Statistics in Psychology

CSGnet Archive CSG2009
1

[From Bill Powers (2009.01.01.0627)]

I declare this the Year of PCT.

Martin Taylor 2009.01.01.01.01–

Being of use to “those of
us who are trying to understand living control systems” is quite
different from “providing useful information about how living
control systems might work”. Yes, I thought it would be useful in
suggesting possible studies that might help understand why results like
theirs happen – why some people seem to change their overt behaviour in
the presence of something that on the face of it would seem to be
irrelevant. No, I didn’t think that the results said anything about how
living control systems might work.

“On the face of it would seem irrelevant” is a private
assumption, which contradicts all the reasons the authors gave for
suggesting it might be relevant. But “relevant” doesn’t tell us
anything useful, either: it’s just a hint that some regular relationship
might exist. Why should we be surprised if it either does or doesn’t
exist?

I think I’ve got it. You and Rick are talking about two different things.
You are saying that Keizer et. al. brought to our attention a
phenomenon that might be useful to explore using control theory.
Rick reads what you said as a statement that these authors brought to our
attention an explanation of the phenomenon that might be useful to
PCT. When you say “useful information about how control systems
might work,” you must mean “how they behave in specific
circumstances,” not “what mechanisms underly their
behavior.” The article offers no suggestions about the latter
subject.

The experiment showed us that some people in an observed population,
exposed to the possible sight of disorderliness, are more disorderly
themselves. Not many of them, but some of them. When A is true, B
happens. That is simply an observation of an apparent fact. Since PCT
applies to all of human behavior, it might be interesting to see what
explanation of this fact we might come up with using the control-system
model. Of course we would have to do an extensive amount of additional
experimention, first to identify the individuals who do and do not change
their behavior when exposed to disorder, then to find out how each one
perceived what the experimenters were calling “disorder” and
what their reference levels for that perception were, and finally to find
out why some individuals became more disorderly, why others became less
disorderly, and why most showed no effect at all. Then we would have an
explanation of this phenomenon in terms of first principles, which
someone might use to design a program for decreasing the
“disorderliness” (or whatever) of urban environments.

All that Keizer et. al. did was to observe some phenomena. True, they
spoke as if there was some kind of influence of the environment on the
behavior, but they didn’t offer any explanation of why that might come
about, or what mediated this influence, or why only some of the people
exhibited it. Their observations might be helpful to those responsible
for living conditions, in that they found an implied strategy that might
slightly reduce the number of people who litter, steal, trespass, and so
on. Any little improvement is better than none. But the authors offered
no theory to explain the effect, and no way to tell who would be subject
to it.

In principle, Martin is right in saying that we might learn more about
living control systems by looking into this phenomenon. But we would not
learn anything theoretical from the article, because the article offered
no theory; it offered only a recording of unexplained observations. There
is no shortage of unexplained behavioral phenomena that have not been
analyzed using PCT, so any given theoretician, I for example, would need
some pressing reason to investigate this one instead of some other.

I don’t find this study particularly interesting because it provides only
a few introductory observations and is far from complete. My interests
are in exploring, testing, and expanding PCT, and since my time and
resources are limited, I want to do this in as direct a way as I can
given the means available to me. There doesn’t seem any advantage in
doing two-step investigations, the first step revealing a very rough
picture of the phenomenon of interest over a population, and the second
filling in all the data-taking about individuals missing from the first.
Not that I object to pilot studies, but usually pilot studies don’t merit
publication in a major journal. If you study the individuals you get the
population data anyway, so why not do that first? Why deliberately design
the experiment so you can’t get the data about individuals?

Did my post with the diagram make it through everyone’s spam filters? It
shows a possible PCT explanation of the phenomenon – without many
details, but it’s at least a sketch. There’s nothing suprising in it –
it simply shows a diagram of how a higher-level perception made up of two
lower-level perceptions can be controlled by altering the reference level
of a lower-level control system. That could easily account for the
contextual effect observed, without requiring anything new in HPCT. And
it certainly shows that there is no need to imagine any direct effect of
the contextual variable on the behavior.

Best,

Bill P.

2

[Martin Taylor 2009.01.01.10.10]

[From Bill Powers (2009.01.01.0627)]

I declare this the Year of PCT.

“Possibly Conflicting Theories”?

The Wikipedia disambiguation page lists 32 different expansions of
“PCT” in seven domains of knowledge. So you are probably right.

I’ve probably written a lot more than I should in what follows, because
most of it is really agreeing with Bill, and expanding on what he says.

Martin Taylor 2009.01.01.01.01–

Being of use to “those
of
us who are trying to understand living control systems” is quite
different from “providing useful information about how living
control systems might work”. Yes, I thought it would be useful in
suggesting possible studies that might help understand why results like
theirs happen – why some people seem to change their overt behaviour
in
the presence of something that on the face of it would seem to be
irrelevant. No, I didn’t think that the results said anything about how
living control systems might work.

“On the face of it would seem irrelevant” is a private
assumption, which contradicts all the reasons the authors gave for
suggesting it might be relevant. But “relevant” doesn’t tell us
anything useful, either: it’s just a hint that some regular
relationship
might exist. Why should we be surprised if it either does or doesn’t
exist?

Yes, it’s a private assumption – a perception, if you will. There’s no
reason you should be surprised, at least not if you perceived a reason
for the behaviour (or if the possibility were uninteresting to you,
which opens another can of worms about “surprise”). The reason it would
be a surprise for me and not for the authors is that I come at it from
a PCT viewpoint whereas they didn’t. They expected the results, because
they set up the study to be analogous to what has been done in many
cities, where policies of cleaning up the streets has been accompanied
by reductions in crime.

I may have an unsophisticated appreciation of PCT, but I understood
that a change in the magnitude of the output is the usual result of
changes in the reference level or in the disturbance, and changes in
the nature of the output are the result of changes in the environmental
feedback function. I could see no apparent relation of the “disorderly
environment” with any of these, if the controlled perception was one
that had the “orderly-disorderly” action as its output. That’s why I
personally had the private assumption that the disorderly environment
was “on the face of it” irrelevant. It clearly cannot be irrelevant in
a correct analysis.

I felt that the situation demanded the functioning of at least two
control systems, one of which included the context as a contributor to
its perceptual variable, while a different one included the observed
“orderly-disorderly” actions as its output possibilities. My intuition
said that the way these interact was through conflict. Bill made
another suggestion, which at this moment seems to me to be equally
viable. Whether both offer equally viable solutions as to why some
people are affected while others are not is an open question. To test
between them would require experiments of quite different nature.

