

Incidentally, if the chicks follow at a fixed distance from a moving
object, the object is not moving relative to the chicks. So perhaps
"moving object" is not the right concept in the first place. The object
moves mainly from the observer's point of view.

If imprinting is really specific to one moving object, then clearly more
perceptions than size and motion are being controlled; perhaps there are
also color, odor, markings, shape, and so forth. Each one of these
should be investigated, until it can be determined what the chick is
actually controlling. And when that is done, there will be no need to
invoke a metaphorical term like "imprinting" or "attachment." The chick
is not literally attached to the object; that is only a false appearance
created by the chick's control actions. And there is certainly no
evidence of "imprinting" of anything on anything else. If the chick
learns to control certain perceptual variables, all that is observed
will follow from that alone. What do the ideas of imprinting and
attachment add to that?

     However, the situation was then changed so that when the birds ran
     toward the object, it retreated from them faster than they could
     approach, and when they ran away from the object, it approached
     them faster than they were retreating. After some experience with
     this arrangement, the birds learned to move in the direction that
     would keep them within a specific distance from the object.

This was Wayne Hershberger's thesis experiment. He found that chicks had
a great deal of trouble solving this problem, and they did it mainly by
showing very abnormal behaviors. You seem to be talking about a
replication of Wayne's experiment, which found different results
(control of distance from the object, with no apparent difficulties).

This experiment shows another phenomenon, the ability to reverse the
sign of the output function when the sign of the environmental feedback
function reverses. The next logical experiment would be to switch back
and forth from the normal relationship to the reversed one, to see how
rapidly the chicks could change the internal sign of the control system.
This would give some information about a higher level of control system,
acting on the parameters of a lower-level system (as in Rick Marken's
experiments with reversals).

Dagc Forssell pointed out over the phone today that this reversal
phenomenon is a perfect proof that it is perception, not output, that is
under control.

The problem with these studies is that the object was to find out
something about the metaphorical phenomena of imprinting and attachment.
As a result, the REAL phenomenon, which is the learning of control
processes, was barely investigated. A great deal more could have been
learned if the experimenters had just abandoned those two vague concepts
and concentrated on studying controlled variables.

That's what I mean by starting from scratch. Abandon all the old
categories and start over by studying control processes. The more you
learn about control processes, the less use you will have for terms like
imprinting and attachment (except to communicate with people who still
believe they mean something real). You can still investigate chicks
following things, if that is what you want to investigate.

     Even Copernicus didn't demand that astronomers throw away their
     laboriously and meticulusly assembled maps of the heavens and start
     from scratch. Their conceptions, yes; the observations, no.

He did, however, demand that they throw away all their laboriously
assembled diagrams showing epicycles and deferents and all the concepts
they thought they were studying. The observations were simply records of
where the planets were relative to the stars at successive times. These
Copernicus kept. The rest went in the garbage can.

I recommend that we retain the records of the chicks' velocities and
positions relative to the moving objects at successive times. And throw
the rest in the garbage can. If we accidentally throw something useful
away, we will reinvent it anyway, only this time on solid grounds.

     It seems to me that the phenomena of attachment and loss, extending
     as they do from lowly chickens clear across to the human child and
     parent, have already demonstrated their dependence on specialized
     control systems designed by evolution for the purpose of keeping
     the child safely within its parents' protective influence.

I don't think that terms like attachment and loss have any place in a
scientific study of behavior. They are not phenomena; they are metaphors
and interpretations by an observer who chooses to see the same thing in
different behaviors. If they belong anywhere, it is at the END of the
study, where you try to interpret the actual findings for the layman who
knows only a non-technical vocabulary. You may actually find surprising
similarities between the control behavior of chicks and the control
behavior of human children. The idea of a scientific investigation is to
let such similarities come as a surprise, not to jump to conclusions
based on the human habit of classing different things together and
calling them by a single name.

I also don't think that evolution designs anything for any purpose.
"Keeping the child safely within its parents' protective influence" is
not a goal of a chicken or a chick, much less of evolution. You're
describing how a human being would see the _consequences_ of controlling
as the chicks do, but the chicks know nothing of those consequences.
They control only what they can perceive, and that does not include
verbal generalizations as far as I know.

     The benefits of this analysis are already being widely felt in
     clinical and other applied settings. It absolutely astonishes--and
     saddens--me to hear you say that you think such research is
     antithetical to PCT.

As I said, I'll take the observations, if they are actually adequate for
a study of control processes. Whether you consider the applications of
the analysis to be beneficial depends on how you interpret the effects.
I have never heard any psychological researcher claim that the
applications of his ideas to clinical settings were harmful or
irrelevant. You could just as well be talking about the enthusiasm with
which psychologists typically lap up the latest fad. Maybe there have
been benefits: I wouldn't know. But I would rather have someone other
than the originators of the ideas or the psychologists applying the
ideas evaluate the results.

     I suggest you read Bowlby's (1969) book and see whether I doesn't
     change your opinion.

OK, I'll get it through interlibrary loan. That will take a while.

···

-----------------------------------------------------------------------
Best,

Bill P.

[Bruce_Abbott]

[From Bruce Abbott (951011.2020 EST)]

Bill Powers (951010.0130 MDT) --
    Bruce Abbott (951011.2350 EST)

    Output variables in chicks: peeping, movement. Peeping affects
    proximity through the action of the mother hen's control system,
    movement by closing the distance between visual representation of
    mother and (I believe) her sounds; pathways: visual, auditory.
    Additional inputs: sensation of warmth, physical contact with
    mother or others in brood (speeds restoration of error to zero):
    pathways: somatosensory.

That's what you would say now. Were those observations reported when the
study was published? Were any measurements made of the relationships
among these variables? Were disturbances applied in all possible
directions to identify these controlled variables, to prove that they
were actually under control? Or are you just offering plausible general-
idea interpretations?

Ethologists beginning with Lorenz (and later, comparative psychologists)
have done a very good job of identifying the essential variables; I am not
going to attempt a review of all those studies here. The bulk of these
studies did not seek to identify the precise quantitative relationships one
would like to have for constructing a PCT model of the system, but they did
seek to determine the nature of the necessary inputs and even gathered some
data on the relationship of imprinting difficulty to the age of the bird
(which led to the discovery of a "critical" or "sensitive" period during
which imprinting was easy to achieve and following which imprinting became
increasingly difficult. With respect to goslings, Lorenz was able to serve
as the imprinted object simply by hunkering down onto his haunches, waddling
about in front of the birds, and imitating an adult goose's sounds during
the right time-period. Later studies showed that successes was greatly
facilitated by those sounds (and Lorenz was good at imitating them).

Whether all possible tests were conducted to identify the essential
variables I don't know. My initial statement on this subject was that
_some_ work in this direction had been done; I never claimed that anyone had
attempted a complete PCT-style study. Am I just offering plausible
general-idea interpretations? I don't think so. It's been a long while
since I was active in this area and my memory of it is not exactly fresh,
but I believe that the variable I noted have been studied and confirmed.

    As I recall, the study examined the following behavior of chicks or
    ducklings or goslings (I don't remember which) that had been
    imprinted on an object whose motion could be readily controlled by
    the investigator. (It was mounted on an arm extending from a
    central pivot, which moved the object in a circular path through a
    circular corridore.) The imprinted birds followed the object as
    they would have followed their natural mother under normal
    circumstances.

Well, that's interesting. Was this study really done with multiple
chicks, or with one chick at a time?

One chick at a time. Ethologists are not especially fond of group-based
statistical methodology.

The way chicks follow their natural

mother, as I have observed many times (including pictures of goslings
following Konrad Lorenz), is in a line. That is, the first chick follows
the mother, the second chick follows the first chick, and so on, as in
the CROWD demo called "oneline." So it looks as if only the first chick
need imprint on the object; the others imprint on another chick. The
observer, however, who is hung up on the idea that the chicks imprint on
the mother, may have seen only the relationship between each chick and
the mother, and may not have tested to see what, in fact, each chick was
following. If all the chicks were following the mother, they would
cluster around at roughly the same distance from the mother (as in the
"guru" demo). If they were simply following a familiar moving object,
they would follow in a line. One way to test this would be to pull one
chick aside slightly with a thread; if the chick behind it followed the
deflected chick, the chick behind was following another chick, not the
mother.

Chicks imprint on their mother AND on their broodmates. But you are right:
they do tend to follow each other as well as the mother as in the "oneline"
demo. I don't know whether they follow a specific broodmate when not first
in line behind the mother hen. However, if separted from mother by a short
distance, the chicks will all run toward her rather than maintaining a line
behind each other, so the rule seems to be "follow mom, but if there's
another chick already behind her, follow the other chick." Researchers did
not fail to notice this aspect of the chick' following behavior.

Control of distance implies obstacle avoidance as well. Were the chicks
controlling for preventing collisions as well as for maintaining
distances? Were distances or velocities under control? Was direction
under control as well?

Good questions, but I'm not familiar enough with the literature to provide a
definite answer.

If chicks imprint on any large moving object that is seen at the right
time, then presumably they will thereafter follow "any large moving
object." In other words, the controlled perception is the distance from
some large object that is moving. So the next question is whether a
different large moving object can be substituted. If not, the controlled
quantity has been misidentified: the chicks are maintaining something
else constant, not just the largeness or the relative distance.

Imprinting appears to be accomplished via an innate mechanism tuned to
identify certain simple but critical features in the chick's environment,
when found together in the same object, as its mother. Once this mechanism
"locks onto" a presumably appropriate object, the chick's perceptual
apparatus is focused on it and learning takes place: the chick identifies
other features that allow it to distinguish this particular variant from
similar ones. Thus under ordinary conditions the chick first identifies a
particular hen as its mother (the one that is moving around close by) and
then learns to distinguish her sight/sound/smell from that of all other hens.

