# EAB and PCT **URL:** \ **Category:** CSG1996\ **Created:** [April 7, 1996, 12:44am UTC](http://discourse.iapct.org/t/eab-and-pct/3713 "1996-04-07T00:44:08Z")\ **Posts on this page:** 13\ **Page:** 1

**Author:** ![William\_T\_Powers4](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/w/977dab/32.png) [@William\_T\_Powers4](http://discourse.iapct.org/u/William_T_Powers4)\ **Post date:** [April 7, 1996, 12:44am UTC](http://discourse.iapct.org/t/eab-and-pct/3713/1 "1996-04-07T00:44:08Z")

[From Bill Powers (960406.1640 MST)] Bruce Abbott (960406.1255 EST) -- Research by Sidman, by Dinsmoor, and by Herrnstein and Hineline strongly suggested that rats could somehow integrate events over time and respond on the basis of average shock frequency reduction You're going to have to explain that one a bit further. What does it mean to say that rats respond "on the basis of" something? Is this the same as saying they response \_to\_ something? Is what they are responding to the average shock rate, or the average shock rate \_reduction\_? Or is what is meant that they emit responses (i.e., act) \_in order to\_ reduce shock rate? Or is your odd wording an attempt to \_avoid\_ saying that, while still preserving the same meaning? Data from concurrent and concurrent chains schedules indicated that the proportion of responding emitted on one of two keys tended to match the relative rate of reinforcement associated with the schedule programmed on that key (for VI schedules, at least) ... We've been through this before. I think that the interpretation of "matching" phenomena comes as close to fudging the data as anything I've seen in this field. Is exclusive preference "matching?" Why doesn't the principle say that the rate of responding is proportional to the schedule parameter, or some other such unequivocal proposition? Could it be because there is no clear way to say what matching means that will make the data fit the hypothesis? When you say that the behavior "tended" to match, you also imply that it tended NOT to match. What measure of matching is used? What would perfect matching be? How much matching error must occur before you discard the idea of matching? > **···** > > ----------------------------- > Sorry, Bruce. I really don't want to get back into this. What we're > doing with your rat experiments is real science that will lead to solid > results, and we won't have to ambiguate our language to talk about them. > You have an investment in EAB, and want to present it in the best light, > but that's really your problem, not mine. I don't want to fall back into > EAB-bashing. And I find the defenses unconvincing. So let's turn to what > we agree about and keep on keeping on. > ---------------------------------------------------------------------- > Best, > > Bill P. ---

**Author:** ![Bruce\_Abbott](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/b/ba8739/32.png) [@Bruce\_Abbott](http://discourse.iapct.org/u/Bruce_Abbott)\ **Post date:** [April 7, 1996, 3:44pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/2 "1996-04-07T15:44:39Z")

[From Bruce Abbott (960407.1045 EST)] > Bill Powers (960406.1640 MST) -- > Bruce Abbott (960406.1255 EST) -- > > Research by Sidman, by Dinsmoor, and by Herrnstein and Hineline > strongly suggested that rats could somehow integrate events over > time and respond on the basis of average shock frequency reduction > > You're going to have to explain that one a bit further. What does it > mean to say that rats respond "on the basis of" something? Is this the > same as saying they response \_to\_ something? What I was trying to get across is the notion that the organism is sensitive to the rate of events over time, and can distinguish the reduction in rate that occurs as a function of its behavioral output on the manipulandum. In a reinforcement-based explanation, the reduction in shock frequency would serve as the reinforcer for responding. > Data from concurrent and concurrent chains schedules indicated that > the proportion of responding emitted on one of two keys tended to > match the relative rate of reinforcement associated with the > schedule programmed on that key (for VI schedules, at least) ... > > We've been through this before. I think that the interpretation of > "matching" phenomena comes as close to fudging the data as anything I've > seen in this field. You must have some strange new definition of "fudging the data." In normal scientific discourse, fudging the data means altering the numbers to make them fit the theory. It's a serious charge and one I wouldn't be tossing around lightly. It another thing entirely for one to conclude that some function \_fits\_ the data when in fact the fit isn't all that good. This, I think, is what you intend to convey, but what you actually said leaves a much more sinister implication than is warrented. > Is exclusive preference "matching?" Why doesn't the > principle say that the rate of responding is proportional to the > schedule parameter, or some other such unequivocal proposition? Could it > be because there is no clear way to say what matching means that will > make the data fit the hypothesis? Matching as a description of performance was developed for concurrent VI-VI schedules; later it was noted that "matching" \_could\_ be used to describe performance on concurrent ratio schedules, but that it would be only trivially true. So let's stick to the situation for which the description was intended, for starters. The principle as initially formulated did apply to the schedule parameters. However, where there were large differences in VI values between keys, it was soon noticed that using the obtained rather than scheduled rates provided a better fit. We both know why, but as a \_description\_ of a relationship between variables matching still held. > When you say that the behavior > "tended" to match, you also imply that it tended NOT to match. What > measure of matching is used? What would perfect matching be? How much > matching error must occur before you discard the idea of matching? As usual in any scientific work, fits can be evaluated only within the limits of precision of the measure. Within the limits of precision in the original studies, relative response rates matched relative reinforcement rates. Perfect matching would have been identical values for relative response rate and relative reinforcement rate, but one has to allow for measurement error (even in physics). By now a large number of studies have investigated matching. Measurement precision has improved, and it has been shown that matching as a general principle does not hold. > Sorry, Bruce. I really don't want to get back into this. What we're > doing with your rat experiments is real science that will lead to solid > results, and we won't have to ambiguate our language to talk about them. > You have an investment in EAB, and want to present it in the best light, > but that's really your problem, not mine. I don't want to fall back into > EAB-bashing. And I find the defenses unconvincing. So let's turn to what > we agree about and keep on keeping on. I didn't think I was presenting an argument -- certainly not an argument for the reinforcement view. I was offering a bit of history to show how empirical findings of the early 1960s led to a line of enquiry concerning global principles like optimization and melioration. This presentation was offered to show how these developed naturally from the data that were developed at that time. You had asserted that going after such global principles first puts the cart before the horse, that one should begin with the data. I was showing how the theories actually emerged in the context of examining the data. For some reason you wish to characterize this contribution as reflecting my "investment" in EAB (a charge you also levied agaist Chris Cherpas). Well, in my view, you wish to pontificate about things of which you know little, making smug charges of "fudging data" and the like (without evidence), and it does not make you happy to have your nice little fantasies contradicted by someone more familiar with the facts. Regards, Bruce ---