I think I’ve got it. You and Rick are talking about two different
things.
You are saying that Keizer et. al. brought to our attention a
phenomenon that might be useful to explore using control
theory.
Rick reads what you said as a statement that these authors brought to
our
attention an explanation of the phenomenon that might be useful
to
PCT. When you say “useful information about how control systems
might work,” you must mean “how they behave in specific
circumstances,” not “what mechanisms underly their
behavior.” The article offers no suggestions about the latter
subject.

That puts in much better words what I’ve been trying to say all along.
I’ve known that Rick and I have been talking about different things,
but he hasn’t, and I haven’t been able to find the words to get him to
understand. I hope you have.

The experiment showed us that some people in an observed population,
exposed to the possible sight of disorderliness, are more disorderly
themselves. Not many of them, but some of them. When A is true, B
happens. That is simply an observation of an apparent fact. Since PCT
applies to all of human behavior, it might be interesting to see what
explanation of this fact we might come up with using the control-system
model. Of course we would have to do an extensive amount of additional
experimention, first to identify the individuals who do and do not
change
their behavior when exposed to disorder, then to find out how each one
perceived what the experimenters were calling “disorder” and
what their reference levels for that perception were, and finally to
find
out why some individuals became more disorderly, why others became less
disorderly, and why most showed no effect at all. Then we would have an
explanation of this phenomenon in terms of first principles, which
someone might use to design a program for decreasing the
“disorderliness” (or whatever) of urban environments.

Yes. It would be interesting to know whether the designed program would
be more effective than the ones in at least five countries that led
Keizer et al. to do their experiment. They identified as a problem that
the results in those cities were merely correlational, looking at
changes in criminality over time before and after cleanup campaigns
were introduced, whereas the experiment was set up to compare the
likelihoods of “disorderly” behaviour in two situations as similar as
possible apart from the “disorderly-orderly” contrast in the context.

This sequence is often the case. One might lay it out like this:

At least some of the public believe effect X exists -> a political
decision is based on this belief -> the politico-social effects are
(or are not) as expected -> experiments are done to test whether the
effect “really” occurs (my advisor in graduate school said that the job
of psychology was to find out whether what everyone knows is actually
true). I would like to add to this chain: -> PCT studies illuminate
the mechanism for the effect and the conditions in which it islikely to
affect particular individuals.

In principle, Martin is right in saying that we might learn more about
living control systems by looking into this phenomenon. But we would
not
learn anything theoretical from the article, because the article
offered
no theory; it offered only a recording of unexplained observations.

Yes, although they thought they were testing theories, the theories
were not what we would be considered to be more than generalized
observations.

There
is no shortage of unexplained behavioral phenomena that have not been
analyzed using PCT, so any given theoretician, I for example, would
need
some pressing reason to investigate this one instead of some other.

If you remember the context in which I introduced this paper, it was to
suggest that “conventional” research can provide leads toward effects
that one (e.g. me) might well not have derived from a basic
understanding of PCT, and that therefore might suggest a fruitful
avenue for research. It was just offered as an example of the class.

Research can be “fruitful” in at least two ways. One helps advance the
theoretical foundations of PCT and the other helps the application of
PCT to socially significant problems. The Keizer et al. paper seemed to
me to address a socially significant problem and at the same time to
offer the possibility that there might be some theoretical advances to
be had in the investigation. (It helped that it appeared in Science at
the same time I was thinking of intervening in the ongoing “Statistics
in Psychology” to make the point that I felt was clarified by this
paper).

Did my post with the diagram make it through everyone’s spam filters?
It
shows a possible PCT explanation of the phenomenon – without many
details, but it’s at least a sketch.

Yes. It came through OK. It represents what I had understood from your
verbal description.

There’s nothing suprising in it –
it simply shows a diagram of how a higher-level perception made up of
two
lower-level perceptions can be controlled by altering the reference
level
of a lower-level control system. That could easily account for the
contextual effect observed, without requiring anything new in HPCT. And
it certainly shows that there is no need to imagine any direct effect
of
the contextual variable on the behavior.

I’d be happier with your diagram if I could think of a plausible
higher-level controlled perception with the proposed characteristic
connections. What is the “Perceived contextual effect”? As drawn, it’s
quite ad-hoc, like a perception of a salty taste combined with a red
chair. You don’t need to specify the controlled perception for the
explanation to be viable, but the explanation becomes more plausible if
you do. The experimental (or perhaps theoretical) issue is whether this
is a correct description, or whether the conflict-based description I
initially proposed (based on imagining myself in that context) is
correct, or whether something else entirely is happening.

Anyway, the point I was trying to raise has nothing to do with this
particular study, socially important though it may be.

The point is that over the years conventional research has produced
many observations that are believed to be widely applicable, even if
they are of the kind that “condition X leads to more of behaviour B
than does condition Y”. None of those say any more than that the
difference between conditions X and Y affect some people in a way that
leads them to produce different outputs. Quite often, at least in the
social context, experiments are done to test a popularly believed
effect, which often the experiment shows to be no more than
superstition (why is it good luck in one country for a black cat to
cross your path, while it is bad luck in a neighbouring country?
–England and Scotland, though I can’t remember which is which).

The conventional psychologist might see the correlation between change
of condition and change of behaviour as a causal effect. The PCT
psychologist would not, but if PCT is to become mainstream (as
suggested in Bill’s first line), PCT must be able to provide a natural
explanation of how the effect happens in those people who are affected,
why it does not happen in those who are not, and what is the difference
between those classes of people. In many cases, a PCT explanation is
obvious, though of course it isn’t demonstrably a correct explanation
without experiment (as Dick Robertson’s investigations on self-image
have shown).

In the course of providing these explanations, it is not at all
unlikely that we might learn more about the structures of control
systems peculiar to humans than simply the assumption that there exists
an amorphous control hierarchy (which is presumably true of all living
things).

Martin

3

[From Rick Marken (2008.01.01.0930)]

Martin Taylor 2009.01.01.01.01]

Yes, I thought it would be useful in
suggesting possible studies that might help understand why results like
theirs happen

OK, so this is what you meant by "useful to a control theorist". In
this sense the study you mention is no more useful than any other
study in conventional psychology; it's a description of something that
happened. It is no more useful to me than the studies of the effect of
peer pressure on conformity or the effect of leading questions on
eyewitness testimony (two classic conventional studies). What you are
saying is that the results of conventional research are useful to
PCTers because they might suggest possible studies (I presume studies
done using "the test" since that's the only kind of study that can
tell us anything about control) that will help us understand why
results like these happen.