Incidentally, if the chicks follow at a fixed distance from a moving
object, the object is not moving relative to the chicks. So perhaps
"moving object" is not the right concept in the first place. The object
moves mainly from the observer's point of view.

Initially the chick is not moving with respect to the object; it is during
this phase that imprinting takes place. After imprinting, the chicks
follow, but they are unable to track her movements precisely, so there is
constant relative movement between chick and hen even then, so long as the
hen keeps moving.

If imprinting is really specific to one moving object, then clearly more
perceptions than size and motion are being controlled; perhaps there are
also color, odor, markings, shape, and so forth. Each one of these
should be investigated, until it can be determined what the chick is
actually controlling. And when that is done, there will be no need to
invoke a metaphorical term like "imprinting" or "attachment." The chick
is not literally attached to the object; that is only a false appearance
created by the chick's control actions. And there is certainly no
evidence of "imprinting" of anything on anything else. If the chick
learns to control certain perceptual variables, all that is observed
will follow from that alone. What do the ideas of imprinting and
attachment add to that?

I doubt that the chick is controlling proximity to each of these features
independently. More likely the chick's brain is able to construct a
representation of its mother that includes many of these distinct features,
and recognizes her as a discrete object when that object presents the
appropriate signs in the right locations. However, we really have a great
deal more to learn about object perception before we can say how such
recognition is actually accomplished.

I'm not sure Mary would understand if you just up and told her that you no
longer feel attached to her. (;-> What does it mean to say that you feel
this attachment? Does it reduce to control of proximity to her, or is there
something more to be included in the meaning of this term? What the ideas
of imprinting and attachment add is a whole class of related changes in the
way the chick (or person) responds to separation from the "object of its
affections." Following behavior is only a single manifestation of this
change. What seems to be involved is at least one much higher-level system,
one of whose lower-level manifestations include a reference for proximity to
the caregiver(s). Among the higher-order perceptual manifestations of this
system in at least the larger-brained mammals may be this feeling-state we
humans call "love" (or at least one kind of love).

Ultimately we may be able to identify the relevant control systems and their
connections and interactions; beyond that point we may then discover the
precise anatomical representations of these mechanisms and their signals.
At that stage we will have reduced these phenomena variously placed under
the terms "imprinting" and "attachment" to a specific wiring diagram and a
set of system equations. Will we have eliminated love and a child's
affection for its parents, or explained them?

The problem with these studies is that the object was to find out
something about the metaphorical phenomena of imprinting and attachment.
As a result, the REAL phenomenon, which is the learning of control
processes, was barely investigated. A great deal more could have been
learned if the experimenters had just abandoned those two vague concepts
and concentrated on studying controlled variables.

That's what I mean by starting from scratch. Abandon all the old
categories and start over by studying control processes. The more you
learn about control processes, the less use you will have for terms like
imprinting and attachment (except to communicate with people who still
believe they mean something real). You can still investigate chicks
following things, if that is what you want to investigate.

But that is precisely what I do NOT want to investigate. By reducing (and
trivializing) the phenomena of attachment to "chicks following things," you
have eliminated precisely that which attracted researhers to the study of
these phenomena in the first place. YOU study chicks following things, if
it interests you; I want to know why some children cry when separated from
their parents, why children whose environements failed to offer an
appropriate object of attachment often fail to develop compassion and
empathy for others, why young children suddenly and permanently deprived of
their parents become dispondent and listless, why autistic kids sit and rock
their bodies precisely like rhesus monkeys deprived of a mother, and the
whys to a dozen other questions similar to those. How chicks control their
proximity to mother may be of some interest, but the question that really
burns is what the whole system, of which this behavior is merely a single
manifestation, normally does, what happens when the system fails to properly
develop, and what can be done to ameliorate the damage when it does.

Before you conclude that I just don't get it, let me try to summarize this
last point of yours and offer some thoughts about it. Your proposal, your
program, if you will, is to start afresh at the most fundamental levels
(e.g., simple tracking experiments) and through a long, patient series of
studies to gradually build an understanding of the brain's control systems
from the bottom up. At each step what appear on the outside to be rather
complex phenomena involving perhaps central planning and coordination may
(you expect, will) be shown to be reducible to the actions of specialized
control systems acting on specific perceptual inputs and (except at the
bottom level) outputing reference values and setting lower-level system
parameters such as gain. Knowledge of these functional arrangements will
then guide the search for their physical representations in the brain.
Ultimately the highest levels involving the slowest-acting systems engaged
in the control of the high-level system goals such as self-esteem will be
understood in the same way that electronic circuits are now understood, as
sets of dynamical systems equations. In this distant future time there will
be no need for metaphorical constructs or reference to subjective states as
the entire system will be fully described in purely mathematical terms in
much the way that the turbulent flow over an aircraft's wing during stall
can today be so described and modeled via computer.

I look forward to that day. At the same time, I don't see any reason to
disparage the efforts that have been made thus far and the progress that has
been achieved in coming to grips with some important and pressing issues
relating to mind, brain, and behavior. Ptolemy's system was fundamentally
wrong (as was Newton's), but it provided a basis for computing values
essential to ship navigation and thus represented a quantum leap over what
had come before it. Much of our current understanding of brain and behavior
will need to be drastically revised in the light of new knowledge, perhaps
the fundamental understandings supplied by programmatic research on PCT, but
many important insights about relationships such as those uncovered in
attachment research will stand even when the alchemy by which the original
observations were initially understood has been replaced by this new
chemistry of the mind. They will be explained, but not explained away.

Regards,

Bruce

[Bill_Leach1]

<[Bill Leach 951012.00:06 U.S. Eastern Time Zone]

[Bruce Abbott (951011.2020 EST)]

I am getting to where even the hint of the possibility of a debate
between you and Bill results in me having joyous anticipation (as S-R
sounding as that may be).

This latest one has resulted in both of you presenting "your respective
cases" with elegance. Your last three paragraphs were particularly good,
in my opinion.

The shame is that there are so few scientists in the behavioural sciences
with both an understanding of control theory (and many of its'
implications) and genuine intellectual honesty. It would be of great
benefit to behavioural science if _only_ the fundamental understanding of
control theory were more widespread. Where control theory can not be
applied directly at least trying to think in terms of control system
interaction would help greatly.

Bill is right I think except that we can't just give up on everything
else and wait. But what we can do, is try to be honest. PCT definately
CAN NOT tell us what _is_ going on for most of the sort of work that you
are talking about. The best that it can do is provide rather vague
suggestions unless one can then conduct further research to begin
checking out each of the possibilities (a matter that could well not be
practical even if attempts should be made in that area). What would help
greatly though is that for almost all work there is a "whole world" of
ideas about "what is going on that can be discarded with little more than
just the recognition that a control system is involved. That is, PCT can
tell us a great deal about what IS NOT going on.

-bill

[William_T_Powers4]

[From Bill Powers (951012.0530 MDT)]

Bruce Abbott (951011.2020 EST) --

It may be that we are going to arrive at a real agreement. If we do, it
will be largely because of your ability to stay focused on the important
issues without taking offense at criticisms. I don't say that
condescendingly; it's an ability that I wish I had had through my years
of trying to get PCT across to psychologists. What you are doing will be
as good for PCT as I hope PCT will some day be for psychology.

I find that the Bowlby book is available at Fort Lewis College; you
didn't tell me it was a 3-volume monster! I will get started on it
sooner than anticipated. There's a later book there, too.

Back to the fray.

     By reducing (and trivializing) the phenomena of attachment to
     "chicks following things," you have eliminated precisely that which
     attracted researhers to the study of these phenomena in the first
     place. YOU study chicks following things, if it interests you; I
     want to know why some children cry when separated from their
     parents, why children whose environements failed to offer an
     appropriate object of attachment often fail to develop compassion
     and empathy for others, why young children suddenly and permanently
     deprived of their parents become dispondent and listless, why
     autistic kids sit and rock their bodies precisely like rhesus
     monkeys deprived of a mother, and the whys to a dozen other
     questions similar to those.

My intent is not to trivialize, nor is it reductionistic. This
appearance is created, I think, when I argue for going back to basic
observations and building according to a new plan. Ultimately, I hope
that we will be able to use PCT to deal with experience in a way that is
even richer in human content, even more relevant to everyday life, than
the way that is currently dominant in the psychology that you describe.
But I think that by the time we are able to return to that level of
discourse, the images will all be different, the metaphors will be more
disciplined and less ideosyncratic, and the understanding will be more
reliable.

What I don't trust about the paragraph just cited is your assumption
that you know what is common to chicks, monkeys, and human beings. It
may be that when autistic children sit and rock, what they are doing
internally is not "precisely" what rhesus monkeys deprived of their
mothers do; it may be that the observer is being deceived by a
similarity of gross behavior, and that the internal processes are quite
different. There are certain problems of survival that all organisms
must either solve or be equipped from birth to deal with, but there is
no reason to think that organisms as different as chicks, infant
monkeys, and human babies solve them the same way, despite appearances.
If we draw too strong an analogy based on subjective impressions of
similarity in behavior, we could be missing the essential differences,
and come to very wrong conclusions, such as a conclusion that all we
need to know to understand human behavior we can learn from studying
chickens or rats.

···

----------------------------------
It seems to me that there is an ethical and logical dilemma in using
lower animals to learn things that apply to human behavior. The
rationale behind using animals is that we can't do certain experiments
on human beings -- we can't, for example, deliberatly isolate babies
from the care they need, to show the importance of the parents in the
normal maturation of the baby. Our reasons for not being able to do such
experiments vary; for some, the reasons are ethical or moral; for
others, obviously, the reasons are simply to avoid retribution.

We can, however, use "animal models," because such manipulations of
animals do not violate ethical and moral precepts. Animals do not
experience such things as human beings do, if they experience them in
any conscious way at all. It is perhaps regrettable that animals must
suffer to provide us with essential information, but their suffering is
not comparable to human suffering.