**Author:** ![Richard\_Marken1](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/r/ed8c4c/32.png) [@Richard\_Marken1](http://discourse.iapct.org/u/Richard_Marken1)\ **Post date:** [April 7, 1996, 8:45pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/3 "1996-04-07T20:45:09Z")

[From Rick Marken (960407.1430)] Bruce Abbott (960406.1255 EST) -- > Research by Sidman, by Dinsmoor, and by Herrnstein and Hineline > strongly suggested that rats could somehow integrate events over time \>and respond on the basis of average shock frequency reduction Bill Powers (960406.1640 MST) -- > You're going to have to explain that one a bit further. What does it > mean to say that rats respond "on the basis of" something? Is this \>thesame as saying they response \_to\_ something? Bruce Abbott (960407.1045 EST) -- > What I was trying to get across is the notion that the organism is \>sensitive to the rate of events over time, and can distinguish the \>reduction in rate that occurs as a function of its behavioral output \>on the manipulandum. I think Bill's problem was the same as mine. You said that research "strongly suggested" that rats "respond on the basis of" a perception. Now I know, and Bill knows, that \_you\_ know that this is only what this research "strongly suggests" to researchers who don't know that animals are controlling. I'm sure neither Bill nor I would have been inclined to say anything about your comments if you had just made it a bit clearer that you were saying, not what \_you\_ thought the research strongly suggested, but what the EAB researchers thought the research strongly suggested. For example, it might have been clearer if you had said something like: Research by so and so strongly suggested that rats could perceive events integrated over time; unfortunately, these researchers mistakenly concluded that rats respond on the basis of these perceptions. Because of the way the research was conducted, these researchers failed to notice the possibility that these perceptions were controlled by the rat. Best Rick ---

**Author:** ![Bill\_Powers1](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/b/8e7dd6/32.png) [@Bill\_Powers1](http://discourse.iapct.org/u/Bill_Powers1)\ **Post date:** [September 12, 1997, 10:59am UTC](http://discourse.iapct.org/t/eab-and-pct/3713/4 "1997-09-12T10:59:43Z")

[From Bill Powers (970912.0400 MDT)] I guess until this gets said I don't get back to sleep. Some ideas are just so simple there there doesn't seem to be any way to express them. The difference between EAB and PCT is one of these ideas. It's so obvious and elementary -- or anyway seems so at the moment -- that it's easy to find yourself going twice around the block just to go next door. First, what is a contingency? It's a relation among physical variables and nothing more. Every natural law is a contingency. Every dependency of one environmental variable on another one is a contingency. It makes absolutely no difference whether an organism's behavior or something else affects the independent part of the contingency, and it makes absolutely no difference whether the dependent part affects, is perceived by, or is otherwise associated with an organism. All that a contingency says is that if variable B is to change, one or more of the variables (A1, A2... An) on which it depends must change. This is a recognition that in the physical world, nothing happens spontaneously. Nothing moves of itself. Any physical variable is a function of other physical variables: B = f(A1, A2, ... An). In an operant conditioning situation, the world is set up so that the only way a certain consequence can be created is for certain antecedent events to happen in some particular way. If the consequence does occur, then one or more of the antecedents on which it depends must have occurred. If a necessary antecedent depends on a particular behavior, then the behavior must have occurred. So the consequence depends on at least one of the necessary behaviors' having occurred. What we observe is that some kinds of consequences, some of the time, are made to occur to a degree higher than background by behavior when it is possible for that to happen -- that is, when a contingency exists. Behavior will keep changing until certain consequences are made to repeat at a non-chance level. Suppose we change the contingency: now a \_different\_ behavior will produce the \_same\_ consequence. We observe the same thing: behavior will change until it produces the same consequence as it did before. What we usually find is that whatever behavior will produce certain consequences, that behavior will eventually be produced. Putting all these observations together, we can arrive at a clear conclusion: the consequence produced by a given behavior has no particular amount or direction of effect on behavior. We can show that the same consequence will be produced by one behavior as by a different one, and that it may even be produced by one behavior or its opposite. The only factor that remains the same across these different conditions is the consequence. Whatever the form of the contingency, the behavior will change until the same consequence as before is produced by it. No matter what behavior must be performed (within the limits of possibility), the food pellets will be delivered and eaten. Since the production of the consequence remains the same over a set of different behaviors and contingencies, its occurrance cannot explain \_any\_ of the behaviors that produce it. If taken as a cause of one behavior that does occur, it can't also be taken as the cause of a different behavior that didn't occur this time but did occur at another time, or as the cause of a behavior directed oppositely, which also didn't occur. Its causal properties would have to change with each change of contingency, so as to cause exactly the behavior needed to produce itself, no matter what that behavior might be. This renders the concept of the consequence as a cause vacuous. It is a cause that has the property of being able to cause whatever effect is observed, and that means it is not a cause at all. What we actually observe is that behavior changes in such a way as to keep producing the same consequence, whenever a change in environmental properties occurs. The essential vacuousness here is not visible when one considers only one contingency and one consequence, so there is only one behavior that can produce the consequence. Nor it is visible when different consequences are made to result from a given behavior. The critical case is where different behaviors are necessary, because of different contingencies, to produce the same consequence. Only when we consider the proposed effect of consequences on behavior across different experiments related in this way can we see that consequences actually have no causal relation to behavior. We're talking, of course, about the basic phenomenon described by William James, to no avail, 100 years ago: variable means achieving constant ends. This observation was ignored, leaving the way open to behaviorism and to Pavlov's concept of reinforcement. Best, Bill P. ---

**Author:** ![HANS\_BLOM2](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/h/f17d59/32.png) [@HANS\_BLOM2](http://discourse.iapct.org/u/HANS_BLOM2)\ **Post date:** [September 15, 1997, 12:57pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/5 "1997-09-15T12:57:21Z")

