Hayley Clatterbuck, The Logic Problem and the Theoretician's Dilemma

While surfing around I ran across Hayley Clatterbuck's, essay,  The Logical Problem and the Theoretician’s Dilemma, Philosophy and Phenomenological Research doi: 10.1111/phpr.12331 in a journal I usually don't read. It is almost good, just tiptoes up to goodness and gets no farther, leaving some oddities and bad arguments along the way and huge opportunities untouched. It reminded me of two occasions. On one, Judea Pearl asked a dinner party of UCLA philosophers "Why don't you guys do anything?" On another, after hearing two hours of lectures by Alvin Goldman on the difference between "hard wired" and "soft-wired" capacities, Allen Newell asked: "So what has your laboratory discovered about hard wired capacities?"

Clatterbuck's problem is the warrant for attribution of understanding to creatures that are not human. She rightly sees that claims of behavioral evidence for such attributions come face to face with the behaviorist version of Hempel's Theoretician's Dilemma.  She first proposes that understanding can be established by having independent observable stimuli with correlated responses, inviting explanation by a mediating variable. She represents this by a graphical causal model, roughly

E1 :  S1                         R1 
                      U
E2: S2                           R2

with arrows S1 -> U; S2 -> U; U -> R1; U -> R2. Citing the Causal Markov Condition, which she modestly says she does not fully understand, she claims the graphical model above implies that R1 and R2 are correlated.  (That is correct but since S1 and S2 are mutually exclusive, they are associated, so perhaps they should be collapsed into a single variable with 2 values; but Clatterbuck does not want the experimental treatment to be a variable common cause of the results.) She rightly goes on to object that nothing says the mediating variable U has to be some state of understanding; it could be a lot of different things.  So she goes on to suggest that designs are needed in which U -> R1 is a positive association and U -> R2 is negative, or vice-versa.  I guess the idea is that understanding would produce positive associations in some circumstances and negative ones in others that were perceptually similar.  So here is a good reason for positing a mediating variable, essentially using Reichenbach's common cause principle, and an argument I don't fully understand for it's interpretation.

However that works out, her discussion is lexically odd.  She says that the graphical model shown, which produces (with Faithfulness) an association between R1 and R2 is "syntactical" but the revised model that produces a negative association is "semantic."  Associations are syntactic but negative associations are semantic?Since "syntactic" is a term of abuse in contemporary philosophy of science, I wonder at the rationale for her terminology.  But on to something more serious.

She argues, I think, that the schema illustrates a way round the Theoretician's Dilemma. Following John Earman, Clatterbuck argues that prior evidence, call it E,  provides “inductive support” for some theory t, and t entails (and hence predicts) some new phenomenon N which thus would not have been predicted without recourse to t.  Earman puts the argument in Bayesian terms, as does Clatterbuck.  But if t entails N then Pr(N, E) ≥ Pr(N, t, E) hence Pr(N | E) ≥ Pr(N | t, E) Pr(t | E) = Pr(t | E): the novel phenomenon is at least as probable on the prior evidence as is the theory on the same evidence.  The Bayesian could skip the theory and go directly to the predicted phenomenon.  So that doesn't work.

Towards the end of her essay, she reformulates the idea in a way that I think she takes to be just an elaboration of Earman's (bad) argument, but is not: “In a case of within‐domain extrapolation, an empirical regularity within a domain is redescribed in terms of a theoretical relation which is then extrapolated to unobserved cases of that same domain. In a case of cross‐domain extrapolation, empirical regularities in domain A and B are redescribed in terms of the same theoretical relation, and it is induced that what is true of A is also true of B.”

I read this suggestion this way: given data from cases in one domain, find "theoretical" features of those cases that hold in another domain, and use those invariant features to predict about data in this second domain.  That would be a reason for theories. 

Ok, how can that be done...what is the script, the recipe? How can such invariant theoretical features be found? Nada. Full stop in Clatterbuck's essay. My graduate student, Biwei Huang, has an illustration for neuroscience. Taking fMRI images from subjects in one laboratory, she identifies strengths of some neural causal relations ("effective connections" in contemporary neuropsychology jargon) that separate autistic subjects from normals. She then uses the presence (or absence) of these connections and their strengths inferred from  fMRI scans from another laboratory (another "domain")  to predict autistic versus normal in the second laboratory (actually, in each of several other laboratories). 