On the other hand, when one does such experiments the justification is
that by doing them we learn about human nature because human beings are
also animals. So now we must begin arguing on the basis of essential
similarities of lower animals to human beings. If these similarities
were not very close, then we would not be learning much about human
nature by manipulating animals. By the time we have finished showing the
relevance of animal experimentation to human behavior, we have erased
all the justifications for using animals rather than human beings as our
subjects (unless we are among those who need no justification, realizing
that there isn't much the animals can do about it by way of getting
even).

More likely, since this is a conflict, we would arrive at a compromise
in which animals retain just enough of the right differences from human
beings to permit using them in any experiments we please, while still
retaining enough similarities of the right kind to permit generalizing
from animal behavior to human behavior. However, what suffers in this
compromise is the truth: we are choosing a conclusion that comes as near
as possible to letting us have it both ways, but which is also, for the
same reasons, as wrong as it can be on both sides of the question.
-----------------------------
I am all in favor of the naturalistic approach to behavior which we find
in ethology. I only wish it were more naturalistic and less entangled
with theory. I wish that animals could be studied for what they are,
without reading patterns into their behavior that are of proven
importance only to human beings.

What seems to be missing from the ethological approach to imprinting is
any consciousness of the experimenter as a human observer, operating out
of human characteristics. If there is anything new that PCT brings to
the study of human and animal nature, it is a clear picture of the role
that human perceptions play in determining what we will experience of
the world, including the other creatures in it. PCT is a self-reflexive
theory; it always applies to the observer as much as the observed. In
PCT research there are no disembodied observers; all observers are made
of flesh and blood, muscle and brain. Whatever properties are assigned
or denied to human subjects must also be assigned or denied to human
observers. This consideration, even if not the normal focus of
attention, is always in the background; whatever we say about human
behavior is always monitored in terms of its applicability to ourselves
who are doing the saying.

This leads to an unspoken understanding that what we observe are always
_appearances_ rather than realities. Even when we are most
enthusiastically holding forth about the patterns we see in nature, we
are always wondering how we are going to establish that these patterns
have some justification outside our own urge to read patterns into
everything. This is why there is such an emphasis on challenging
theoretical statements, putting them to tests which make the outcome as
independent as possible of our own interpretations and wishes. This is
why Rick Marken, Tom Bourbon, and I are always thinking up experiments
and demonstrations, and then inviting others to try them out to see if
they come to the same conclusions, to see if the same results are
obtained when others are in charge of the apparatus. This emphasis on
challenging and testing and demonstrating and double-checking comes from
our acute consciousness of our own subjectivity, and the difficulty of
separating our interpretations from the natural course of events --
separating higher-level interpretations from reports of lower-level
experiences. One has to internalize the abstract notion that behavior is
indeed the process by which we control our own perceptions in order to
develop the healthy sense of insecurity that leads to such an insistence
on replication and testing.

It is the job of the naturalist to report appearances at the lowest
level of perception that is practical, leaving out all higher-level
interpretations where alternatives are possible. But human beings,
unless they have become unusually aware of the subjectivity of
experience, find it difficult to do this. Few even realize that it is
possible. In such a simple matter as observing the behavior of chicks
following a hen, observers are seldom able to separate their own higher-
level interpretations from a simple report of the configurations,
events, and relationships that are observed. They report that the chicks
follow along behind the mother, not realizing that this is the
appearance only from their vantage point; from the chick's vantage
point, the proximity of the mother is being maintained in a certain
state that varies around some average stationary state, with the chick
itself as the unmoving center of the world. From the chick's point of
view, the problem is not to follow a moving object, but to keep the
object from moving. When a chick succeeds in keeping an object from
moving, we, on the outside, observe that sometimes the chick follows the
object. But when the object itself can't be stabilized, the only way to
keep its appearance the same in the perceptual field is to use the motor
apparatus that moves the observer, the chick. That is what makes it seem
to us that the chick is following the hen.
-----------------------------------
     Before you conclude that I just don't get it, let me try to
     summarize this last point of yours and offer some thoughts about
     it. Your proposal, your program, if you will, is to start afresh
     at the most fundamental levels (e.g., simple tracking experiments)
     and through a long, patient series of studies to gradually build an
     understanding of the brain's control systems from the bottom up.
     At each step what appear on the outside to be rather complex
     phenomena involving perhaps central planning and coordination may
     (you expect, will) be shown to be reducible to the actions of
     specialized control systems acting on specific perceptual inputs
     and (except at the bottom level) outputing reference values and
     setting lower-level system parameters such as gain. Knowledge of
     these functional arrangements will then guide the search for their
     physical representations in the brain. Ultimately the highest
     levels involving the slowest-acting systems engaged in the control
     of the high-level system goals such as self-esteem will be
     understood in the same way that electronic circuits are now
     understood, as sets of dynamical systems equations. In this
     distant future time there will be no need for metaphorical
     constructs or reference to subjective states as the entire system
     will be fully described in purely mathematical terms in much the
     way that the turbulent flow over an aircraft's wing during stall
     can today be so described and modeled via computer.

This is more or less correct except for the part about doing away with
metaphorical constructs or reference to subjective states. The making of
metaphorical constructs and the observations of subjective states are
part of the normal operation of a human brain. To do away with them we
would have to lop off our brains at the thalamus. What I want to do away
with are metaphors and descriptions of subjective states that are based
on the deep-seated acceptance of wrong theories about how the human
system works. A metaphor like "attachment" accounts for the behavior of
a chick in the same way we would account for it if the chick were
fastened to the hen by a string. The image of attachment is simply the
wrong image. The chick follows the hen, the lover follows the object of
love, not because there is some attachment dragging the pursuer around
like a balloon, but because of active control processes designed to make
the world become closer to what the pursuer wants to experience. I love
Mary (since you bring it up) not because there is some umbilical
attachment between us that hurts if stretched too far, but out of a
voluntary wish for her happiness and well-being and an appreciation of
all that she does for selfish me, not to mention a hope that she will
choose to continue doing such things. I don't claim that loving is a
conscious act -- remember what Isaac Kurtzer has been saying -- but it
is a consequence of the desires of the lover, not of forces in the
external world. The metaphors we would choose under PCT would be very
different from those that have been chosen under other theories. We
would speak of "attachment" only if we were sure it would be taken as a
sort of in-joke.

I think you would understand better what my objections to psychological
theories are if you would just sort out the metaphors that are used and
ask yourself how they would sound if you took them literally. The
language we have all learned to speak has grown out of long centuries of
belief in a causal model of behavior. Our metaphors freely hand out
responsibility for behavior to everything in the universe but the
behaving system itself. What we need are metaphors that recognize the
properties of organisms as control systems. Metaphors like "controlling
perceptions," which can be taken literally without changing their
meaning, and also offer a nice pun to see where the listener is coming
from.
-----------------------------
As to the worth of current research and applications, I think that is
probably a subject that I am ill-advised to pursue (see? somebody else
made me pursue it, through advice). There is no way to introduce a
fundamentally new approach to behavior without at least indirectly
hinting that there is something about the old approach that needs
improvement. I have, in fact, tried to simply introduce PCT and methods
and interpretations to which it leads (see? I didn't lead, PCT did), but
the psychologists who have heard such presentations had no hestitation
in telling me that I had missed the entire point, that I didn't
understand scientific research, that I didn't know about any of the
important work that was going on, and that nobody believed in my theory
anyway. I'm talking about HOSTILITY, man. I don't have to spell out the
fact that if the ideas behind PCT are true, then the ideas behind
conventional psychology are probably not true. That's the first thing
that psychologists have picked up about PCT: it is a threat to their
beliefs and livelihoods. It is an interruption of their work, which is
just on the verge of an important breakthrough Real Soon Now. Or at
least a publication that will extend their employment for another year.

I confess that I have often met hostility with hostility, attack with
attack. It takes a conscious effort for me to just let it pass. Letting
it pass is hard to do, because doing so means marking down another
skirmish lost, another effort wasted. I want to grab them by their silly
throats and yell "GODDAMMIT YOU POMPOUS IDIOT CAN'T YOU JUST LISTEN LONG
ENOUGH TO FIND OUT WHAT I'M TALKING ABOUT?"

I have not actually tried that method, since even I can predict that it
would not get me what I want. However, perhaps you can understand that I
occasionally have an urge to try it out on people who are trying to be
on my side.
-----------------------------------------------------------------------
Bill Leach (951012.0006 EDT) --

I really appreciate your supportive remarks about the current
interchange between Bruce and me. You are supporting progress, not
taking sides. You're another one who is good at the Big Picture
viewpoint.
----------------------------------------------------------------------
Best,

Bill P.

[Bruce_Abbott]

[From Bruce Abbott (951012.1635 EST)]

Bill Powers (951012.0530 MDT) --

It may be that we are going to arrive at a real agreement. If we do, it
will be largely because of your ability to stay focused on the important
issues without taking offense at criticisms. I don't say that
condescendingly; it's an ability that I wish I had had through my years
of trying to get PCT across to psychologists. What you are doing will be
as good for PCT as I hope PCT will some day be for psychology.

I suspect that we are not as far apart on these issues as it may seem from
our exchanges. In debates like these it is necessary to stake out a clear
position; if I were to attempt a complete statement of my views on any one
of these positions I'd have to go on for pages and those pages would be
filled with qualifications. As for the rest, there are two of us in these
exchanges and it is my perception that you have always conducted yourself in
a gentlemanly and scholarly manner. I'm just trying to maintain the same
standards.

My intent is not to trivialize, nor is it reductionistic. This
appearance is created, I think, when I argue for going back to basic
observations and building according to a new plan. Ultimately, I hope
that we will be able to use PCT to deal with experience in a way that is
even richer in human content, even more relevant to everyday life, than
the way that is currently dominant in the psychology that you describe.
But I think that by the time we are able to return to that level of
discourse, the images will all be different, the metaphors will be more
disciplined and less ideosyncratic, and the understanding will be more
reliable.