[Hans Blom, 970915b] (Bill Powers (970912.0400 MDT)) > Some ideas are just so simple there there doesn't seem to be any way > to express them. Ideas only \_appear\_ simple. No idea truly is. Explanations have no bottom, regrettably. > First, what is a contingency? It's a relation among physical > variables and nothing more. Every natural law is a contingency. > Every dependency of one environmental variable on another one is a > contingency. It makes absolutely no difference whether an organism's > behavior or something else affects the independent part of the > contingency, and it makes absolutely no difference whether the > dependent part affects, is perceived by, or is otherwise associated > with an organism. > All that a contingency says is that if variable B is to change, one > or more of the variables (A1, A2... An) on which it depends must > change. This is a recognition that in the physical world, nothing > happens spontaneously. Nothing moves of itself. Any physical > variable is a function of other physical variables: B = f(A1, A2, > ... An). Strange. When I offered this same argument in the past -- that the world shows law-like behaviors -- you rejected it, with the argument that disturbances -- unlawlike behaviors -- are overwhelmingly the rule. Now what is it, Bill? Are organisms controllers because they effectively "reject" disturbances, or because they learn the laws of the world? Or do the two go hand in glove? Right, contingencies are relations. That is simple. But how come that rats can get to know -- and use -- only some contingencies and not others? Why is that different for pigeons or for humans? What are the limitations, why do they exist, and why are they so strongly species- specific? That's \_not\_ simple. Given the fact that we humans can perceive a lot of contingencies that rats and pigeons cannot, one may extrapolate and wonder how limited we humans are in this respect, and how much lawfulness there is out there where we only believe we see "disturbances". Why did it take millenia before someone discovered the relation F=ma which we now find so obvious? > Suppose we change the contingency: now a \_different\_ behavior will > produce the \_same\_ consequence. We observe the same thing: behavior > will change until it produces the same consequence as it did before. > What we usually find is that whatever behavior will produce certain > consequences, that behavior will eventually be produced. You skip a step. When the contingency is changed, the first thing that is observed (both by the rat and the external observer) is that the \_same\_ behavior produces a \_different\_ consequence. It must be this perception (of failure) that prompts the animal to try different behavior. Until -- at long last, after much exploration, maybe -- it discovers some behavior that realizes the original desire. Or not: if pushing the lever does not produce pellets anymore, no adequate behavior is left, no control is possible any more. Discovering the contingency preceeds its use. Learning preceeds using the knowledge that is learned. Simple? > Putting all these observations together, we can arrive at a clear > conclusion: the consequence produced by a given behavior has no > particular amount or direction of effect on behavior. We can show > that the same consequence will be produced by one behavior as by a > different one, and that it may even be produced by one behavior or > its opposite. But what \_is\_ constant? Two things. First, the rat will (within its limitations) learn the contingency. Second: the rat will use its knowledge of that contingency in "computing" its actions. If the physical contingency is broken, the rat will soon learn that its lever pushing actions are ineffective. As a result, it will stop acting (this way). In your analysis, the lack of discrimination between learning (getting to know the environment function) and acting (using the acquired knowledge of the environment function) is a great source of confusion. > Since the production of the consequence remains the same over a set > of different behaviors and contingencies, its occurrance cannot > explain \_any\_ of the behaviors that produce it. You oversimplify things. Your analysis presupposes both that \_some\_ alternative way to achieve the goal is available, and that this alternative can be discovered. > If taken as a cause of one behavior that does occur, it can't also > be taken as the cause of a different behavior that didn't occur this > time but did occur at another time, or as the cause of a behavior > directed oppositely, which also didn't occur. Its causal properties > would have to change with each change of contingency, so as to cause > exactly the behavior needed to produce itself, no matter what that > behavior might be. Do you see now how "perception of a relation" -- and its deployment in the control loop -- solves this apparent paradox? > This renders the concept of the consequence as a cause vacuous. It > is a cause that has the property of being able to cause whatever > effect is observed, and that means it is not a cause at all. What we > actually observe is that behavior changes in such a way as to keep > producing the same consequence, whenever a change in environmental > properties occurs. You miss something. An analysis of what \_does\_ remain constant (or gets "strengthened") might help... Greetings, Hans ---

**Author:** ![R\_Marken](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/r/8797f3/32.png) [@R\_Marken](http://discourse.iapct.org/u/R_Marken)\ **Post date:** [September 15, 1997, 3:30pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/6 "1997-09-15T15:30:10Z")

[From Rick Marken (970915.0820)] Hans Blom (970915) -- > A loop gain of 1000 hardly ever occurs in practice I'd guess that the loop gain of the typical biological control system is in the 10^3 to 10^6 range. In our tracking experiments the disturbance has only a fraction of its expected effect, suggesting a loop gain of at least 10^3. > I've only encountered such high loop gains in simulations ;-). You should try observing nature;-) > if one considers learning, that in the case of a high gain control > system (p = 0.999 r + 0.001 d) there is hardly any perception of the > disturbance. There is \_never\_ any perception of the disturbance by the control system that is controlling the "disturbed" perception; all the control system perceives is the combined result of disturbances and its own output. This is old, old news, Hans. Hans Blom (970915b) -- > Are organisms controllers because they effectively "reject" > disturbances, or because they learn the laws of the world? Or > do the two go hand in glove? Organisms are controllers because they exist in a closed-loop, negative feedback relationship with respect to their own sensory input. If they were not controllers they would not have been able to maintain themselves as organisms; they would just be dust (which is what happens to collections of matter that are organized "like a rock" rather than like a control system). Because organisms are controllers they automatically act to resist disturbances to the variables they are controlling. We know that they can do this controlling without learning the laws of the world because we can build artificial systems that control without knowing anything about the laws of the world. Nevertheless, it is possible that living systems do learn the laws of the world in order to control, but, so far, experimental tests (see [http://home.earthlink.net/~rmarken/ControlDemo/OpenLoop.html](http://home.earthlink.net/~rmarken/ControlDemo/OpenLoop.html)) reject this possibility. Bill Powers said: > Since the production of the consequence remains the same over a set > of different behaviors and contingencies, its occurrance cannot > explain \_any\_ of the behaviors that produce it. Hans Blom replies: > You oversimplify things. Your analysis presupposes both that > \_some\_ alternative way to achieve the goal is available, and > that this alternative can be discovered... Do you see now how > "perception of a relation" -- and its deployment in the control > loop -- solves this apparent paradox? I don't. Could you give the solution, please? Best Rick > **···** > > -- > Richard S. Marken Phone or Fax: 310 474-0313 > Life Learning Associates e-mail: rmarken@earthlink.net > [http://home.earthlink.net/~rmarken](http://home.earthlink.net/~rmarken) ---