I think you couldn't be more wrong about this. Saying that such
research is useful because it suggests other studies that might be
done implies to other conventional psychologists studies along the
same lines. The result is the Carver/Scheier approach to studying
control phenomena -- using conventional causal research. Carver and
Scheier make no attempt to test for controlled variables in
individuals. This is what happens when psychologists think of
conventional research as "useful"; conventional research simply gets
interpreted with control theory terminology.

The idea that conventional psychology is "useful" has certainly made
control theory palatable to a larger audience -- Carver and Scheier
and their ilk are referenced all over the place -- but that's because
they are not actually studying control. They just _sound like_ they
are studying control because they know how to use _some of_ the
vocabulary of control to describe the results of their conventional
research. When I first encountered Carver and Scheier I was impressed
by their understanding of Powers' version of control theory (it was
not called PCT at the time). They did an excellent job of describing
the theory in the first couple chapters of their book (this was in
1982, I think). But then things when haywire when they started
describing their research. It was all based on the causal model.
Clearly, Carver and Scheier did not really get the relationship
between the theory and the phenomenon of control. That's why they were
completely content to study control using causal methodology -- which
is absurd.

Now that I think of it, It was probably this very disappointing
encounter with Carver and Scheier's work that convinced me that
"understanding PCT" involved more than understanding a control
equation or diagram. Really understanding PCT involves (for me) an
understanding of how to study control; it involves understanding
control methodology. In order to understand how to study control you
have to understand how the model maps to the phenomenon of control.

After 30 years working on PCT and trying to present it to
psychologists I have found that the main obstacle to acceptance and/or
understanding of PCT among research psychologists is preconceptions
about how to study behavior. The causal research paradigm in
psychology is so strong that it's nearly impossible to get
psychologists to reorient and see behavior in terms of the maintenance
of often difficult to detect controlled variables that are being
maintained at fixed or variable reference levels by the subject. I
think the obstacle is methodological because I have rarely seen much
resistance to the PCT model itself. Many psychologists (like Carver
and Scheier) are just fine with control theory; it makes a lot of
sense to them and it doesn't conflict (in their minds) with anything
they care about. The problems arise (for me) when they go to test it
and try to fit these tests into the Procrustean bed of causal research
methodology.

So your suggestion that the Science article might be useful in the
sense of suggesting further research on control is very troublesome to
me because it gives legitimacy to the causal approach to studying the
behavior. I think that, as a source of ideas for real control research
this Science research is no better than just looking around and
noticing everyday behavior; noticing, for example, that some people
litter. So you might do a study to find out what a person is
controlling for when they litter. Or you might do a study to see what
people are controlling for when they answer questions about what they
have seen (eyewitness testimony); or you might do a study to see what
people are controlling for when they drive a car. You don't need the
results of causal research to suggest what you might study from a
control perspective. Just look around.

I think the notion that the results of conventional research can be
"useful" in some way to a control theorist is just about the best way
to keep control theory (the real thing; not the Carver/Scheier type)
from making any headway into the life sciences. It will just keep
people comfortable doing research the old fashioned (causal
model-based) way. And it will keep 2009, once again, from being the
year of PCT. PCT won't happen (scientifically) until we have a bunch
of people studying control using the appropriate methodology -- a
methodology aimed at testing a control rather than a causal model of
behavior. We now finally have some people doing clinical work using a
completely control theory based methodology (MOL). It would be nice if
we could get a couple more people doing scientific work using a
completely control theory based methodology (the test). We won't get
that if leaders in the field (like yourself) keep giving the
impression that the results of conventional methodology are useful to
(or should even be considered by) control theorists, either as
evidence of control or as suggestions for research or whatever.

In my humble opinion, anyway;-)

Best

Rick

···

--
Richard S. Marken PhD
rsmarken@gmail.com

4

[From Goldstein (2009.01.09,12:27 EST)]

About [ Bill Powers (2009.01.01.0627)]

I think that this is a good summary of the exchange between Rick and Martin.

Conventional approaches to research might help identify some socially significant phenomena. PCT approaches to research might help identify what is going on within a person who displays the phenomena.

I am attaching a pdf file which addresses the issue of whether EEG Biofeedback is helpful in treating children diagnosed with some form of ADHD.

What is a person learning to control after EEG Biofeedback that he/she was not able to control before EEG Biofeedback?

Would it be possible to use PCT ideas to measure how well a person is controlling his/her brain waves?

Is a person different in how well he/she can control specific levels of perception?

Is the way that awareness interfaces with the perceptual hierrarchy changed?

As you can see from the editorial, the editorial is pointing to certain brain structures (for example, the cingulate gyrus) which might be changed in some way. This seems to be one kind of explanation that is looked for.

David

Hirshberg_Editorial.pdf (83.4 KB)

···

----- Original Message -----

From:
Bill Powers

To: CSGNET@LISTSERV.ILLINOIS.EDU

Sent: Thursday, January 01, 2009 9:32 AM

Subject: Re: Statistics in Psychology

[From Bill Powers (2009.01.01.0627)]

I declare this the Year of PCT.

Martin Taylor 2009.01.01.01.01–

Being of use to "those of us who are trying to understand living control systems" is quite different from "providing useful information about how living control systems might work". Yes, I thought it would be useful in suggesting possible studies that might help understand why results like theirs happen -- why some people seem to change their overt behaviour in the presence of something that on the face of it would seem to be irrelevant. No, I didn't think that the results said anything about how living control systems might work.

“On the face of it would seem irrelevant” is a private assumption, which contradicts all the reasons the authors gave for suggesting it might be relevant. But “relevant” doesn’t tell us anything useful, either: it’s just a hint that some regular relationship might exist. Why should we be surprised if it either does or doesn’t exist?

I think I’ve got it. You and Rick are talking about two different things. You are saying that Keizer et. al. brought to our attention a phenomenon that might be useful to explore using control theory. Rick reads what you said as a statement that these authors brought to our attention an explanation of the phenomenon that might be useful to PCT. When you say “useful information about how control systems might work,” you must mean “how they behave in specific circumstances,” not “what mechanisms underly their behavior.” The article offers no suggestions about the latter subject.