I've always suspected that your apparent rather uncategorical rejection of
current psychological research findings and methods is at least partly
tactical (the other part arises from an appreciation of what one can and
cannot correctly deduce about individual living control systems from the
standard methods usually employed). Certainly one way to get people to try
the PCT approach to research is to assert that current methods are
inappropriate, misguided, and misleading. The danger of taking a too
extreme position on this, in my judgment, is that there are just too many
examples of research using these methods that have provided important and
useful information (even though there is probably an equal number of
examples where these same methods, applied to different problems, have
produced just the kind of nonsense you so rightly rail against). Thus, for
experienced researchers in a given area, the claim that such methods are
useless appears utterly contradicted by their own experiences. My
preference therefore is to take a more moderate view, which is that these
methods can produce useful general information (when used properly and for
answering the kinds of questions for which these methods are at least
adequate). [What researchers need to be better educated about is what these
methods really are capable (and more importantly, NOT capable) of doing.]
But for discovering the detailed functional organization of these complex
living, behaving multilayered control systems, it must be emphasized, these
methods need to be replaced by the systematic, individual-centered approach
you advocate. On that we agree.

What I don't trust about the paragraph just cited is your assumption
that you know what is common to chicks, monkeys, and human beings. It
may be that when autistic children sit and rock, what they are doing
internally is not "precisely" what rhesus monkeys deprived of their
mothers do; it may be that the observer is being deceived by a
similarity of gross behavior, and that the internal processes are quite
different. There are certain problems of survival that all organisms
must either solve or be equipped from birth to deal with, but there is
no reason to think that organisms as different as chicks, infant
monkeys, and human babies solve them the same way, despite appearances.
If we draw too strong an analogy based on subjective impressions of
similarity in behavior, we could be missing the essential differences,
and come to very wrong conclusions, such as a conclusion that all we
need to know to understand human behavior we can learn from studying
chickens or rats.

This is certainly a valid concern; the antidote is careful research. I view
these cross-species similarities as tentative hypotheses that must be
examined closely in the light of empirical evidence. These hypotheses are
derived from neuroanatomy and evolutionary theory. We know that certain
aspects of brain structure and wiring have been highly conserved over the
course of evolution: they are essentially the same whether you are examining
the brains of chickens, rats, cats, dogs, chimpanzees, or humans, differing
only in size (both absolutely and relative to the sizes of other structures,
such as the cerebral cortex). These ancient structures appear to serve the
same functions and use the same neurotransmitters in all these species.
Over the long course of evolution these structures have been built upon,
like an old farmhouse that has undergone successive remodeling through the
addition of new rooms, yet still contains the old, original rooms still for
the most part serving their old purposes. This evident conservatism offers
some hope that, at least with respect to the functions served by these
ancient structures, what we learn about imprinting in chicks will help us in
a rather direct way to understand the functions and mechanisms of homologous
structures in us. Furthermore, if certain functions emerged early and
continued to be adaptive during the long course of mammilian evolution, one
would expect that such solutions would be preserved the thus that there
would have been no need for the emergence of independent solutions to the
same problem, as was evidently the case for flight (which emerged
independently in insects, reptiles/birds, and mammals). Still, one must
take such notions as hypotheses rather than established fact until the
evidence warrants such a conclusion.

The dilemma you note regarding animal research is a very real one and has
been pointed out previously by "animal rights" activists whose goal is to
eliminate all human use of all animals for any purpose whatsoever. It
certainly is a troubling one for me, one I have given considerable thought
to. If a resolution of this dilemma is possible, it must reside in the
conservation of brain structure just discussed, or even more generally in
the limited number of general solutions to certain problems faced by all
living things. For example, consider what can be learned about neural
"control" of movement just by studying the anatomical and functional
organization of the spinal cord/somatic muscle system. What we learn about
that complex of intermeshing servomechanisms in rats and chickens seems to
apply directly to the homologous system in man (even though there are some
differences as well, that must be taken into account). It is not necessary
for the rat or chicken to have mental capacities on a par with those of
humans before we can justify applying this knowledge toward understanding
how the human spinal systems work, nor does the existence of this
organization in rats and chickens necessitate our adopting the view that
rats and chicks think and feel as we do.

Evolutionary theory teaches that conscousness and self-awareness did not
magically appear when the first true human being was born, but were in all
probability features of the functioning of other brains before ours, and
probably can be found in our nearest relatives and perhaps even in some who
are not so near. As one moves from the study of chicks and rats to dogs and
monkeys and primates, the findings as to the operation of higher brain areas
become more direcly applicable to the human brain and it becomes
correspondingly more difficult from an ethical viewpoint to justify the
necessary experiments.

What I want to do away
with are metaphors and descriptions of subjective states that are based
on the deep-seated acceptance of wrong theories about how the human
system works. A metaphor like "attachment" accounts for the behavior of
a chick in the same way we would account for it if the chick were
fastened to the hen by a string. The image of attachment is simply the
wrong image. The chick follows the hen, the lover follows the object of
love, not because there is some attachment dragging the pursuer around
like a balloon, but because of active control processes designed to make
the world become closer to what the pursuer wants to experience.

I'm not sure that this is such a serious problem in this case: I don't think
too many people would view emotional attachments in this literal sense of
being pulled around by a string, any more than a physicist would be led to
believe that an electron has some kind of desire to be close to a proton by
the use of the word "attraction" to denote the effect of the electron's and
proton's opposite charges. To discuss a phenomenon we believe to have some
generality, we need labels for convenient reference. Here we have a change
developing in the young chick's brain, following a specific experience, and
resulting in the appearance of specific, well-defined behaviors under
specific, well-defined conditions; the most obvious manifestations are that
the chick attempts with all its ability to stay close to some particular
object and manifests what appears to we humans as distress when that contact
is broken. If we have to call this phenomenon something, what label should
we apply to it? To me, attachment seems as good as any for communicating
the essense of what I am studying. But let's assume I accept your argument
for avoiding such content-laden and potentially misleading metaphorical
labels. With what do I replace the term "attachment?" What else can do as
good a job at conveying the entire set of related changes that occur in the
chick's observable behaviors under various circumstances after
what-ever-it-is has occurred? We could invent a new term based on ancient
Greek or Latin cognates, I suppose. But if we did, which term do you think
would give your grant proposal the better chance of being funded?

Regards,

Bruce

[William_T_Powers4]

[From Bill Powers (951012.1605 MDT)]

Bruce Abbott (951012.1635 EST) --

     I suspect that we are not as far apart on these issues as it may
     seem from our exchanges.

Yes.

     I've always suspected that your apparent rather uncategorical
     rejection of current psychological research findings and methods is
     at least partly tactical (the other part arises from an
     appreciation of what one can and cannot correctly deduce about
     individual living control systems from the standard methods usually
     employed).

That is part of it; we have had terrible results from people trying to
amalgamate PCT with the work they had been doing previously. But a great
deal of my problem comes as soon as the researcher gets beyond stating
what he did and what he found, and starts drawing conclusions. These
conclusions invariably rest on S-R or cause-effect assumptions of one
form or another, and for me that simply negates whatever was good about
the work.

     We know that certain aspects of brain structure and wiring have
     been highly conserved over the course of evolution: they are
     essentially the same whether you are examining the brains of
     chickens, rats, cats, dogs, chimpanzees, or humans, differing only
     in size (both absolutely and relative to the sizes of other
     structures, such as the cerebral cortex).

You have to be very careful about saying that these structures are "the
same." Some time back, Gary Cziko provided some examples of
neuroanatomical research that showed VERY LARGE differences in the
wiring of individuals from the SAME species. It's extremely hard to
judge similarity of function from similarity of location, color, neuron
forms, or chemistry.

     These ancient structures appear to serve the same functions and use
     the same neurotransmitters in all these species. Over the long
     course of evolution these structures have been built upon, like an
     old farmhouse that has undergone successive remodeling through the
     addition of new rooms, yet still contains the old, original rooms
     still for the most part serving their old purposes.

This is another point about which you have to be very careful. We tend
to forget that an organism which has only those "ancient" structures has
been evolving just as long as we have, and that evolution probably has
produced radical changes from the actual ancient structures. This is an
especially shakey argument because we have no idea what the ancient
structures were back when they were the latest current rage. Fossils do
not preserve the soft parts or the neural organization.

···

--------------------------
     It is not necessary for the rat or chicken to have mental
     capacities on a par with those of humans before we can justify
     applying this knowledge toward understanding how the human spinal
     systems work, nor does the existence of this organization in rats
     and chickens necessitate our adopting the view that rats and chicks
     think and feel as we do.

So as long as you're just studying the spinal functions, you can forget
about how the animal feels or what it thinks about the consequences to
it? The animal-righters do have some points to make, you know.

However, in the case of chicks and separation anxiety, it seems to me
that you _are_ trying to compare higher functions, and that you _do_
have a dilemma: if what you are finding informs our understanding of
human experiences of the same kind, then you really shouldn't be doing
that. The only real answer is to say that there's nothing the animals
can do about it, and you consider human welfare to take priority over
animal welfare. MacDonald's does it all the time, why not psychologists?

     Evolutionary theory teaches that conscousness and self-awareness
     did not magically appear when the first true human being was born,
     but were in all probability features of the functioning of other
     brains before ours, and probably can be found in our nearest
     relatives and perhaps even in some who are not so near. As one
     moves from the study of chicks and rats to dogs and monkeys and
     primates, the findings as to the operation of higher brain areas
     become more direcly applicable to the human brain and it becomes
     correspondingly more difficult from an ethical viewpoint to justify
     the necessary experiments.