**Author:** ![Myrexsw](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/m/858c86/32.png) [@Myrexsw](http://discourse.iapct.org/u/Myrexsw)\ **Post date:** [September 16, 1997, 2:46am UTC](http://discourse.iapct.org/t/eab-and-pct/3713/7 "1997-09-16T02:46:29Z")

i.kurtzer (970915) > [Hans Blom, 970915b] > > (Bill Powers (970912.0400 MDT)) Bill: > > All that a contingency says is that if variable B is to change, one > > or more of the variables (A1, A2... An) on which it depends must > > change. This is a recognition that in the physical world, nothing > > happens spontaneously. Nothing moves of itself. Any physical > > variable is a function of other physical variables: B = f(A1, A2, Hans: > Strange. When I offered this same argument in the past -- that \>the world shows law-like behaviors -- you rejected it, with the \>argument that disturbances -- unlawlike behaviors -- are \>overwhelmingly the rule. Now what is it, Bill? Are organisms \>controllers because they effectively "reject" disturbances, or \>because they learn the laws of the world? Or do the two go hand \>in glove? Are you suggesting that a monkey knows about tensile strength as it swings on a vine? Also, controllers do not "reject" , effectively or not, disturbances. > In your analysis, the lack of discrimination > between learning (getting to know the environment function) and > acting (using the acquired knowledge of the environment function) is > a great source of confusion. how did you just define learning as "getting to know the enviromental function"; did i miss something? was that a conclusion or a premise? i. ---

**Author:** ![HANS\_BLOM2](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/h/f17d59/32.png) [@HANS\_BLOM2](http://discourse.iapct.org/u/HANS_BLOM2)\ **Post date:** [September 16, 1997, 1:06pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/8 "1997-09-16T13:06:51Z")

[Hans Blom, 970916d] (i.kurtzer (970915)) > > Strange. When I offered this same argument in the past -- that > > the world shows law-like behaviors -- you rejected it, with the > > argument that disturbances -- unlawlike behaviors -- are > > overwhelmingly the rule. Now what is it, Bill? Are organisms > > controllers because they effectively "reject" disturbances, or > > because they learn the laws of the world? Or do the two go hand > > in glove? > Are you suggesting that a monkey knows about tensile strength as it > swings on a vine? Certainly. Although it may not know the (human) concept of tensile strength, it knows enough \_about\_ the tensile strengths of vines to be able swing. When you swung on vines (or ropes) as a kid, did you know the concept "tensile strength"? No, but you did acquire the knowledge (which you would find very hard to express in words) which ones would most likely support you and which ones would not. Would you maintain that it is important to know the concept of "tensile strength" in order to swing on a vine? Do you need to know how a car engine works before you drive a car? Do you need to know how the light bulb lights up before you flip the switch? Being able to \_use\_ a relationship does not imply being able to consciously "understand" or "explain" it. > Also, controllers do not "reject" , effectively or not, > disturbances. But you do understand what I intend to get across when I use these words? > > In your analysis, the lack of discrimination between learning > > (getting to know the environment function) and acting (using the > > acquired knowledge of the environment function) is a great source > > of confusion. > how did you just define learning as "getting to know the > enviromental function"; did i miss something? was that a > conclusion or a premise? Hey, that would make an interesting discussion! Yes, you did miss something: I've discussed extensively how a controller is only able to control relative to the environment in which it finds itself. It is the \_whole\_ loop, for instance, that determines what the loop gain is. A controller cannot arbitrarily decide what its gain should be. Suppose it picks the value 1000 but then it happens to find itself in an environment whose gain is 0.000001: we wouldn't consider the controller to be a controller at all... But back to your remark. First it was a conclusion. Simply replace the word "conclusion" by "higher level perception" and we're back to a PCT discussion. Then I recognized the reliability of this conclusion and I started to \_use\_ it -- as a premise, you could say -- for the "computation" of my actions, e.g. in the design of control systems. And with some success, I might say. But then, that "success" might appear arbitrary to you, because it would be success relative to \_my\_ goals, not yours. "It's all perception", some say. I extend this -- except, maybe, for the lowest levels of the HPCT hierarchy -- to "it's all conclusion". Would that be wrong? Greetings, Hans ---

**Author:** ![Bill\_Powers1](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/b/8e7dd6/32.png) [@Bill\_Powers1](http://discourse.iapct.org/u/Bill_Powers1)\ **Post date:** [September 17, 1997, 9:43pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/9 "1997-09-17T21:43:33Z")

[From Bill Powers (970917.1535 MDT)] Hans Blom, 970915b-- > > All that a contingency says is that if variable B is to change, one > > or more of the variables (A1, A2... An) on which it depends must > > change. This is a recognition that in the physical world, nothing > > happens spontaneously. Nothing moves of itself. Any physical > > variable is a function of other physical variables: B = f(A1, A2, > > ... An). > > Strange. When I offered this same argument in the past -- that the > world shows law-like behaviors -- you rejected it, with the argument > that disturbances -- unlawlike behaviors -- are overwhelmingly the > rule. Disturbances have nothing to do with contingencies or laws: they are extraneous influences added to the consequences of behavior. We measure laws under special conditions in which all extraneous influences have been excluded, to the best of our ability. Outside the laboratory, no such special conditions exist. However, once we are aware that disturbances do exist, we can measure them, too, and see that a control system resists their effects even without being able to sense or model them. We can then see that most of behavior consists of adjusting outputs to oppose the effects of unanticipated disturbances. > Now what is it, Bill? Are organisms controllers because they > effectively "reject" disturbances, or because they learn the laws of > the world? Or do the two go hand in glove? I have not become more tolerant of this mode of argument than I was before. I don't want to get involved. Best, Bill P. ---

**Author:** ![HANS\_BLOM2](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/h/f17d59/32.png) [@HANS\_BLOM2](http://discourse.iapct.org/u/HANS_BLOM2)\ **Post date:** [September 18, 1997, 10:38am UTC](http://discourse.iapct.org/t/eab-and-pct/3713/10 "1997-09-18T10:38:33Z")