The experiment showed us that some people in an observed population, exposed to the possible sight of disorderliness, are more disorderly themselves. Not many of them, but some of them. When A is true, B happens. That is simply an observation of an apparent fact. Since PCT applies to all of human behavior, it might be interesting to see what explanation of this fact we might come up with using the control-system model. Of course we would have to do an extensive amount of additional experimention, first to identify the individuals who do and do not change their behavior when exposed to disorder, then to find out how each one perceived what the experimenters were calling “disorder” and what their reference levels for that perception were, and finally to find out why some individuals became more disorderly, why others became less disorderly, and why most showed no effect at all. Then we would have an explanation of this phenomenon in terms of first principles, which someone might use to design a program for decreasing the “disorderliness” (or whatever) of urban environments.

All that Keizer et. al. did was to observe some phenomena. True, they spoke as if there was some kind of influence of the environment on the behavior, but they didn’t offer any explanation of why that might come about, or what mediated this influence, or why only some of the people exhibited it. Their observations might be helpful to those responsible for living conditions, in that they found an implied strategy that might slightly reduce the number of people who litter, steal, trespass, and so on. Any little improvement is better than none. But the authors offered no theory to explain the effect, and no way to tell who would be subject to it.

In principle, Martin is right in saying that we might learn more about living control systems by looking into this phenomenon. But we would not learn anything theoretical from the article, because the article offered no theory; it offered only a recording of unexplained observations. There is no shortage of unexplained behavioral phenomena that have not been analyzed using PCT, so any given theoretician, I for example, would need some pressing reason to investigate this one instead of some other.

I don’t find this study particularly interesting because it provides only a few introductory observations and is far from complete. My interests are in exploring, testing, and expanding PCT, and since my time and resources are limited, I want to do this in as direct a way as I can given the means available to me. There doesn’t seem any advantage in doing two-step investigations, the first step revealing a very rough picture of the phenomenon of interest over a population, and the second filling in all the data-taking about individuals missing from the first. Not that I object to pilot studies, but usually pilot studies don’t merit publication in a major journal. If you study the individuals you get the population data anyway, so why not do that first? Why deliberately design the experiment so you can’t get the data about individuals?

Did my post with the diagram make it through everyone’s spam filters? It shows a possible PCT explanation of the phenomenon – without many details, but it’s at least a sketch. There’s nothing suprising in it – it simply shows a diagram of how a higher-level perception made up of two lower-level perceptions can be controlled by altering the reference level of a lower-level control system. That could easily account for the contextual effect observed, without requiring anything new in HPCT. And it certainly shows that there is no need to imagine any direct effect of the contextual variable on the behavior.

Best,

Bill P.

5

[From Bill Powers (2009.01.01.1050 MST)]

Rick Marken (2008.01.01.0930) –

Martin Taylor
2009.01.01.01.01]

Yes, I thought it would be useful in

suggesting possible studies that might help understand why results
like

theirs happen

OK, so this is what you meant by “useful to a control
theorist”. In

this sense the study you mention is no more useful than any other

study in conventional psychology; it’s a description of something
that

happened. It is no more useful to me than the studies of the effect
of

peer pressure on conformity or the effect of leading questions on

eyewitness testimony (two classic conventional studies). What you
are

saying is that the results of conventional research are useful
to

PCTers because they might suggest possible studies (I presume
studies

done using “the test” since that’s the only kind of study that
can

tell us anything about control) that will help us understand why

results like these happen.

I think Martin agrees with me about what is considered a theory in
psychology. As far as I can tell, there is only one actual theory
in psychology: it is the theory that says behavior is caused by the
environment (which includes the behaving system’s physiology). All the
rest of what is commonly called theory is actually just a proposal that
under condition C, behavior B will be observed. I have never seen any
proposals about how C produces B, other than vague references to reflexes
or intervening variables, or just “Don’t ask.”
We keep hearing “But how does PCT explain X?” where X is some
observed C that is accompanied by a B. What is expected, evidently, is
something like a syllogism:
*Human beings between 30 and 50 years old try to behave like other
people.
John is a human being between 30 and 50 years old.
Therefore, we observe John trying to behave like other people.*The major (first) premise is the supposed explanation.
Now consider the explanation implicit in that diagram I sent
yesterday.
*Higher-order Reference condition: I am behaving like other
people
Lower-order perception 1: I am not littering
Lower-order perception 2: I see litter that other people left
Higher-order perception : I am behaving differently from other
people
Higher-order error signal: not behaving enough like others
[translates into increase of littering reference signal at lower
level, which creates an error at the lower level]
Lower-level Error: Not enough littering
Behavioral effect: drop the paper on the ground.
[Corrects errors at lower level and higher level]*I’m sure a better set of propositions could be put together, but the
above makes the point. In the PCT rendition, we have an underlying model
which leads to a series of testable proposals. We would try to test them
through interviewws or added experiments with each individual. What we do
next would depend on what we find out about a population of individuals,
and of course on what we intend to do about the littering, if anything.
We might, for example, launch a campaign aimed at persuading people that
it’s very cool to be different from other people. We would know that
simply fighting the littering directly (“DON’T LITTER: $50
FINE”) would just create a conflict in anyone who wants to be like
other people if that person failed to litter in an already-littered
environment. Cleaning up the environment, on the other hand, might
succeed. But it wouldn’t succeed if the higher-order goal was “No
more than X amount of litter.” By reducing the amount below X, you
send the signal that a little bit of littering is OK.

I think you couldn’t be more
wrong about this.

I can think of lots of ways he could be more wrong. “I
disagree” would have sufficed. Putting emotional pressure behind
your statements just causes opposition. When you grow up you’ll
understand.

Saying that such

research is useful because it suggests other studies that might be

done implies to other conventional psychologists studies along the

same lines.

It does? All by itself, it suggests that? Are you claiming that saying
those words will cause conventional psychologists to do more conventional
studies? I thought you didn’t believe in that.

In my humble opinion,
anyway;-)

When did you start having that kind of opinions?

Best,

Bill P.

6

[Martin Taylor 2009.01.01.14.12]

[From Bill Powers (2009.01.01.1050 MST)]

I think Martin agrees with me about what is considered a theory in psychology.

I also think I do, though it sometimes may not seem so.

  As far as I can tell, there is only one actual theory in psychology: it is the theory that says behavior is caused by the environment (which includes the behaving system's physiology). All the rest of what is commonly called theory is actually just a proposal that under condition C, behavior B will be observed. I have never seen any proposals about how C produces B, other than vague references to reflexes or intervening variables, or just "Don't ask."