This is a pretty neat illustration of the invariance strategy whose suggestion I attribute to Clatterbuck. And it does defeat the Theoreticians Dilemma: you couldn't make comparably accurate predictions by, say, comparing the correlations among fmri signals in different brain regions in subjects in one lab with those in another lab. People have tried.  

Huang's example is just that, not a general procedure for learning theoretical invariants for cross-domain classification.  My colleague, Kun Zhang, has developed one, explicitly in those terms.  Of course, that leaves a lot of room for work on the description of general procedures for other kinds of cross-domain invariants, of which physics provides many examples, e.g., classical thermodyanmics.

Afterword: Goldman replied to Newell that there is a division of labor: philosophers help science by posing the problems and distinctions; psychologists investigate them in the laboratory. Newell said thanks, but psychologists have no trouble doing both jobs. 

References

B. Huang, Diagnosis of Autism Spectrum Disorder by Causal Influence Strength Learning from Resting-Stae fMRI Data, M.S. Thesis, Department of Philosophy, Carnegie Mellon University, 2018.

Gong, M., Zhang, K., Huang, B., Glymour, C., Tao, D., & Batmanghelich, K. (2018). Causal Generative Domain Adaptation Networks. arXiv preprint arXiv:1804.04333.

Remarks on Constructive Empiricism and on Nora Boyd, “Evidence Enriched,” Philosophy of Science, 85, 201

Counting the Deer in Princeton

Remarks on Constructive Empiricism and on Nora Boyd, “Evidence Enriched,” Philosophy of Science, 85, 2018

Once upon a time, philosophers thought that scientific theories are collections of statements about the world.  The statements have logical connections that could be studied mathematically by the idealization of formal languages, and the statements have semantic relations that could be studied mathematically by the idealization of model theory, supplemented by various accounts of how terms in the language or mathematical objects in the models relate to things one can see, hear or touch.  Then along came constructive empiricism, which kept the idealized models but did away entirely with the formalized language and the logical relations it characterized and said little about how mathematical objects in the models relate to things one can see, hear or touch.   

Rather belatedly, two difficulties with constructive empiricism were noticed. The first was, indeed, how the models relate to things we can see, hear or touch, a matter that is, after all, at the heart of empiricism. The answer given is so odd that one might have thought the author was just kidding. The idea is that the theorist has a mathematical data model, and either that model can be embedded in a model of the theory or it cannot be. Van Fraassen considers a theory T of the growth of the deer population in Princeton, and the theorist’s data model, a graph of the variation of the deer population over time. He writes: “Since this is my representation of the deer population growth, there is for me no difference between the question whether T fits the graph and the question whether T fits the deer population growth” (256). The question of whether the mathematical model describes the actual deer population (not for me, but in fact) does not arise; it is not even sensible.

Suppose we ask a scientist how the curve of deer population growth in Princeton was obtained, and we are told “For each of several years, I counted the number of hoof marks in Princeton and divided by 4.’” We advise the scientist that his curve may be a severe overcount, since the same deer makes many more than 4 hoof marks.  The scientist replies that there is no point to the challenges.  If the critics have a different theory, construct their own data model. Constructive empiricism, after all.

 Suppose a group of physicists launch a mass spectrometer aboard a satellite to record ion concentrations above the atmosphere. They fail to calibrate the instrument before launch, with the result that it returns values in wild disagreement with previous measurements. (This really happened with the Swedish Freya satellite.) Would the scientists use the data anyway to try to publish a new estimate of ion concentrations? Would referees and a journal editor not care?  Of course they would care, and what the scientists actually published was a procedure for calibrating the spectrometer in-flight.

No one who takes science seriously can take seriously this constructive empiricist account of how data and theory meet. Nora Boyd does. Her essay focuses on facts familiar to anyone who has read almost any scientific paper: scientific data typically are accompanied by ancillary information that records the provenance of the measurements: what instruments were used, how they were calibrated and shielded, what resolutions of space or time or other variables were obtained, how were the data censored, or clustered or transformed, what statistical procedures were used, how were the units selected for measurement or treatment, where and when the measurements were made, whether the study was blinded or double-blinded, etc. This sort of information is typically given in the body of scientific reports or in supplementary material or in documents attached to databanks.  