[Hans Blom, 970918b] (Bill Powers (970917.1535 MDT)) > Disturbances have nothing to do with contingencies or laws: they are > extraneous influences added to the consequences of behavior. Ah, I see: you take disturbances as being fundamentally additive, whereas I prefer to not introduce this limitation as an a priori. You say, for instance, that perception = f (action) + disturbance whereas I pose that the more general model would be perception = f (action, disturbance) Sometimes I even favor the model perception = f-disturbance (action) where f-disturbance is a function (think of a function as a mapping) with a random component. The latter two models are mathematically equivalent; only the notation differs. The former (and yours) allows the interpretation that the two terms represent the two "causes" for my perceptions, (1) my actions, i.e. me as actor, and (2) unpredictable vagaries, modeled as a second "actor" on the world ("the hand of God"? "fate"?). The latter allows the interpretation that it is only my actions that determine what I perceive, but through a badly predictable or partly indeterministic world; with the implication that if only f-disturbance could be better known, I'd be in a situation with less noise, higher signal- to-noise ration, and better control. Psychologically speaking, I find the second interpretation far more empowering -- and in line with the equally empowering view that organisms are controllers ("you are in control!"). Moreover, mathematics shows that your model is the first order (series expansion) approximation of mine. If higher orders can be neglected (which we often do, for Occam's reasons of convenience and simplicity), all three models equivalent. Ah, models. Math says they're equivalent, yet interpretations may vary widely. Isn't that strange? > > Now what is it, Bill? Are organisms controllers because they > > effectively "reject" disturbances, or because they learn the laws > > of the world? Or do the two go hand in glove? > I have not become more tolerant of this mode of argument than I was > before. I don't want to get involved. May I remind you -- once more -- that it is \_the whole loop\_ which determines the characteristics of the control system? The environment contributes just as much to the most basic properties of the control system (e.g. loop gain, phase margin, stability, quality of control) as the controller. Either we take it as an a priori given (a divine miracle?) that organisms/controllers/humans just happen to be adapted to their environment or we study the ways in which this adaptation arose (in a species) and arises (in each individual). But that is just \_my\_ opinion. If you're not involved, others will do the job. Greetings, Hans ---

**Author:** ![Bill\_Powers1](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/b/8e7dd6/32.png) [@Bill\_Powers1](http://discourse.iapct.org/u/Bill_Powers1)\ **Post date:** [September 18, 1997, 3:25pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/11 "1997-09-18T15:25:29Z")

[From Bill Powers (970918.0837 MDT)] Hans Blom, 970918b-- > Ah, I see: you take disturbances as being fundamentally additive, > whereas I prefer to not introduce this limitation as an a priori. Yes, additive disturbances are one kind that is very common in real environments. They arise when the controlled variable is directly affected by influences in the environment other than the actions of the control system itself. You treat such additive disturbances as "noise," as if nothing can be done about them. But within the bandwidth of control, a control system of the PCT type can counteract the effects of additive disturbances; only the frequency components above the bandwidth of control remain unopposed. Even if the disturbance is "random," the components within the bandwidth of control will be opposed by corresponding fluctuations in the control system's action, so the lower-frequency effects on the controlled variable will be suppressed. By the way, don't tell me that \_your\_ model-based control system \_can\_ do this. I have determined that your program actually relied on real-time error information in opposing the disturbance; it was actually a closed-loop PCT control system and it always needed real-time perceptions to oppose the disturbance. If the perceptions were lost, your system would instantly lose the ability to oppose arbitrary additive disturbances. The other kind of disturbance is one that affects the form of the environmental feedback function, which you call "the plant." To compensate for this kind of disturbance, a model-based control system must adapt its internal model to reduce the difference between the predicted and actual perceptions. If any parameter of the plant is noisy, the effects of the noise can be opposed only up to the bandwidth of the adaptation process. In the PCT model, the effects of noisy parameters in the environmental feedback function can be opposed up to the full bandwidth of control, if the noise amplitude is not too great (so it grossly affects the loop gain). If the adaptation process is made to operate very fast, so as to match the performance of a PCT model, the main reason for using model-based control is lost: the ability to go on producing control-like outputs after the real-time input is cut off. The system can't distinguish between a disturbance and a total loss of input, and it will try to adapt as if a parameter had changed, with the same undesirable effects that we see in a PCT system when the input is cut off. > ... the two terms > represent the two "causes" for my perceptions, (1) my actions, i.e. > me as actor, and (2) unpredictable vagaries, modeled as a second > "actor" on the world ("the hand of God"? "fate"?). The latter allows > the interpretation that it is only my actions that determine what I > perceive, but through a badly predictable or partly indeterministic > world; with the implication that if only f-disturbance could be > better known, I'd be in a situation with less noise, higher signal- > to-noise ration, and better control. The PCT model can oppose the effects of even "hand-of-God" disturbances, whether additive or multiplicative, up to the high-frequency limit of control. Fortunately, in the real world, random effects tend to be of the 1/f sort; the higher the frequency, the smaller the effect of the disturbance. The bandwidth of control in real organisms seems to be such that all the large fluctutations, that have effects important to the organism, are cancelled out by control action; the remainder have effects too small to be of importance. There are exceptions, of course. > Moreover, mathematics shows that your model is the first order > (series expansion) approximation of mine. If higher orders can be > neglected (which we often do, for Occam's reasons of convenience and > simplicity), all three models equivalent. Except that in order to control in the absence of input for any appreciable length of time, the model-based system must adapt correspondingly slowly, so it loses the advantage of being able to counteract arbitrary disturbances within the bandwidth of control. The PCT model then becomes the model of choice, because it can nullify the effects of disturbances without having to predict them. > > > Now what is it, Bill? Are organisms controllers because they > > > effectively "reject" disturbances, or because they learn the laws > > > of the world? Or do the two go hand in glove? No, organisms do not, in general, and in ways other than metaphorically, "learn the laws of the world." I have tried to point out that a PCT system contains no literal model of the world, yet it controls perfectly well. Its output function can be very simple, yet it can control very complex processes. Your response has consistently been that if the PCT model does control, it MUST contain something that can be SPOKEN OF as a model of the world. This shows only that you have difficulty in distinguishing premises from conclusions. Your model-based control examples all have contained a literal simulation of the properties of the world lying between the system's output and its input. That is, they contain a literal model of the world. But the PCT model accomplishes the same degree of control without any such simulation. If you want to say that "absence of a simulation" is, through some rationalization, the same as "presence of a simulation," feel free -- but don't expect me to accept the argument. One last thing. I do wish that you'd give up your idea that the PCT model is not concerned with adaptation or learning. It is. It's just that adaptation and learning are dealt with as a separate problem from the problem of describing and predicting the performance of a system when adaptation and learning are complete. In the PCT model, the reorganizing processes are attributed to a distinct set of functions that act ON a control system. And it is recognized that most such adaptive processes take place on a time scale that is much slower than the time scale for performance of control. Your conception tries to combine the performance and adaptation aspects into a single system architecture, by using \_one particular method\_ of adaptation, a very computation-intensive method. It's a clever method, but it has drawbacks and it requires computations that are extremely unlikely to exist anywhere but at the higher levels of control. It certainly can't explain the way the spinal reflexes perform or adapt. You're confusing a clever invention that has certain nice features with a model of a real organism. Best, Bill P. ---