If I may demur, I don't think J.G.Taylor's (no relation) "Behavioural Basis of Perception" (Yale University Press, 1962) fits that mold. It was an explicitly modelled, but not simulated, multilevel feedback account of how what we would call "reorganization of perceptual functions" occurs. He used reinforcement theory, which puts an element of magic into it, but otherwise it was an explicit theory that accounted for some rather strange observations on individuals (one of whom was Seymour Papert, in case that interests you).

One strange observation that fell out from his theory was that when he (and one or two others) trained with spectacles that rotated the world 180 degrees, there was a stage when he would see a person sitting quite normally in a chair with the floor below and the ceiling above, and yet the smoke from the person's cigarette was floating downward to the ceiling. He had a lovely movie of Seymour Papert learning to ride a bicycle while wearing left-right inverting spectacles -- or not. At first, Papert simply fell down when wearing the spectacles. then he would be fine with the spectacles but would fall down when he took them off. After more practice, he could ride while putting the spectacles on and off with no problem, until Jim substituted straight-through glass for the inverting prisms, at which point Papert would fall down when he put the spectacles on. All of this was predicted beforehand from the maths of the theory.

When I first encountered PCT around 1991, I initially thought it was the same as Jim's theory. Of course it isn't, but I think Jim's was a real theory.

Putting emotional pressure behind your statements just causes opposition.

All by itself it causes opposition? I thought you didn't believe in that :slight_smile:

Saying that such
research is useful because it suggests other studies that might be
done implies to other conventional psychologists studies along the
same lines.

It does? All by itself, it suggests that? Are you claiming that saying those words will cause conventional psychologists to do more conventional studies? I thought you didn't believe in that.

Maybe it's another effect like the one in the Keizer et al. study. Some conventional psychologists reading those words might be led to do more conventional studies along those lines than they would if they had not read the words. But I guess Rick doesn't believe in such effects, either.

In my humble opinion, anyway;-)

When did you start having that kind of opinions?

Don't be too hard on him. Humility is a strange associate to a high-gain control system that has a zero threshold in its comparator. That's how I read Rick's control of the perception of PC correctness in other people. He cares deeply about PCT, and the slightest deviation of other people's understanding from his understanding is an error that induces strong output to correct that deviation.

The problem is, as I see it, that there is no guarantee that Rick's or my or even Bill's understanding of PCT is scientifically correct. If there were such a guarantee, then a zero-threshold comparator function might be appropriate. Whether the high-gain output would always act in a way to reduce the error is a separate question, which I guess is the background to your "Putting emotional pressure behind your statements just causes opposition."

Isn't PCT fun :slight_smile:

Martin

7

What is a person learning to
control after EEG Biofeedback that he/she was not able to control before
EEG Biofeedback?
Is a person different in how
well he/she can control specific levels of
perception?
Is the way that awareness
interfaces with the perceptual hierrarchy changed?
As you can see from the
editorial, the editorial is pointing to certain brain structures (for
example, the cingulate gyrus) which might be changed in some way. This
seems to be one kind of explanation that is looked for.
[From Bill Powers (2009.01.01.0810 MST)]

Goldstein (2009.01.09,12:27 EST)

···

–

It has to be something the person can perceive with unaided senses if the
control continues after the artificial feedback path is removed. I have
heard of people thinking of peaceful scenes as a means of making a blood
pressure reading decrease. When they can’t see the blood pressure
indication, they can still think of peaceful scenes, but of course unless
someone measures their blood pressure they won’t know if that actually
lowered their blood pressure.

So they can’t really “control” blood pressure without the
biofeedback apparatus. If something disturbs it, increasing it, they
won’t sense any error and won’t think of the peaceful scene. Blood
pressure would then fail the test for the controlled variable. If there
is some symptom of high blood pressure that they could notice, then they
could learn to control that symptom, and again as a side-effect, control
blood pressure. But if the sensed symptom changed without the blood
pressure changing, they would control ther symptom back to its
“proper” state, and thus cause the blood pressure to be too
high or too low.

I think biofeedback works open-loop after the training, unless the person
actually learned to control something he can sense without the apparatus.
I suppose that can happen.

Would it be possible to use PCT
ideas to measure how well a person is controlling his/her brain
waves?

My impression is that biofeedback is a way of enabling people to
sense an artificial indicator that stands for something the person can’t
sense, like brain waves. Without the indicator, the brain waves still
can’t be sensed, but the person may have learned to control something
else that can be sensed, doing which has a side-effect of altering the
brain waves. If the brain waves can’t be consciously sensed, they can’t
be consciously controlled.

Brain waves exist because of all the activities in the brain; they are
side-effects of the actions of all the control systems in the brain. So
anything you learn to control is going to alter brain waves, and if you
change the way you control something you will change the brain waves
resulting from that control. It may look as if the brainwaves themselves
are being controlled, but they’re not, because they’re not perceived.
Brain waves are electrical currents in the scalp, not neural signals in
the brain.

However, since EEGs measure currents generated by millions of neurons,
the effects of most control activities probably can’t be distinguished
individually. Only when a large number of neurons are affected more or
less in the same way, or a part of the brain very close to the electrode
placement is involved in controlling something, would you expect to see a
large enough effect to show in one EEG site and in one frequency
band.

Remember that EEG tracings are the outputs of filters which respond only
to certain frequencies. This does not mean that those frequencies are
connected with specific functions in the brain. The electrical fields of
the brain fluctuate according to the activities of control in the brain,
which create very complex electrical waveforms as ions flow hither and
thither. If you do a Fourier analysis of those waveforms, you can
represent them as a collection of signals with different frequencies, but
that is true of any waveform no matter how it was created. If you look at
a scene through green sunglasses, everything looks green, but that
doesn’t mean everything IS green. If you look at a brain’s activities
through a 10-Hz filter, you will see 10-Hz variations.

So I don’t believe that there is anything about brain waves that is
fundamental to the operation of the brain, or that corresponds to any one
perception, control activity, or level of control. The use of the EEG for
diagnosis is strictly correlational, which of course can be very useful
for indicating problems in the brain, but it’s of no theoretical
help.

I think so. In terms of evolution, the lower-level systems have been
evolving much longer than the higher-level systems, and even in the
individual, the higher level systems get reorganized last. On top of
that, people adopt a good many different system concepts, some of which
work a lot better than others.

By biofeedback? I don’t think so. What is reorganized is a hierarchical
control system or a perceptual function, and that only changes what there
is to be aware OF.