All speculation, my friend, and you know it. There are some hard
questions here to which nobody has any answers.
-----------------------------------
RE: attachment

     I'm not sure that this is such a serious problem in this case: I
     don't think too many people would view emotional attachments in
     this literal sense of being pulled around by a string, any more
     than a physicist would be led to believe that an electron has some
     kind of desire to be close to a proton by the use of the word
     "attraction" to denote the effect of the electron's and proton's
     opposite charges.

But people DO view attachments as something one person does to another
person. Unlike the physicist, they have no deeper layer of theory to
fall back upon to say what they really mean: f = m1*m2/r^2. When the
underlying theory says yes, it is perfectly true that stimuli from the
environment determine your behavior, the term "attachment" takes on a
very explicit meaning: you are being dragged around by stimuli from the
environment like a balloon.

Words like attachment refer to classes of behavior that are important to
people. No argument about that. But the particular word we have
inherited was assigned by people who didn't know diddly-squat about how
behavior works, and the chances are that they really believed there was
some mysterious bond floating in the air and connecting people together.
These are the same people who gave us "looking at" to mean receiving
optical information from the environment.

When we're talking among ourselves and aren't worried about
misunderstandings about the underlying theory, we can use terms like
attachment to designate a general phenomenon. But in doing so, we know
very clearly that there is no actual attachment, no physical link
holding people together. I agree with you that inventing new terms for
everything is impractical and wouldn't help communicate what we mean to
people who don't already know what we mean. This is a real problem,
though, because there are some terms we just have to abandon, like
"stimulus" and "response," which are very explicitly tied to a theory
antithetical to PCT. When you say "response" to a psychologist, that
psychologist is not going to hear "action that prevents a disturbance
from altering a sensory input."

     ... the most obvious manifestations are that the chick attempts
     with all its ability to stay close to some particular object and
     manifests what appears to we humans as distress when that contact
     is broken. If we have to call this phenomenon something, what
     label should we apply to it? To me, attachment seems as good as
     any for communicating the essense of what I am studying.

But isn't that only because you grew up for years believing that there
was some actual kind of attachment at work? If you now understand PCT,
whenever you use that term, you should feel a little discomfort, an urge
to explain that you don't really mean it the way it sounds. When you
start becoming conscious of the load of old theories that is carried by
words like this, you'll start to become like me, and begin to look
around for better ways of saying what you mean.

     With what do I replace the term "attachment?" What else can do as
     good a job at conveying the entire set of related changes that
     occur in the chick's observable behaviors under various
     circumstances after what-ever-it-is has occurred?

How about X? All you need is a symbol to remind people of the phenomenon
you're talking about. Of course a unique symbol would be better. Buy why
would you say that this particular symbol does an especially good job at
convenying the phenomenon, when it actually suggests something that
doesn't exist? Isn't that simply because you have accepted what it
suggests?
-----------------------------------------------------------------------
Best,

Bill P.

[Richard_Marken]

[From Rick Marken (951012.2300)]

Bruce Abbott (951011.1425 EST) --

there is an important difference between PCT the theory (and its
implications) and certain attitudes and conclusions held by some of its
major proponents.

It depends on which "attitudes and conclusions" you're talking about.
For some attitudes and conclusions this is true; for others, it is not. For
example, people who understand the basics of PCT can certainly hold different
attitudes and conclusions about the best music to play; but these same people
can't honestly hold different attitudes and conclusions about the value of
conventional behavioral research.

When you understand the basics of PCT you know that conventional research
methods are based on a mistaken notion of the nature of behavior itself.
Behavior is not (as conventional methods assume) the activities that an
observer sees; it is the perceptions that an organism controls. My "mind
reading" demo shows what this means; when you watch people doing this
demo you cannot (except by chance) tell what perceptions they are
controlling, even though you are looking at their visible behavior. The
computer can tell because it applies The Test; the computer does "mind
reading" by looking past the visible behavior to the perceptions that are
under control.

Bruce Abbott (951012.1635 EST)

The danger of taking a too extreme position on this, in my judgment, is
that there are just too many examples of research using these methods that
have provided important and useful information (even though there is
probably an equal number of examples where these same methods, applied
to different problems, have produced just the kind of nonsense you so
rightly rail against).

The PCT view of conventional research is not a "position" and it is not
"extreme". Once you know that organisms are control systems controlling
their own perceptions you know that what you see these organisms doing is
just your interpretation of the side effects of this control process. You
can then see that all research based on the conjventional view of behavior
is neither useful nor nonsensical; it is simply the wrong way to find out
about control This is not an extreme position; it is a testable statement
of a fact about the nature of control systems.

Bill Powers said:

If we draw too strong an analogy based on subjective impressions of
similarity in behavior, we could be missing the essential differences,

Bruce Abbott:

This is certainly a valid concern; the antidote is careful research.

The antidote is not careful _conventional_ research; it is a completely
different approach to research -- one aimed at identifying controlled per-
ceptual variables. The more carefully you do conventional research, the more
precisly the results of your research miss the point. The point is that
organisms control perceptual inputs relative to internally specified
references. The goal of most conventional research is to identify the
variables (internal and external) that control observed behavior. It provides
no systematic information about the perceptual variables that organisms
control.

Conventional psychologists have been seduced by the ease with which they
can see fascinating appearances in the behavior of organisms; it is easy to
see many wonderful things in "emitted" behavior: imprinting, affiliating,
dominating, socializing, etc. In many ways the conventional psychologist is
the poor man's version of the great novelist who can see Homeric tales
in the daily rountine of a cuckolded Dublin Jew. I can see why one would
be reluctant to give up the rich mythology of conventional behavioral
science for the elegant simplicity of perceptual control theory. Yet the
fascinating stories we read into observable behavior are as irrelevant as the
dramatic profanity spelled out by the hand using the rubber band to control
the "profanely" disturbed knot.

There is really no way to prove that the conventional approach to behavioral
research is wrong. It is only wrong if you are willing to accept the
possibility that organisms are living control systems and that, therefore,
the behaviors you see -- no matter how fascinating and seemingly profound --
are just your perceptual interpretation of the side effects of perceptual
control. If you are not willing to accept this possibility, then you will
be happy to take the appearance of behavior at face value -- and be carried
along by the fascinating statistical relationships between some appearances
and others. And you will never start the process of testing the PCT model
of living systems.

Demonstrations of the controlling done by humans have led me to tentatively
accept the possibility that organisms are perceptual control systems. The
only way to test this possibility is by doing research aimed at identifying
controlled variables and the means used to control them. The findings of
conventional research are relevant to this process only inasmuch as they
lead to hypotheses about perceptions which, if controlled, would lead
to the behavioral appearances that are the data of the conventional research.

Now, back into hibernation

Rick

[Bruce_Abbott]

[From Bruce Abbott (951013.1245 EST)]

Bill Powers (951012.1605 MDT) --
    Bruce Abbott (951012.1635 EST)

    We know that certain aspects of brain structure and wiring have
    been highly conserved over the course of evolution: they are
    essentially the same whether you are examining the brains of
    chickens, rats, cats, dogs, chimpanzees, or humans, differing only
    in size (both absolutely and relative to the sizes of other
    structures, such as the cerebral cortex).

You have to be very careful about saying that these structures are "the
same." Some time back, Gary Cziko provided some examples of
neuroanatomical research that showed VERY LARGE differences in the
wiring of individuals from the SAME species. It's extremely hard to
judge similarity of function from similarity of location, color, neuron
forms, or chemistry.

Fortunately we have more to go on than neuroanatomy and neurochemistry; for
example, brain stimulation studies conducted (with their permission!) on
people undergoing brain surgery and studies of the aftermath of localized
destruction of brain tissue by tumor or accident often support conclusions
drawn from animal studies. For example, certain nuclei of the brainstem
identified in studies of the cat as critical for certain aspects of
slow-wave and REM sleep turn out to be involved in those same functions in
humans, and stimulation of certain parts of the amygdala (a structure of the
limbic system) in humans activates an emotional state of trepidation;
stimulation of the analogous area in rats produces changes in the rat's
behavior that, to an outside human observer, appear to be manifestations of
fear. This is not to claim, of course, that such homologies are always
found, but only that it is often possible to draw conclusions about the
general functional characteristics of brain structures in humans from
studies of the homologous structures in animals even as distantly related to
humans as rats and chickens.

    These ancient structures appear to serve the same functions and use
    the same neurotransmitters in all these species. Over the long
    course of evolution these structures have been built upon, like an
    old farmhouse that has undergone successive remodeling through the
    addition of new rooms, yet still contains the old, original rooms
    still for the most part serving their old purposes.

This is another point about which you have to be very careful. We tend
to forget that an organism which has only those "ancient" structures has
been evolving just as long as we have, and that evolution probably has
produced radical changes from the actual ancient structures. This is an
especially shakey argument because we have no idea what the ancient
structures were back when they were the latest current rage. Fossils do
not preserve the soft parts or the neural organization.

Which makes it all the more amazing to find these functional parallels in
homologous structures. You'd have to assume either that this is a
coincidence of parallel evolution or that the functional significance of
these structures has been strongly conserved since these various species
began to diverge from a common ancestor. In most cases the latter seems the
more reasonable interpretation to my mind.

    It is not necessary for the rat or chicken to have mental
    capacities on a par with those of humans before we can justify
    applying this knowledge toward understanding how the human spinal
    systems work, nor does the existence of this organization in rats
    and chickens necessitate our adopting the view that rats and chicks
    think and feel as we do.

So as long as you're just studying the spinal functions, you can forget
about how the animal feels or what it thinks about the consequences to
it? The animal-righters do have some points to make, you know.