**Author:** ![HANS\_BLOM2](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/h/f17d59/32.png) [@HANS\_BLOM2](http://discourse.iapct.org/u/HANS_BLOM2)\ **Post date:** [September 23, 1997, 1:54pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/12 "1997-09-23T13:54:13Z")

[Hans Blom, 970923b] (Bill Powers (970918.0837 MDT)) Thanks for this post. It shows up a number of misunderstandings that may need to be rectified. In a later post I'll return to the theme of implicit versus explicit models. > ... additive disturbances are one kind that is very common in real > environments. I just wanted to remind you that the "additivity" of disturbances is a \_model\_, a way of perceiving (and, in the process, simplifying) the "world". It is both very common and very useful. If possible at all (sometimes it is not), I employ this simplification as well. > You treat such additive disturbances as "noise," as if nothing can > be done about them. But within the bandwidth of control, a control > system of the PCT type can counteract the effects of additive > disturbances; only the frequency components above the bandwidth of > control remain unopposed. We basically agree, even though we have a different "explanation". Where we differ is that you prefer to talk in terms of the \_frequency domain\_ and thus the \_frequency response\_ of a controller (where bandwidth is a central notion) and that I prefer to talk in terms of the the \_time domain\_ and thus the \_impulse response\_ or \_step response\_ of that controller (where bandwidth is not a meaningful notion but settling time, for instance, is). Both notions are mathematically equivalent: they are just transformations of each other. So neither is "more correct" than the other; they just employ a different terminology. Where you say "within the bandwidth of control, a control system can counteract the effects of disturbances" I would say "a control system can effectively counteract slowly varying but not rapidly varying disturbances". But that is essentially the same thing, looked at from different angles. But note also, that one formalism can express some "intuitive truths" much more easily than the other -- and the other way around. Why do I pester you so much with the formalism that you're less acquainted with rather than employing yours? Well, just for this reason. Using yours, for instance, you see no "model" inside a PCT controller except, maybe, in the most metaphorical manner. Using mine, however, I insist that there must be one, however hidden. Mathematically, there would be no "conflict"; just a very complex expression versus another, very simple one. That, I guess, is the reason why I'm not a single paradigm person... > Even if the disturbance is "random," the components within the > bandwidth of control will be opposed by corresponding fluctuations > in the control system's action, so the lower-frequency effects on > the controlled variable will be suppressed. We also saw this in my theodolite demo, in a quite analog fashion. An immediate (very high frequency) change of the disturbance could not be counteracted, but when the disturbance remained constant (\_very\_ low frequency), it was fully suppressed. There is a basic difference, however, between controllers with different criteria of what is "good" control. A frequency domain specification says that control must be accurate within a certain control bandwidth. A time domain specification may say, for instance, that a step change of the disturbance must be counteracted as well as possible. These are different criteria, and they will most probably lead to different designs. "But organisms were not designed", you might say. "But they were", I might counter, "implicitly. Organisms that weren't sufficiently able to cope with their environment just don't exist anymore. Those that are still alive were effectively designed by their environment". And who would be "right"? > By the way, don't tell me that \_your\_ model-based control system > \_can\_ do this [counteract a rapid disturbance, e.g. a step change]. Sure it can. Remember that it models the \_impulse or step response\_. If it discovers a step-wise change of the disturbance, it "knows" (through its model -- which may be more or less accurate) what the future perceptual effects of this step-wise change will be, if unopposed. And it is therefore able to oppose them with the right countermeasures immediately after the step change has been perceived -- which is, of course, always after the fact (if only one sample period). > I have determined that your program actually relied on real-time > error information in opposing the disturbance; it was actually a > closed-loop PCT control system and it always needed real-time > perceptions to oppose the disturbance. If the perceptions were lost, > your system would instantly lose the ability to oppose arbitrary > additive disturbances. Of course. And, if you remember, I showed exactly that in a demo. What you say is equivalent to saying that with eyes closed we don't see. What you say is true for \_any\_ controller, whatever its type. What is a PCT controller without its perception? Note that \_being without a perception\_ is NOT the same as \_having a perception of value zero\_ (a matter of great misunderstanding). > If the adaptation process is made to operate very fast, so as to > match the performance of a PCT model, the main reason for using > model-based control is lost: the ability to go on producing > control-like outputs after the real-time input is cut off. Please enlighten me: how could there possibly be \_any\_ (let alone "very fast") adaptation when the real-time input is cut off? When there can be no adaptation/learning, we effectively use only what we learned in the past, although we also ought to be less certain about what we (think we) know. That's what an adaptive controller does. That's also a pretty accurate description of someone returning to a city that he hasn't seen or heard about for a long time: expect the same, but don't be too certain about it... By the way, how does the PCT model handle (un)certainty? > The system can't distinguish between a disturbance and a total loss > of input... A system \_ought to be able to\_ make this distinction. An adaptive controller must, but in practice the distinction is often hard-wired in. Just like in us humans, who just seem to know that with our eyes closed we don't obtain (much) information about the world out there. There are, however, methods to implement this as a separate and extra mechanism in adaptive controllers. Kludges, mostly, so far; no good hard theory is available yet. > The PCT model can oppose the effects of even "hand-of-God" > disturbances, whether additive or multiplicative, up to the > high-frequency limit of control. In the time-domain description, one would say that the "hand-of-God" is pretty predictable (slow?). > Fortunately, in the real world, random effects tend to be of the > 1/f sort; the higher the frequency, the smaller the effect of the > disturbance. Yes, that helps to better predict things ;-). > ... in order to control in the absence of input for any appreciable > length of time, the model-based system must adapt correspondingly > slowly, so it loses the advantage of being able to counteract > arbitrary disturbances within the bandwidth of control. The PCT > model then becomes the model of choice, because it can nullify the > effects of disturbances without having to predict them. The PCT model becomes the model of choice \_in the absence of input for any appreciable length of time\_? I'm flabbergasted: the PCT model \_cannot\_. It always depends on input being there and being compared to the reference. If there is no input (NOT input = 0!), there can be no PCT control. At least not until you've actually implemented the imagination mode! > No, organisms do not, in general, and in ways other than > metaphorically, "learn the laws of the world." I have tried to point > out that a PCT system contains no literal model of the world, yet it > controls perfectly well. And I've tried to point out that even a PCT system \_must\_ contain some "model" of the world, in whatever form. I don't care whether that model is "literal" or not, whatever you mean with that. Finally, since I recognize that \_any\_ model is a metaphor, I fully agree with your sentiment that organisms only metaphorically "learn the laws of the world". Agreement at last! Greetings, Hans ---