In the first place, I don’t believe there such a thing as ADHD,
except as a diagnostic category. Children with that diagnosis don’t have
any attention deficit; they have plenty of attention – they just don’t
attend to things that adults want them to attend to. They are, in the
adult’s opinion, too active, but that still doesn’t tell us what, if
anything, is wrong with them. If a person doesn’t behave the way you
want, maybe the one with a problem is you. I think a lot of diagnoses
reveal the diagnoser’s cultural biases or personal preferences (like
those “oppositional” or “defiant” disorders). Good
heavens, if a child defies my authority, there is obviously something
wrong with the child!

In the second place, I still find it amusing that neuroscientists seem to
be fascinated at discovering that brain activities have something to do
with perception and behavior. How do they think behavior works, and where
do they think experiences happen? “Few neuroscientists now doubt
that we are able to exercise volitional control over neural functioning
when given real-time feedback” could be restated as " … now
doubt that behavior is the control of perception." Only of course
they don’t think of it that way. When you look at your hand and
curl the fingers into a fist, you’re volitionally controlling all sorts
of neural functioning. Should we be surprised if we stumble across a few
neurons that change their activity as we do this?

One thing I agree with: in biofeedback training, there are probably
reorganizations going on of which nothing is perceived consciously.
Learning to control a cursor with neural signals (other than the motor
signals sent to muscles) must feel a good deal like learning to wiggle
your ears. You never actually experience what it is you do to make the
required result happen, yet you gradually reorganize until it happens
when you want it to (not I, however). A baby goes through exactly the
same process when learning how to make arms, legs, hands, and finally
fingers behave as wanted. As we know, it’s not necessary to understand
HOW your action affects a perception in order to control the
perception.

Side thought to Rick, Bruce Abbott, and any other modelers interested. We
ought to be able to construct a demonstration in which actions performed
with a mouse are translated into multiple indirect effects on screen
objects. You would have to reorganize in order to learn how to make, say,
the green square move up without causing the orange circle to move
sideways. This would be a nice analog to the baby’s world and might give
us a window into the reorganizing system.

All the data in the editorial appear to be population statistics used to
determine treatments for individuals. I have zero interest in that and
would stop it if I could. Notice how nobody ever discusses the chances
that the implied treatments would help a particular individual. I think
there’s a damned good reason why they don’t discuss it. And I am really
put off by the calm self-assurance in Hirshberg’s discussion of people
who are “determinedly opposed to medical treatment.” I’m all
for “evidence-based treatment,” but show me some evidence that
means something, not this worthless statistical crap. People do get all
wrapped up in their customary ways of doing things, don’t they?

Yes, Rick isn’t the only one who gets mad.

Best,

Bill P.

8

[From Goldstein (2009.01.04.00:02 EST)]

About [Bill Powers (2009.01.01.0810 MST)]]

Bill: So I don’t believe that there is anything about brain waves that is fundamental to the operation of the brain, or that corresponds to any one perception, control activity, or level of control.

David: There is a NJ Psychologist who has taken a very different approach. His name is Kirtley Thornton.

Take a look at his website: http://chp-neurotherapy.com/

His general approach is to give a person a task of interest, say reading a paragraph, while recording the person’s EEG. The EEG is analyzed into QEEG variables. This is done for a whole group of people. Then he divides the the group into those who performed well on the task and those who performed poorly. The QEEG variables which correlate with good performance become the training targets in EEG Biofeedback.

Dr. Thornton is getting some very impressive results as you can see from the website. The person is engaged in a task of interest. The normative group gives a picture of the EEG when good performance (control?) is happening.

It would be interesting to take Dr. Thornton’s approach for the pursuit tracking task. We might find out the relationship between the parameters that you estimate and the QEEG variables. This might tell us something of theoretical interest, no?

9

[From Rick Marken (2009.01.04.1015)]

Bill Powers (2009.01.01.1050 MST)--

I think Martin agrees with me about what is considered a theory in
psychology. As far as I can tell, there is only one actual theory in
psychology: it is the theory that says behavior is caused by the environment

There are many theories in psychology that are not S-R theories.
Martin mentions JG Taylor's R-S theory; and, of course, there is PCT
as per Carver and Scheier and several cognitive computer models, like
Newell and Simon's GPS model of problem solving, are true control
models. My point is that, when one tests these theories using
conventional methods, one is implicitly assuming (and testing) an S-R
theory: the general linear model. There is only one actual theory in
psychology (S-R theory) because there is only one approach to testing
theories in psychology: causal methodology.

Best

Rick

···

--
Richard S. Marken PhD
rsmarken@gmail.com

10

[From Rick Marken (2009.01.04.1345)]

Martin Taylor (2009.01.01.14.12) --

Humility is a strange associate to a high-gain
control system that has a zero threshold in its comparator. That's how I
read Rick's control of the perception of PC correctness in other people.
He cares deeply about PCT, and the slightest deviation of other people's
understanding from his understanding is an error that induces strong
output to correct that deviation.

It's not your understanding of PCT that I question; it's your
understanding of what PCT implies about how to go about studying the
behavior of a control system. I think you don't understand what PCT
says about what we can learn about control systems (living or
artifactual) by studying them using conventional research methodology.
I am high gain about this because I don't think PCT will get the kind
of attention it deserves until it has a nice large corpus of data to
point to, data collected using control methodology. But I don't know
why I keep pointing this out on CSGNet; it's clearly a waste of time.
So I'll just drop it. You can point to findings in the conventional
literature all you want; I won't make a peep;-)

Best

Rick

···

--
Richard S. Marken PhD
rsmarken@gmail.com

11

[From Rick Marken (2008.12.21.1450)]

While looking for some information about the history of the use of
statistics in psychology I ran across a text called "Statistics in
Psychology: A Historical Perspective" by Cowles and, I saw, in there,
a reference to an interesting looking dissertation by one M. C Acree.
If this is the M. Acree who occasionally posts to CSGNet (I mean you,
Mike;-)) I wonder if you could post some of your thoughts how
psychology came to be addicted to statistics. The reference to the
dissertation is:

Acree, M. C. (1978).Theories of statistical inference in psychological
research: A historico
critical study. Unpublished doctoral dissertation, Clark University,
Worcester, MA.

So it seem like the Acree fellow should know a lot about what I want
to know about. So, if it's you Mike, could you put down your eggnog
long enough to say something about the history of statistics in
psychology.

Thanks.