I thought I had made it clear that they do indeed. The point I was trying
to get across here is that one can learn things that will help us to
understand the functional organization of the human brain/spinal cord/muscle
system without having to assume that the animal's experience is identical to
ours; for example, the observation that the rat's brain contains control
circuitry aimed at keeping perceptions of threat or damage near zero does
not necessitate the conclusion that rats are able to perceive and experience
the complex, long-range sources of threat of threat we humans can. A rat
waiting in its cage between daily sessions in which it receives electric
shock shows no sign that it is being consumed by an anxious anticipation of
the next day's session; a chimpanzee in the same situation may well do so.
For this reason I would be far less willing to perform the experiment on the
chimp than on the rat.

However, in the case of chicks and separation anxiety, it seems to me
that you _are_ trying to compare higher functions, and that you _do_
have a dilemma: if what you are finding informs our understanding of
human experiences of the same kind, then you really shouldn't be doing
that. The only real answer is to say that there's nothing the animals
can do about it, and you consider human welfare to take priority over
animal welfare. MacDonald's does it all the time, why not psychologists?

And that is an answer many psychologists have been comfortable to adopt.
But it's not an easy decision for most.

    Evolutionary theory teaches that conscousness and self-awareness
    did not magically appear when the first true human being was born,
    but were in all probability features of the functioning of other
    brains before ours, and probably can be found in our nearest
    relatives and perhaps even in some who are not so near. As one
    moves from the study of chicks and rats to dogs and monkeys and
    primates, the findings as to the operation of higher brain areas
    become more direcly applicable to the human brain and it becomes
    correspondingly more difficult from an ethical viewpoint to justify
    the necessary experiments.

All speculation, my friend, and you know it. There are some hard
questions here to which nobody has any answers.

Yes, but informed speculation, based on both observation and evolutionary
theory. At the moment it's the best we can do.

In closing, let me lift a quote from John Bowlby that nicely expresses some
of the opinions I've offered about homology of brain structure and function
across species.

    Those who dispute the view that there is in man behaviour homologous with
    what in other species is traditionally called instinctive have a heavy
    onus of proof on their hands. In respect of man's anatomical and
    physiological equipment a continuity in structure with that of other
    species is unquestionable. In respect of his behavioural equipment
    continuity of structure may be less evident, but were continuity to be
    totally absent all we know of man's evolution would be contradicted.
    What is far more probable than absence of continuity is, therefore,
    that the basic structure of man's behevioural equipment resembles that
    of infra-human species but has in the course of evolution undergone
    special modifications that permit the same ends to be reached by a much
    greater diversity of means. The Romans could reach York by few routes;
    today we can select from hundreds. The ancient Sanskrit language
    provided only limited means of expression; its modern successors provide
    astonishing, simingly infinite, variety. Yet in each case the structure
    of the modern equipment, whether roads or language, is founded on and
    derived from the ancient structure. The early form is not superseded: it
    is modified, elaborated, and augmented but it still determines the overall
    pattern. This is the view of instinctive behaviour in humans that is
    advanced. Its basic structure is assumed to derive from some prototype or
    prototypes that are common to other animal species; that they have been
    augmented and greatly elaborated in certain directions is taken for granted.

    What, then, can these prototypic structures be like? What sorts of system
    can we imagine that, in less elaborated forms, can acocunt for instinctive
    behaviour, say, in fish, that in some more elaborated forms can account
    for such behaviour in birds and mammals, and that, in forms still more
    greatly elaborated, can account for instinctive behaviour in man? The
    search for prototypes is comparable to the search for a prototypic pelvic
    girdle by a comparative anatomist whose problem starts with the special-
    ized pelvic girdle of a horse.

    Models that promise to make great contributions to our understanding of
    the prototypic structures of instinctive behaviour are models derived
    from control theory. . . . Although it would be naive to assume that
    such theory can already solve behavioural problems of the complexity
    that confront the clinician, or even that it will do so soon, its
    usefulness in the analysis of simple movements is already demonstrated
    and it holds high promise of casting light on more elaborated sequences.
          Bowlby (1969, p. 40)

Regards,

Bruce

[Bruce_Abbott]

[From Bruce Abbott (951013.2000 EST)]

To continue . . .

Bill Powers (951012.1605 MDT) --
    Bruce Abbott (951012.1635 EST)

Words like attachment refer to classes of behavior that are important to
people. No argument about that. But the particular word we have
inherited was assigned by people who didn't know diddly-squat about how
behavior works, and the chances are that they really believed there was
some mysterious bond floating in the air and connecting people together.
These are the same people who gave us "looking at" to mean receiving
optical information from the environment.

I think when you've had the chance to read Bowlby's first volume
(_Attachment_) you may come to a different conclusion about what this term
meant for its originator.

    ... the most obvious manifestations are that the chick attempts
    with all its ability to stay close to some particular object and
    manifests what appears to we humans as distress when that contact
    is broken. If we have to call this phenomenon something, what
    label should we apply to it? To me, attachment seems as good as
    any for communicating the essense of what I am studying.

But isn't that only because you grew up for years believing that there
was some actual kind of attachment at work?

As you will discover when you read Bowlby's book, my introduction to
attachment was nothing like this. In fact, it had what you should find to
be an oddly familiar ring to it.

I'm looking forward with great anticipation to your review!

Regards,

Bruce

[William_T_Powers4]

[From Bill Powers (951014.1245 MDT)]

Bruce Abbott ()--

I don't know why it's taken me this long to realize what has gone wrong
with our discussion. What I'm interested in, as you know, is to develop
PCT into a full-blown theory of behavior, complete with a methodology, a
background of experimental demonstrations and explanations, and
applications to as many aspects of human and animal behavior as can be
assembled. This means starting with observations, formulating hypotheses
from the standpoint of PCT, and developing tests for separating the good
guesses from the bad ones. Isn't this how anyone would go about
developing any comprehensive theory?

The problem that you and I have had from the start is that in bringing
up problems on which psychologists have been working, which would be a
useful source of material for us to tackle, you have also brought along
all the standard theories under which these materials have been
interpreted. Why else would we have had such a long go-around over the
difference between PCT and reinforcement theory? In fact, reinforcement
theory is just one element of a whole theoretical structure, one in
which all the observations already carry theoretical labels like
reinforcement, discriminative stimulus, response, conditioning, and so
on. About every third word contains a theoretical assertion.

Obviously, as we try to develop PCT we want to develop it in terms of
basic observations of behavior, not in terms of other theories. We're
now engaged in a long discussion of findings of ethology, in which we're
talking about imprinting, separation anxiety, effects of brain
structures on behavior, and so on -- more theoretical terms than
observations, in fact. Once again, PCT is being applied not to data, but
to interpretations made from the standpoint of a well-developed and
highly interconnected theoretical structure different from PCT.

The only result that this approach can have is endless arguments about
the worth of this or that concept, the reality of this or that effect,
the correctness of this or that way of stating the observations. This is
bound to happen, because PCT involves looking at behavior from the
ground up as a different kind of phenomenon from what proponents of
other theories see going on. We don't even assume that the brain creates
"behavior," so what possible relevance can there be to statements about
which areas of the brain cause which behaviors? Under PCT, the brain
_controls,_ in the course of doing which it generates actions that
affect the sensed aspects of organism and environment that are involved.
Starting with that idea, one will naturally approach every aspect of
behavior and brain function differently.

When I say that we have to start from scratch, this is what I have been
trying to get across. I really don't care what ethologists call the
phenomenon of chicks, at a certain age, starting to follow large moving
objects. I want to know what the chicks are really doing and how they do
it. I want to test to see what variables they are learning to control.
In other words, I want to apply PCT to the phenomenon, directly, not to
keep worrying about whether the results will be interesting to
ethologists in terms they can understand. The results will be what they
are; if they are interesting to ethologists, fine; if not, so what? PCT
is not ethology, nor is it constrained by the theoretical considerations
that lead ethologists to interpret behavior as they do.

When you tell me about all the wonderful work that is being done in
psychology, about the important applications to human behavior, all I
can say is great, best of luck with it, I hope it works out. I'm
starting to sound like Rick Marken, or maybe I'm just beginning to
understand where he's coming from. All your evaluations of the work of
psychologists and its worth come from within the huge framework of
interlocking concepts that constitutes psychology, starting with your
description of what is wrong with a person in trouble and ending with
what is better about the person after being treated. All of these things
you're saying are relative to the framework of concepts from which you
speak: they are products of a system concept, and they are designed to
support the same system concept.

PCT is not just a new set of considerations to be added to the system
concepts of existing psychology. It is a new system concept which
interprets everything differently; it is a _substitute_ for the existing
system concepts. An interlocking structure of theoretical explanations
based on PCT will be completely different from the one that exists in
psychology. In such a structure, for example, there will be no entity
called "separation anxiety." There will be no "imprinting." Brain
structures will not be said to "produce behaviors." There will be no
"releasing stimuli," no "habits," no "reinforcement." Such terms belong
to other theoretical structures and carry connotations appropriate to
those other theories.

When we consider phenomena of behavior, the only questions relevant to
PCT are those that ask what an organism is controlling, and how and why.
Other theoretical interpretations are of no interest unless they contain
a hint about controlled variables. There is simply no other way to go
about this project.

I have a lot more to say, but this is all I can be coherent about right
now.

···

-----------------------------------------------------------------------
Best,

Bill P.

[Bruce_Abbott]

[From Bruce Abbott (951015.1200 EST)]

Bill Powers (951014.1245 MDT) --

I'll start with the bottom line:

When we consider phenomena of behavior, the only questions relevant to
PCT are those that ask what an organism is controlling, and how and why.
Other theoretical interpretations are of no interest unless they contain
a hint about controlled variables. There is simply no other way to go
about this project.

Yes.