**Author:** ![William\_T\_Powers2](http://discourse.iapct.org/letter_avatar_proxy/v4/letter/w/c67d28/32.png) [@William\_T\_Powers2](http://discourse.iapct.org/u/William_T_Powers2)\ **Post date:** [October 22, 1994, 4:40pm UTC](http://discourse.iapct.org/t/eab-and-pct/3713/13 "1994-10-22T16:40:07Z")

[From Bill Powers (941022.0815 MDT)] Bruce Abbott (941020.1815) -- > Demonstrating control over behavior in EAB means identifying variables > that, when manipulated, can be shown to alter the behavior in > predictable ways. PCT says there are are such variables and that by manipulating them one can control behavior. The two classes of variables that can be used to control behavior are the feedback function (as in the schedule of reinforcement) and disturbances (not much used in EAB). By altering the form of the feedback function you force the organism to alter its behavior in order to maintain the former effect on its inputs; by applying disturbances directly to the controlled inputs (for example by arbitrarily adding or removing rewards), you again force a change in behavior for the same reason. In all cases, the organism is organized to maintain its own inputs at preferred levels; the behavior itself is varied as required to do this. That is why the behavior can be controlled by outside agencies; normally, the organism is not controlling its behavior but varying it as necessary to control the consequences of the behavior. > Usually the experimenter does not view himself or herself as > controlling; rather it is the environment that does the controlling. This is a matter of language. In PCT, we say that controlling is a process of varying actions to produce a preselected perceptual (and actual) result. So if the experimenter manipulates variables and sees that they produce a predicted result, this is control. Of course control is best seen in the presence of disturbances. If some extraneous factor like a flapping curtain or sticking of the key disturbs the behavior that the experimenter is predicting, so it doesn't fit the prediction, the experimenter will do something to oppose the effects of the disturbance -- remove the cause, shield the organism from the effects, or what have you. The experimenter will be satisfied when the observed behavior again matches the reference level, the predicted behavior. As Rick Marken points out, for the environment to "control" the behavior, it would have to be pretty smart (as we use the term control in PCT). Control is varying an action until its consequences are in, or return to, a desired state. The controlling that the experimenter does is mostly finished by the time the final experiment is carried out for publication. The schedules of reinforcement have been chosen and tweaked and the amount and quality of the reinforcers have been adjusted to bring out the desired features of behavior. The animal has been brought to the proper body weight by adjusting its diet outside the experimental apparatus, and of course the animal has been placed in the apparatus. Usually, as I understand it, there has been a period of "shaping" during which the experimenter leads the organism into performing the behavior that the experimenter wants to see. Experimenter control is illustrated by your remarks to Tom about the COD: > ...the changeover delay prevents the pigeon from adopting a simple > strategy for earning reward from the two keys: simple alternation. On > concurrent VI-VI schedules the pigeon can maximize the rate of reward > only by responding on both keys. When it responds on one key the > schedule programmed on the other key just keeps running, so it becomes > increasing likely as time passes that a reinforcer will have been set > up on that key. In reinforcement-theory terms, because switching keys > produces (in the absence of a COD) immediate reinforcement fairly > often, switching behavior is itself reinforced by the immediate payoff. > Imposing the COD prevents immediate reinforcement following a switch > and prevents reinforcement of simple alternation between the keys (peck > left, peck right, peck left, etc.). Because switching guarantees no > reinforcement for the period of the COD, it discourages pigeons from > switching as often as they otherwise would. This is clearly control behavior on the part of the experimenter (as well as the pigeon). For some reason (which perhaps you can explain), the experimenter did not want to see the pigeon using a simple alternation as a way of providing rewards for itself. In order to prevent this strategy from succeeding, so that some other strategy would have to be used, the experimenter altered the conditions until the "simple alternation" would not work any more. So the experimenter had the goal of doing away with that kind of behavior, and by manipulating the conditions achieved it. That is certainly control in the PCT sense, and it was certainly done by the experimenter, not the environment. This is also a clear illustration of conflict between two control systems. The experimenter wants to see a certain kind of behavior from the pigeon and sets up a two-key situation which he thinks will produce it. The experimenter does not care about the food rewards, and so is willing to vary the experimental setup that produces them until the desired behavior is observed (perceived). The pigeon, which does not care how or where it pecks but cares very much about getting the food reward, uses the keys to supply itself with the reward, eventually discovering the (or a) most efficient method, which is to peck alternately on the keys. But this behavior does not match what the experimenter wanted to see -- perhaps it does not fit what the experimenter thinks of as "choice behavior." So somehow the experimenter has to alter the setup to make the simple alternation less effective. The experimenter reasons that if a change-over delay is used, the pigeon will not be rewarded immediately for pecking on the other key (that is, the pigeon's control of the reward input will be made less effective), and perhaps the pigeon will shift to some other strategy more like what the experimenter perceives as making a choice. So the experimenter introduces the COD, and keeps increasing its length until finally the pigeon does abandon simple alternation. Now the experimenter sees what he wants to see, and the pigeon finds a different action that will deliver what the pigeon wants, the reward. However, the experimenter must be somewhat less than satisfied because of having had to introduce an ad-hoc feature to the experiment, and the pigeon is somewhat less than satisfied because more effort is now required to obtain the same input. > **···** > > -------------------------------- > > > My guess is that it pecks on the key to which it has just switched: > > there is not time to do much else (usually around 2 seconds) and the > > COD contingency would work like a fixed-interval 2-s schedule on those > > occasions when a reinforcer was already set up on the VI schedule > > associated with the key. > > > The effect of varying the length of the COD has been investigated, and > > there has even been some work