Best

Rick

···

--
Richard S. Marken PhD
rsmarken@gmail.com

12

[From Mike Acree (2008.12.21.1740 PST)]

Rick Marken (2008.12.21.1450)]--

While looking for some information about the history of the use of
statistics in psychology I ran across a text called "Statistics in
Psychology: A Historical Perspective" by Cowles and, I saw, in there,
a reference to an interesting looking dissertation by one M. C Acree.
If this is the M. Acree who occasionally posts to CSGNet (I mean you,
Mike;-)) I wonder if you could post some of your thoughts how
psychology came to be addicted to statistics. The reference to the
dissertation is:

Acree, M. C. (1978).Theories of statistical inference in psychological
research: A historico
critical study. Unpublished doctoral dissertation, Clark University,
Worcester, MA.

So it seem like the Acree fellow should know a lot about what I want
to know about. So, if it's you Mike, could you put down your eggnog
long enough to say something about the history of statistics in
psychology.

I'm still working, 30 years later, to turn the dissertation into a book.
Meanwhile, I gave a talk a couple of years ago summarizing the content,
"Why the Concept of Statistical Inference Is Incoherent, and Why We
Still Love It." Although I didn't read the paper, I wrote it out, in an
informal style for oral delivery rather than publication. It was also
designed for a general, nontechnical audience. You may recognize a
paragraph of two from my unplanned remarks at the 1994 PCT conference in
Durango. The current draft of the book is about 20 times as long, so,
if there are points where you would like more elaboration, I can
probably supply it. But this paper would be the place to start; it's a
good overview of what I think. And comments of any kind are most
welcome.

I might add that I haven't contributed much to the discussions of
statistics on the Net, just because Richard has been very reliably quick
and capable. I have very much appreciated both his and Bill's views on
the subject.

Thanks for your interest!

Mike

acree.doc (114 KB)

13

[From David Goldstein (92008.12.22.2008.0641 EST)]

About [From Mike Acree (2008.12.21.1740 PST)]

Thanks Mike.
I skimmed the essay.
I especially was interested in your comments about statistics and research in Psychotherapy.
Are you familiar with William Stephenson and his Q Methodology approach?
David

14

[From Mike Acree (2008.12.22.2008.0958 PST0]

David Goldstein (92008.12.22.2008.0641 EST)--

Are you familiar with William Stephenson and his Q Methodology

approach?

I first read about the Q technique over 40 years ago, and never saw any
value in it.

Mike

15

[From Rick Marken (2008.12.22.0925)]

Mike Acree (2008.12.22.2008.0958 PST0)--

That's a great paperMike. Very interesting stuff and extremely well
written. I have been re-reading Bakan's essay on the significance test
(in "On Method"); he was a darn good writer, too. But not quite as
good as you.

But I do think that all the complaints (like yours and Bakan's) about
the significance test have had _some_ impact on how the results of
psychological research are reported. In almost every recent report of
an experimental result published in journals like _Psychological
Science_ you see not only the usual significance level (p<.01 or
whatever) but also an eta squared value (proportion of variance in the
DV accounted for by variation in the IV); this is the measure I'm
focusing on since it can be taken as a measure of goodness of fit of
the open-loop causal model (the general linear model) of behavior to
the data.

But yours is a really terrific paper; it's got great historical
information and a nice argument regarding why the significance test
just won't go away. You should publish it somewhere so that others can
enjoy it.

David Goldstein (92008.12.22.2008.0641 EST)--

Are you familiar with William Stephenson and his Q Methodology

approach?

I first read about the Q technique over 40 years ago, and never saw any
value in it.

I feel the same way about it.

Thanks again for that wonderful paper!!

Best

Rick

···

--
Richard S. Marken PhD
rsmarken@gmail.com

16

[From Bill Powers (2008.212.22.1044 MST)]

Rick Marken (2008.12.22.0925) --

In almost every recent report of
an experimental result published in journals like _Psychological
Science_ you see not only the usual significance level (p<.01 or
whatever) but also an eta squared value (proportion of variance in the
DV accounted for by variation in the IV); this is the measure I'm
focusing on since it can be taken as a measure of goodness of fit of
the open-loop causal model (the general linear model) of behavior to
the data.

It's only gradually sunk into my head that your approach is a great way to get psychologists to start paying attention to the models they use. I remember asking David Goldstein some time ago what psychologists would think of trying to predict behavior by using the regression equation (which I take it is your meaning of the General Linear Model). His answer: psychologists don't use it that way. Statistics is used for description, but not for prediction, apparently. I hope you get some publications out there; it will be very interesting to see what the reaction is.

Best,

Bill P.

17

[From Bill Powers (2008.12.21.2007 MST)]

Mike Acree (2008.12.21.1740 PST) --

I'm still working, 30 years later, to turn the dissertation into a book.
Meanwhile, I gave a talk a couple of years ago summarizing the content,
"Why the Concept of Statistical Inference Is Incoherent, and Why We
Still Love It." Although I didn't read the paper, I wrote it out, in an
informal style for oral delivery rather than publication. It was also
designed for a general, nontechnical audience. You may recognize a
paragraph of two from my unplanned remarks at the 1994 PCT conference in
Durango. The current draft of the book is about 20 times as long, so,
if there are points where you would like more elaboration, I can
probably supply it. But this paper would be the place to start; it's a
good overview of what I think. And comments of any kind are most
welcome.

I am stunned, absolutely bowled over, by this paper. I hope others on CSGnet are, too. I am, of course, used to receiving cogent remarks from you, and useful knowlege, and witty metaphors. I now realize what a risk I have been taking in arguing against you on any subject, pointing my little popgun at your 16-inch cannon, capable of hurling a Volkswagen 20 miles.

All I can think of now is to ask where this magnificent paper should be published. It would be a perfect way to announce the promise of a book by you, and a sure guarantee of your finding a publisher when you do finish at least part of the book. I appeal to CSGnet -- with your permission, I hope, Mike -- to devote some serious thought to this question. My first thought was that this would make a first-rate New Yorker article in the class of John McPhee's writings on geology. It would be, like McPhee's articles, well over the heads of even the intelligent New Yorker audience -- and they would love it for that, and feel they had learned many important things from you because of that. There may be other suitable venues, but I am sure of one thing: it should not disappear into a scientific journal.

That said, it is clear now who should write the definitive book on the relationship of PCT to the world of psychology. But that can wait. You have laid out a complete complex thought that needs to be recorded and made accessible to all. I think it will open doors for you.