Framing her story as an extension of Van Fraassen’s, she claims the value of such ancillary information is twofold: it helps multiple data sources to be used for related problems or investigations or arguments and it “breaks underdetermination.” I agree it does the first, but not in a way that is accommodated by constructive empiricism. I doubt it does the second in any sense except that of allowing further tests of a theory or theories; if some other theory can account for all of the same possible evidence—Quine’s sense of underdetermination—combining data sets won’t distinguish them.  But the main thing such information does is something she ignores, something to which van Fraassen seems to think there is no point:  it gives assurances that the measurements have not been made by a process that disqualifies them as premises in the assessment of a theory or theories because the measurements are not faithful to the quantities claimed to be measured; and it provides information to investigate whether such assurances are unwarranted.  On constructive empiricist grounds, there is no point to such assurances and no point to arguments that quantities have been mismeasured, or to arguments that data treatments destroyed information, or to objections that in view the provenance of the data the wrong statistical procedures were used, or that the experimental design leaves open alternative explanations of the data whose possibility better designs would have eliminated etc. Boyd misses all of that, perhaps because once science is cast in a constructive empiricist framework, faithfulness to the phenomena, truth, is not the point.

Boyd’s suggestion that ancillary information helps in the proper use of multiple data sets for a question, or the same data set for multiple problems is of course correct, but it is unintelligible in the constructive empiricist framework.  And that is the second belatedly noticed problem with constructive empiricism. On the old-fashioned view, language provides linkages between models. Language makes the connections that a relation in one model is the same relation as in another model. As Hans Halvorson points out, there is no such connection in constructive empiricism, only so many disconnected models, so many monads. A theory that constrains quantities conditionally, Newtonian dynamics for example, has many models under different conditions. One would like to say that the force holding the planets in their orbits is the same as the force acting on pendula, and indeed Newton says just that. On the constructive empiricist reconstruction, these are just different models of the theory, and nothing identifies the property acceleration, in one model with the property, acceleration, in another.  On the old-fashioned philosophy of science that is one of the services of language. Boyd tell me (private communication) that she does not endorse this part of "constructive empiricism," and she does refer to "minimal empiricism." 

Minimal empiricism turns out to be bad wine in new bottles. Citing van Fraassen, she says data are acquired to a theoretical purpose, to support, or not, a particular theory, and data are empirical only with respect to such a purpose.  Being empirical for a purpose is just what has been called, since longtime, being relevant to a theory or hypothesis. So what determines that relevance?  No answer. If I collect data on the spread of California poppies is that relevant to a hypothesis about the acceleration of the universe? Is it if I say that is its purpose?  Of course, there is no theory of relevance in "constructive empiricism" either. If a theory combines dynamics for the universe with dynamics for the spread of poppies, and someone's "data model" for poppies fits into it, is that evidence for the dynamics I postulate for the universe?

Boyd is a new Ph.D from Pitt HPS, and it is not fair to take her to task. Who then?  Pitt HPS. They take smart young people and make them, well, without a sense of what it is personally to discover something worth discovering, even the development of an actually new idea. As Pitt HPS goes, so goes philosophy of science in America, pretty much.

Recent Books on Causation III: Carolina Sartorio, Causation and Free Will, Oxford, 2016

 Carolina Sartorio, Causation and Free Will, Oxford, 2016

The styles of philosophy change. Spinoza gave us axioms, from which it was patent his “theorems” did not follow. Hobbes, and Locke and Hume gave as long essays. Berkeley and Hume, dialogues.  Nowadays, philosophical style is more often like a video game with unspoken rules: the reader is told the author has a goal, followed by example, counterexample, perplex after perplex, which the author dispatches one after another, like so many arcade mopes, with occasional reverses to revive the dead and kill them again. Double tap. And, then, finally, the reader reaches The Theory. Or not.  Ellery Ells’ endlessly annoying Probabilistic Causality is like that, and so, less endlessly—hers is a short, dense book--is Carolina Sartorio’s Causation and Free Will. You can’t say Ells didn’t think hard about his topic, he did, and so evidently has Sartorio, but you can say that both of them, and a lot of other philosophers, could have made reading and understanding a lot easier by laying cards on the table to begin with. At least her syntax is not contrived to hide banality beneath bafflement.

Shelled and peeled, the story is this: an action is done freely by a person if (and I suppose only if) the person caused the action via a sequence of events that included, as actual causes, rational (given the person’s desires and beliefs) reasons for the act and absences of reasons not to do it, absences, again, as actual causes in “a normal, non-deviant way.” (p. 135).