trying offer a unified account of > > behavior on concurrent schedules with and without COD. > > I have always been struck by the extreme complexity of EAB experiments. > What with mixes of schedules each with infinitely variable parameters, > adding CODs, adding arbitrary time-outs, varying the force-compliance > and direction of movement of keys and bars, changing the size and > gustatory qualities of rewards, introducing indirect effects (like the > changeover key), bringing in running wheels and access to mates, > adjusting the "richness" of the environment, and probably dozens more > adjustments of variables, I don't see how any coherent model of behavior > can be generated. If all these factors are important, then each one of > them must be explicitly varied in each experiment to see whether their > effects are interacting with the variables nominally being tested. If, > for example, reward size has been found to have an effect, then how can > you do an experiment in which the reward is "access" to food with no > control of how much food is ingested on each access, and indeed no > record being kept of the quantity ingested? > > It seems to me that EAB researchers, like those in the rest of > psychology, don't take each others' findings very seriously. Each > investigator, or group, starts essentially from scratch, ignoring all > the variables that others have tested and not even reporting on their > status. What was the size of the cage and the lighting? Were there > potential mates or rivals within eye, ear, or nose range? How much work > was required to depress the key or bar? What was the nutritive content > of the food pellets actually swallowed? What was the free-feeding rate > of ingestion of the type of reward used for each individual? How were > the animals handled? Since all these factors have been studied, and many > more, and have been found to have enough effect to warrant a > publication, why were these factors not at least noted and recorded as > part of the experimental conditions? If they were not, are we to > conclude that these other effects have ceased to exist, or that the work > which established them has been discredited? Is it not possible that the > effect seen in a given experiment would disappear or change markedly if > some other factor, known but not accounted for, happened to change? > > It's all much too complicated for my simple mind. > --------------------------------------------------------------------- > > > Animals do not display matching under most two-key conditions, although > > they tend to do well with VI-VI schedules. > > Isn't this begging the question a bit? When you say they "tend to do > well" on VI-VI schedules, what this tells me is that they don't show > matching behavior -- some do, perhaps, but some don't, so the matching > law isn't a law at all. If you have a real law of behavior, it's got to > work all the time, with essentially all organisms to which it applies. > And why on earth would one talk of a "matching law" if "animals do not > display matching under most two-key conditions"? To me, that suggests > that this law has in fact been disproven: it's not a law. Why are we > even talking about it? > ---------------------------------------------------------------------- > > > Judging from some films I've seen, pigeons working on these schedules > > don't spend all their time pecking on the keys. They occasionally turn > > away, perhaps to peck at the floor or as a way to space out responding. > > On especially long intervals they may exhibit signs of emotionality-- > > flapping their wings briefly, for example. An they sometimes check out > > the food magazine prematurely. Despite all this they manage to respond > > at a fairly uniform rate on the keys and usually manage to collect most > > reinforcers soon after they are set up. > > ----------------------------------------------------------------------- > I suspect that this accounts for the two curves we see on Fig. 7.18 in > Staddon's book. The curves show rate of responding versus rate of > rewards, for eight schedules. The two curves are very nearly congruent, > one being a magnified version of the other in BOTH dimensions. I beat my > brain to a pulp trying to find a model that would reproduce both curves > without requiring that most of the parameters be changed from one to the > other. Then I realized that if the animals were not spending all their > time pressing the bar, the differences in both dimensions would be > entirely accounted for without any change in the model. > The larger curve is for animals maintained at 80% of their free-feeding > body weight. This is like a 160-pound man being starved down to 128 > pounds. My guess is that the animals would spend very little time away > from the bar and the feeding dipper. The smaller curve is for animals > maintained at 98% of their free-feeding weight. The curve has the same > shape, but the numbers on both axes are nearly halved. This is what you > would see if the animals really responded just as they do at 80% body > weight, but spent only half their time at the bar. The data are > presented in terms of total presses per session and total rewards per > session, so there is no way to tell what the pressing rates and reward > rates were while the animal was actually engaged in the task. This is > why I need Motherall's raw data. I doubt that it exists any more. > > This guess is encouraged by the figure on the previous page, which also > has a large and a small curve of the same shapes, but in which the > difference in conditions was introduction of a running-wheel into the > cage. > ----------------------------- > You say you don't work with pigeons. What \_do\_ you work with? Getting > the kind of data needed for PCT modeling from the literature has proven > a frustrating job; what's needed is the raw data, a record of every key- > press and every reward against time, as well as observations of what the > animal was really DOING all of the time. If you're doing experiments, > all this data must be available. Do you have anything (simple) we could > start with? I really hate measuring figures with a millimeter rule > trying to get the numbers, without knowing how accurately the points > were plotted and printed or what the data for the individuals were. From > my few results so far, I'm confident that we can come up with a PCT > model that will predict behavior quite well, but to do this we need to > know the raw data, not published summaries of averages. In the model > that fits Staddon's (Motherall's) data, I had to estimate each schedule > by finding the nearest whole number that would match the plotted (and > measured) rates of behaviors and rewards, and I get different numbers > each time I measure some of the rather tiny values from the position of > the points. So no matter how well the model fits, I don't trust it. You > must have some data we could work with, or perhaps you could even devote > some time to doing a real PCT experiment for a simple situation. What > about it? > ----------------------------------------------------------------------- > Best, > > Bill P.