Best,

Bill P.

18

[From Mike Acree (2008.12.22.1232 PST)]

Rick Marken (2008.12.22.0925)--

That's a great paperMike. Very interesting stuff and extremely well

written. I have been re-reading Bakan's >essay on the significance test
(in "On Method"); he was a darn good writer, too. But not quite as good
as >you.

Thanks so much, Rick, for your very generous response. I wish whatever
writing talents I have didn't promptly desert me when I start writing
about economic and political theory.

But I do think that all the complaints (like yours and Bakan's) about

the significance test have had _some_ >impact on how the results of
psychological research are reported. In almost every recent report of an

experimental result published in journals like _Psychological Science_

you see not only the usual >significance level (p<.01 or

whatever) but also an eta squared value (proportion of variance in the

DV accounted for by variation in the >IV); this is the measure I'm
focusing on since it can be taken as a measure of goodness of fit of the
open->loop causal model (the general linear model) of behavior to the
data.

I agree that the criticisms have had that effect (notwithstanding my
blanket denial in the paper), and that it's one, moreover, whose full
impact may not yet have been felt. Cohen's call, in 1962, for power
analysis was ignored for years, partly because calculating power
requires stipulating an effect size of interest, and nobody wanted to
think about whether a 2-point average difference on the Beck Depression
Inventory was of clinical significance. Cohen came to the rescue with
his definitions of small, medium, and large effects; despite his
strenuous warnings against taking them as conventions, that's exactly
what psychologists did, so they are still spared having to think about
what their numbers mean. If, through the use of effect sizes, they ever
came to acquire a feel for magnitudes on the scales they were using,
they could see that the _p_ value was superfluous, and they could just
look and see whether an effect of interest had been obtained. (Not
quite; sample size is still relevant. A single toss of a coin, in a
test for bias, would yield the maximal effect size of 1--if it came up
heads, the statistical inference would be that the coin was
two-headed--but would carry little weight. The problem with the _p_
value, from this perspective, is that it bundles effect size and sample
size together in a way that can't easily be disentangled.) But all of
this is a long way, as you and I agree, from an individual-based
psychology.

Thanks again for your interest and enthusiasm.

Mike

19

[From Mike Acree (2008.12.22.1234 PST)]

Bill Powers (2008.12.21.2007 MST)--

I am stunned, absolutely bowled over, by this paper. I hope others on

CSGnet are, too. I am, of course, >used to receiving cogent remarks from
you, and useful knowlege, and witty metaphors. I now realize what a

risk I have been taking in arguing against you on any subject, pointing

my little popgun at your 16-inch >cannon, capable of hurling a
Volkswagen 20 miles.

Well, please allow me to be absolutely bowled over. Coming from the
popgun author of what I regard as the most important book ever written,
that compliment is the greatest I will ever receive. I will have to
find a head clamp very soon, before the swelling gets too severe. I
think some of my previous audiences have found the paper entertaining,
but I'm totally unaccustomed to having anyone find any of my writing
persuasive. To my own eyes, in fact, the present paper seems glib in
the extreme, with practically every sentence begging for elaboration or
justification; I wouldn't have undertaken such a drastic condensation
except for a strictly time-limited oral presentation. So I'm sure prior
agreement had something to do with its reception in this case. But that
doesn't mean my breathing has returned to normal.

All I can think of now is to ask where this magnificent paper should be

published. It would be a perfect >way to announce the promise of a book
by you, and a sure guarantee of your finding a publisher when you do

finish at least part of the book. I appeal to CSGnet -- with your

permission, I hope, Mike -- to devote some >serious thought to this
question. My first thought was that this would make a first-rate New
Yorker article >in the class of John McPhee's writings on geology.

It would be, like McPhee's articles, well over the heads of even the

intelligent New Yorker audience -- and >they would love it for that, and
feel they had learned many important things from you because of that.

There may be other suitable venues, but I am sure of one thing:
it should not disappear into a scientific journal.

A pleasant surprise to be jolted out of the ethnocentrism of
academentia: I had not imagined any publication possibilities other
than seeing the paper disappear into a scientific journal. There are
problems with either kind of venue; for a journal, filling in what I
would expect to be the necessary supporting arguments would make it far
too long, which is why I haven't done anything with it so far. And I
had imagined that the subject was too esoteric for a popular
magazine--though I have certainly shared your appreciation of many of
the scientific articles in _The New Yorker_. And maybe the obstacles
there are the less formidable. Thanks very much for the encouragement
in that direction, in any case.

All best,

Mike

20

[From Mike Acree (2008.12.22.1235 PST)]

Bill Powers (2008.212.22.1044 MST)--

I remember asking David Goldstein some time ago what psychologists

would think of trying to predict >behavior by using the regression
equation (which I take it is your meaning of the General Linear Model).
His >answer: psychologists don't use it that way.

Statistics is used for description, but not for prediction, apparently.

Regression equations can legitimately be used in contexts, like college
admissions, where the interest is purely pragmatic rather than with
understanding of processes, and the concern is wholly with aggregates
rather than individuals. These, as David indicates, are not the typical
applications in psychological research. Psychologists actually seem to
imagine that these models do reflect causal processes. But why bother
with thinking, when you can get paid so handsomely without it? The
problem again, as I see it, is the third-party system of payments for
psychological research that was set up after WWII, and greatly expanded
after Sputnik. It is also close to a single-payer system, with
government funding of research having crowded out most of the private
funding. There are some philanthropists who would support this kind of
work, but not that many. What is important to members of Congress is to
be able to say that they have allocated a billion dollars to, say, AIDS
prevention research, and to have set up a system for getting the money
into the hands of the best investigators, as determined by their peers,
who are doing the same stupid kinds of things. If the problem doesn't
get solved, it's not the fault of Congress; it just means that more
money needs to be allocated. And the problem is not likely to get
solved, because then thousands of people would be out of a job. The
atmosphere at the UCSF Center for AIDS Prevention Studies on the day in
1996 when protease inhibitors were announced as a possible cure was one
of panic. So the present research regime will continue, as I suggested
at the end of the paper, until the money runs out. It's starting to,
but the public sector will be kept going much longer than the private,
where accountability matters (unless you're "too big to fail").

Cowles, incidentally--whose mention of my dissertation started this
thread--defends the present research regime precisely because it "_is_ a
success." He doesn't clarify that it is an economic rather than a
scientific success. I use him in my book as a wonderful example of
intellectual vapidity.

Mike