Much of my effort has been driven by one fundamental question: how can PCT
help me to understand human and animal behavior? I have been especially
concerned with trying to apply PCT to a wide variety of known phenomena,
phenomena for which currently there may or may not exist what are viewed to
be acceptible alternative theoretical explanations. The examples I have
chosen are those that fall within my own field of interests and expertise.
If PCT correctly describes the basic organizational structure of animals,
including humans (as I believe it does), how might one apply PCT principles
to explain these phenomena? My own task has been to develop a coherent view
of the behaving organism that is not only consistent with PCT, but also with
the large body of observations provided by ethology, neuroscience, and
experimental psychology. Reinforcement, classical conditioning, and
imprinting, to name a few, are not only names for theoretical entities, but
for specific observations these theories were invented to explain. If I
discard reinforcement (the theoretical process) as an explanation for
certain observations, then how DO I explain them? Does PCT offer a way, or
is it something about which PCT, as currently developed, has nothing to say?
In short, I have been seeking a unified account, with PCT at the center,
that makes theoretical sense of these phenomena; I want to be able to look
my colleagues straight in the eye and say things like "forget about
reinforcement, PCT can explain those observations and do so with power and
parsimony, while simultaneously resolving a whole range of other
difficulties that confront reinforcement theory."

I know that PCT does not have all the answers as yet; that will require a
long program of research, but I at least want to see some of the theoretical
possibilities, as when we delved into how one might account of classical
conditioning using specific control-system models. That way when some
colleague asks how PCT might account for these phenomena, I can offer at
least a possibility, to show that such an account is possible.

Given this goal of mine, statements to the effect that all previous research
and observation is mush, not science, and not worth even discussing, is
obviously going to produce serious conflict. When I ask for help in working
out some possible approaches toward modeling these well-established
phenomena, the response "who cares, it's just junk anyway" won't seem
exactly helpful from my perspective.

So, it all comes down to different goals. Mine, at least at this early
stage, has been to construct a coherent view in which I can demonstrate how
PCT can help to make sense of a large number of known behavioral phenomena
(recognizing that the detailed models remain to be worked out); yours has
been to get someone to engage in elementary work designed to elucidate the
basic structure of control systems in the behaving organism. As Rick Marken
put it, he wants to study the phenomenon of control; as I answered, I want
to understand behavior. What I meant by this is that, at this point in my
development, I want to understand how PCT helps me to understand certain
phenomena of behavior with which I have been concerned as a practicing
research scientist. The research scientist wants to know, "how can PCT help
me to come to grips with the problems of concern to me in my studies?" I
doubt you are going to win many converts to PCT by an answer like "we don't
know and we don't care; your studies are of no concern to us and are
probably pseudoscience anyway. Why don't you just abandon them and start
doing research on OUR probems?" Although PCT clearly does not have all the
answers as yet (because so little research has been done), it would be far
more likely to win followers if one can at least demonstrate its _promise_
for coming to grips with the objective psychological/behavioral phenomena
your average card-carrying researcher is interested in understanding.

None of this is an argument against doing basic research on control in
living organisms, nor, as I stated earlier, are these two activities
necessarily incompatible. So here's a basic question: where do we begin?
What needs to be learned? What is the goal? Tracking studies demonstrate
that control is indeed present and can be accurately modeled; fine. But in
the behaving organism generally, what is being controlled at any given
moment changes constantly. I'm on my way out the door when I notice a TV
program has started on a topic I find fascinating. Suddenly my plan to wash
the car is put on hold and I sit down to watch the program. Goals are fluid
things; many of them come and go with the circumstances; my goal to watch
the program no doubt reflects the output of a higher-level system; from its
perspective watching the program is just a means to its own ends, yet the
goal to watch the program would have never been asserted had the program not
come on when it did. A researcher wanting to know what my current goal is
might try flipping off the TV and observing whether my actions resulted in
the restoration of the program (applying the TEST), but this would only tell
the researcher that I am controlling for a view of the picture, something of
no general significance for understanding the general organization of the
human hierarchical system. What the reference is is not as important as
learning about how the control system was created in the first place, its
parameters established, and so on. What is the research program you envision?

Regards,

Bruce

[Richard_Marken]

[From Rick Marken (951016.1300)]

Bruce Abbott (951015.1200 EST) --

I want to be able to look my colleagues straight in the eye and say things
like "forget about reinforcement, PCT can explain those observations and do
so with power and parsimony, while simultaneously resolving a whole range of
other difficulties that confront reinforcement theory."

Why not tell them the truth? Just look them in the eye and say "PCT cannot
explain your observations because those observations are irrelevant side-
effects of control".

statements to the effect that all previous research and observation is mush,
not science, and not worth even discussing, is obviously going to produce
serious conflict.

You are describing what you have heard; not what we have said. I don't
believe I have ever said that conventional behavioral research is "mush" or
"not science". But let me go on the record here and say: conventional
behavioral research would be VERY GOOD SCIENCE if organisms were cause-effect
systems. Unfortunately, there is good evidence that organisms are NOT cause-
effect systems; rather, there is strong evidence that they are control
(purposeful) systems. PCT shows what this means for conventional behavioral
research; it means that the results of this research are perfectly
scientific, non-mushy, carefully collected and catalogued descriptions of
irrelevant side-effects of control.

There have been indications for years that there is something wrong with
conventional behavioral research. The main indication, of course, has been
the resort to statistics; a science that consists of facts that have just a 1
in 20 chance of being non-facts has problems. But even in areas where you get
reliable data (like EAB) it is likely that the phenomena of interest (like
"stimulus control") are side effects of control (of input).

When I ask for help in working out some possible approaches toward modeling
these well-established phenomena, the response "who cares, it's just junk
anyway" won't seem exactly helpful from my perspective.

Again, this may be what you hear but it is not what we say. We don't say
that data is junk unless it IS junk (like group statistical data that is
collected in order to find out about individual psychological processes).
What we DO say is this: PCT shows that the "well-established" phenomena of
behavioral science are likely to be fascinating and compelling appearances
that are an observer's interpretation of the visible (but basically
irrelevant) side effects of control. There is nothing "junky" about much of
this data; it was just collected under the wrong assumption (the REASONABLE
but, unfortunately, false assumption that visible aspects of behavior are the
subject matter of behavioral science). PCT shows that, if organisms are
control systems, then the visible aspects behavior are irrelevant; the
relevant aspects of behavior -- the ones conventional research tells us
nothing about -- are the perceptual consequences of action that are under
control.

at this point in my development, I want to understand how PCT helps me to
understand certain phenomena of behavior with which I have been concerned as
a practicing research scientist.

And PCT does help you understand those phenomena -- it helps you understand
that those phenomena are irrelevant side effects of control. If you read my
"Blind men..." paper you also know that PCT shows why conventional
psychologists have been fooled by these side effects of control into thinking
that behaivor is either a response to stimulation, selected by its
consequences or generated as planned output. The whole point of PCT is to
show people that they must look PAST the appearances of behavior to know what
organisms are DOING. PCT also shows how to do this.

The research scientist wants to know, "how can PCT helpme to come to grips
with the problems of concern to me in my studies?"

Right. And that's why PCT has been a hard sell. PCT doesn't answer this
question the way the researcher expects. The researcher expects to hear "PCT
explains selection by consequences as follows: blah blah blah". The
researcher does NOT expect to hear "PCT shows that selection by conquences is
an irrelevant side effect of control; it is an appearance, not a real
phenomenon; organisms control their perceptions; selection of consequences
is an appearance that occurs in situations where organisms are controlling
some perception; what researchers should do now is start trying to find
out what perceptions are being controlled in situations where it LOOKS LIKE
there is selection by consequences".

The research scientist wants to know, "how can PCT help me to come to grips
with the problems of concern to me in my studies?"

I'm afraid that PCT CAN'T help UNLESS the research scientist wants to come to
grips with the problems of discoveing what variables the organism is
controlling. PCT can't help a physical chemist solve reaction rate problems
either. IF the problems that concern a researcher involve (or are thought to
involve) the behavior of causal systems then PCT is irrelevant.

I doubt you are going to win many converts to PCT by an answer like "we
don't know and we don't care; your studies are of no concern to us and are
probably pseudoscience anyway. Why don't you just abandon them and start
doing research on OUR probems?"

We may not get many converts but this is not quite what we say, it is? We do
care about some things -- like what perceptions organisms might be
controlling; but we can't determine what these variables are from the results
of conventional research. That doesn't mean we don't care about that
research at all; it just means that that research doesn't address the
questions that are pertinent to PCT. It doesn't mean that conventional
research is "pseudo science" either. It's not. It's perfectly good science
but it's being applied to the study if the wrong kinds of systems. If
organisms were cause-effect systems, conventional behavioral science would
not only be good science, it would be useful science; successful science. As
it is, organisms are control systems, so conventional behaviorsl science is
INAPPROPRIATE science; and, quite obviously (from the quality of the data and
modelling we find) failed science.

So here's a basic question: where do we begin?

How about where I left off;-)

What is the research program you envision?

Follow your nose, testing for controlled variables. If you are interested in
how reference states change -- and why they change -- then set up a simple
experimental situation where you can monitor the reference state of a
controlled variable. Start simple; the science of living control systems is
just beginning. Let's build it on a solid foundation.

Back to hibernation for sure this time

Rick

[Bruce_Abbott]

[From Bruce Abbott (951016.1935 EST)]

Rick Marken (951016.1300) --

Bruce Abbott (951015.1200 EST) --

I want to be able to look my colleagues straight in the eye and say things
like "forget about reinforcement, PCT can explain those observations and do
so with power and parsimony, while simultaneously resolving a whole range of
other difficulties that confront reinforcement theory."

Why not tell them the truth? Just look them in the eye and say "PCT cannot
explain your observations because those observations are irrelevant side-
effects of control".

Perhaps it's just a semantic thing, but I just don't view phenomena like a
child's anguish at being separated from its mother as irrelevant, even
though it may arise from the actions of a control system whose perceptual
input is being disturbed. It seems to me that PCT has some important
insights to offer, even if that insight is simply that the child's
observable behaviors are control-system responses to error. Irrelevant to
what? to whom?

One thing that keeps getting overlooked here is that PCT does not have
anything to say about the actions a control system will take to correct a
percepual error, except that (a) those actions will tend to correct the
error (if the system is functioning properly and not overwhelmed), and (b)
the intensity of the action generally will vary directly with the size of
the error. If there is a specific action or set of actions the system
inherently takes, this would be an important bit of information to know
about, don't you think? What if there is a predictable series of
adjustments that takes place during reorganization, after the child's tears
and other responses fail to bring its mother back? Irrelevant? Unimportant?

statements to the effect that all previous research and observation is mush,
not science, and not worth even discussing, is obviously going to produce
serious conflict.

You are describing what you have heard; not what we have said. I don't
believe I have ever said that conventional behavioral research is "mush" or
"not science". But let me go on the record here and say: conventional
behavioral research would be VERY GOOD SCIENCE if organisms were cause-effect
systems.

It's a comfort to hear you say that, Rick. I DIDN'T hear you say it earlier
when Feynman was being quoted as saying that psychology is nothing but a
"cargo-cult science," that is, something having the trappings of science
without the substance. But better late than never.

Unfortunately, there is good evidence that organisms are NOT cause-
effect systems; rather, there is strong evidence that they are control
(purposeful) systems. PCT shows what this means for conventional behavioral
research; it means that the results of this research are perfectly
scientific, non-mushy, carefully collected and catalogued descriptions of
irrelevant side-effects of control.

I beg to disagree. What I see in behavior is evidence of control, not
irrelevant side-effects of control. As an example, consider the complex
courtship rituals of some birds. What is often observed is a complex series
of movements which are manifestations of the workings of a sophisticated
control system operating at at least the "control of sequence" level, and
probably higher. Although the specific muscular contractions involved
change dynamically according to accidents of terrain, position of the
partner, and so on, the general pattern is clearly visible to the observer,
stable over repetition, and follows essentially the same form and sequence
in all members of that species and sex in which it occurs. Now that I know
what the control system is structured to produce, the next question to enter
my mind is "what specific perceptions are being controlled in order to
execute this sequence?" A whole host of related questions about the control
system involved and its sub-systems follows. Irrelevant side-effects? Baah!

There have been indications for years that there is something wrong with
conventional behavioral research. The main indication, of course, has been
the resort to statistics; a science that consists of facts that have just a 1
in 20 chance of being non-facts has problems.

On that we agree. Although statistical methods have their proper place,
they have too often become substitutes for real science. The goal becomes
one of obtaining statistical significance.

But even in areas where you get
reliable data (like EAB) it is likely that the phenomena of interest (like
"stimulus control") are side effects of control (of input).

I think it would be more accurate to say that these effects are
manifestations of control that can be understood as particular forms of
disturbance of a particular form of control system. The ability of these
inputs to disturb a given control system is acquired; how such a system
comes to be organized and how the system's actions change as a result is
certainly a fit subject of scientific investigation, as opposed to being
"irrelevant." Again, irrelevant to whom?

When I ask for help in working out some possible approaches toward modeling
these well-established phenomena, the response "who cares, it's just junk
anyway" won't seem exactly helpful from my perspective.

Again, this may be what you hear but it is not what we say. We don't say
that data is junk unless it IS junk (like group statistical data that is
collected in order to find out about individual psychological processes).
What we DO say is this: PCT shows that the "well-established" phenomena of
behavioral science are likely to be fascinating and compelling appearances
that are an observer's interpretation of the visible (but basically
irrelevant) side effects of control. There is nothing "junky" about much of
this data; it was just collected under the wrong assumption (the REASONABLE
but, unfortunately, false assumption that visible aspects of behavior are the
subject matter of behavioral science). PCT shows that, if organisms are
control systems, then the visible aspects behavior are irrelevant; the
relevant aspects of behavior -- the ones conventional research tells us
nothing about -- are the perceptual consequences of action that are under
control.

The apparent complexity in the behavior is simply a reflection of the
complexity of the environment. If ten ants follow the same path on their
way back to the nest, this may reflect the fact that the disturbances in
their path produced the same pattern of counteracting actions and nothing
more, yet it might appear to the observer that the aunts' neural networks
contained some kind of inherited motor program that steered them first this
way, then that, in a reproducable, sterotypical pattern. To conclude such
would be to interpret noise as meaningful data. Yes, I understand that.
The twists and turns of the ant are just side-effects of the control system
acting to correct error induced by accidental disturbances. Yet with more
observation it would be possible to discern something more important about
the ants' behaviors. No matter what gets in the way, the ant ends up at the
nest. A control systems analysis explains how this happens, but it does not
render the naturalist's observations irrelevant.

at this point in my development, I want to understand how PCT helps me to
understand certain phenomena of behavior with which I have been concerned as
a practicing research scientist.

And PCT does help you understand those phenomena -- it helps you understand
that those phenomena are irrelevant side effects of control. If you read my
"Blind men..." paper you also know that PCT shows why conventional
psychologists have been fooled by these side effects of control into thinking
that behaivor is either a response to stimulation, selected by its
consequences or generated as planned output. The whole point of PCT is to
show people that they must look PAST the appearances of behavior to know what
organisms are DOING. PCT also shows how to do this.

This is what bugs me. "Irrelevant" implies to me that such phenomena are
uninteresting and unimportant. In many cases, in my opinion, this picture
is entirely wrong. These behavioral responses can reveal what is being
controlled and how that control is accomplished. It can also reveal
pathologies of control, such as oscillation or the failure of the actions to
succeed in their purpose. So, while I agree with you that psychologists
have too often ended up studying and describing the constraints and
disturbances of the environment rather than describing the organism, I also
believe that there are plenty of phenomena discovered and characterized by
psychologists and ethologists that deserve to be subjected to careful study,
analysis, and explanation as guided by PCT.

Back to hibernation for sure this time

You've really got to do something about these nightmares, or you're going to
be up all winter . . . (;->

Regards,

Bruce

[Richard_Marken]

[From Rick Marken (951016.1945)]

Bruce Abbott (951016.1935 EST) re: "irrelevant side effects":

Irrelevant to what?

We've been over this many times, Bruce (sigh). Irrelevant side effects are
effects that are not controlled by the control system (though they may be of
great interest to the observer of the control system). Changes in room
temperature and relative humidity resulting from changes in the sensed
temperature controlled by a thermostat are irrelevant to the thermostat but
they can be quite relevant to people in the room.

You've really got to do something about these nightmares, or you're going
to be up all winter . . . (;->

I'll be OK as soon as I get over my disappointment.

Best

Rick

[William_T_Powers4]

[From Bill Powers (951022.1100 MDT)]
Using my son's computer in Boulder ...

Hans Blom (951020b) --

... by _labeling_ a phenomenon Lorenz started another
branch of scientific inquiry. Labeling a new phenomenon is little but
drawing attention to that something, in an attempt to communicate it
to -- and to communicate about it with -- others. "Hey, did you see
what happened? Let's call it X so that we can talk about it in the
future". It is the introduction of a new piece of "jargon" (the
language of experts in a certain domain that they use to communicate
amongst each other). The specific word that is picked is hardly
important, although it may confuse non-experts. Similarly, non-PCT
experts may find terminology like "reference level" or "control of
perception" utterly confusing or without meaning.

"Reference level" and "control of perception" are not jargon terms. They
are defineable so as to link with the larger body of language.
"Reference" is used in the sense of a reference mark, something with
respect to which something else is measured. "Level" is used in the
sense of "amount," as in "water level" or "sound level". A reference
level of a variable is that measure of the variable with respect to
which we measure the actual value -- a reference point on a scale of
values.

A term like "imprinting" also links to the larger body of language, but
in a misleading way that is not meant to be taken literally. It does not
mean "leaving a mark" on something, except perhaps in a metaphorical
sense. So the disadvantage of a term like imprinting is that it points
to perceptions in the listener which are not appropriate to the actual
phenomenon.

Why do you call [imprinting] magic?

It is magic because the effect follows from the cause with no plausible
mechanism linking them. I am aware that all scientific discoveries begin
as observations of magical connections, but in my understanding of
science the task is to substitute proposals about mechanisms to replace
the magic.

···

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Bruce Abbott (951022.1150 EST)--

I appreciate your summary of the debate, and agree that it has been
worth while. In particular, I appreciate your agreement that in order to
bring PCT into the analysis of previously-done studies, we would have to
do the studies over again in almost every case. That is basically what I
have meant by "starting from scratch." We might find the observation of
a phenomenon useful for the purpose of bringing it to attention, but as
PCT researchers we would have many questions which the original
observers did not have in mind, and which could not be answered only on
the basis of what these observers reported.

An analogy: suppose early astronomers had noted that many pairs of stars
appear very close to each other, closer than could be accounted for by
chance. If they had measured the separation of these close pairs very
accurately, later researchers would still have had to repeat their
observations because the early researchers did not conceive of stars in
mutual orbits around each other, and thus didn't (in this imaginary
scenario) see the importance of recording the position angle as well.
Even the original measurements of separations would have to be done
over, because what counts in calculating orbits is the _relationship_
between separation and position angle measured at the same time.

I have the impression that you hope we can use PCT to steer psychology
and other disciplines onto a new track, starting from the progress they
have already made. There might be cases where this could be true. But it
is more likely that 30 or 60 or 90 years of progress will prove to have
gone off the track way back in the beginning, so that as each new idea
was built on the accumulated knowledge of a discipline, the original
misinterpretations have been compounded again and again.

I can't see any way to tell whether this is the case except by going
back to the original observations and doing the studies again, whether
they were made last year or in 1905. And if we do that, it seems to me
very unlikely that we would follow the same trail. The only way to find
out is to do the work, follow our noses, and see how it comes out this
time. Any desire to justify all the investment that has gone into a
discipline, it seems to me, will just get in the way.
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Best to all,

Bill P.