How can absences of reasons be causes, you ask. Easy, you ate ice cream because you did not have a reason not to of the kind “I am allergic to ice cream” because you are not allergic to ice cream and you know it. So the absence of that reason was a cause of your eating ice cream. In the vernacular, we allow absences as causes all the time: my tomato plants died because I didn’t water them.  Of course, if metaphysicians take the vernacular literally and allow absences as causes then they  will have an infinity of them in every case: my plants died because Barack Obama did not water them, and so on.  Sartorio is content with that, and presumably content with an infinity of such ghost causes accompanying every cause that actually happens. Essentially, every ceteris paribus clause becomes an infinity of actual but non-actual (because absent) causes.

Absences as causes might seem gratuitous in her story. They are there because she wants to distinguish, on the one hand, between courses of action in which the agent would be sensitive to reasons against the action were the reasons real (the absent causes) and, on the other hand, courses of reasoning in which the agent would not be sensitive to similar reasons were they real (the absent non-causes).  Philosophy is in some places Humpty-Dumptyish, and metaphysicians are legally free to talk as they want, including saying that if in deciding to do something you would be sensitive to a reason, were you to have it, a reason that you do not in fact have, then the absence of that reason is a cause of what you do.  I don’t think such talk helps anything, and in science, where absences are ceteris paribus clauses or shorthands for unknown (or boring) positive details, it’s silly. 

Absences as causes necessitate recourse to “a normal and non-deviant way,” she argues, because the absence of a reason could be a cause of an effect because, were the reason to be present, that would cause some external process  (Sartorio likes examples with miraculous neuroscientists standing ready to intervene) to prevent the effect, and so the agent would be “sensitive” to the absence of the reason. 

Ever since it became abundantly clear that we are biological and physical machines, not just our bodies, as Descartes allowed, but the whole of us, as Helmholtz allowed, philosophers doing “moral psychology” have tried to reconcile us to the loss of the Thomistic/Cartesian fancy.  The plain fact seems to be that we do not have anything of the kind that Aquinas and Descartes claimed for us. So live with it.  Daniel Dennett (Elbow Room) assures us that we should be content, even happy with our state; it gives us everything we could want. He is wrong. We could want not to be like that, and most of us do. The that is a machine whose workings are determined—or at least caused—by forces that antedated us. The that is a person who has as a zygote or neonate been implanted with a device that determines her subsequent responses to her environment. We do not want to be like that even if nature did the implanting. To be in human bondage, and know it, is one of the metaphysical agonies.

One compatibilist response to the metaphysical agony is that it pines for an incoherence, that there could not thinkably be a system of the kind Descartes and Aquinas claimed us to be. But of course there could. We have perfectly clear mathematical theories of non-deterministic automata, whose transitions between states (Hilary Putnam once thought of them as mental states) are neither determined nor probabilistic.  The other compatibilist response is Orwellian, meaning changing the language. I think Sartorio’s response is of the Orwellian kind, but tempered. She says she has the intuition that if the human machine is formed by nature, well, its actions can be free. She doesn’t offer a survey of others’ opinions. Bless her, she elaborates only on the condition that her intuition is correct.

There remains the serious scientific project of how consciousness, and deliberation happen, and how they came about, and the sociological, anthropological project of understanding the conditions under which various communities claim free agency and when they do not, and how those conditions (which have evidently changed) come about as a social process, and perhaps the moral project of consoling those who agonize for the loss of free will, but there doesn’t remain anything metaphysical to do about freedom of the will.  Nothing, at least, of value.

Recent Books on Causation II, Douglas Kutach, Causation

Douglas Kutach, Causation, Polity Press, 2014

This, too, is an introductory book, but a good one.  The author mixes in historical sources with a wide ranging, and generally accurate and informative exposition of contemporary (i.e, since 1946) accounts of the metaphysics of causation. It has some sensible questions for readers. I would use it as a textbook, with some apologies to the students. What apologies?

1.     Like most other discussions of the metaphysics of causality, Kutach appeals to what we think we know for motivation, examples and counterexamples, but there is not the least hint of how causes can be, and are, discovered.

2.     While the book is less mathophobic than most philosophy texts, it is not always mathematically competent, doesn’t use what it does develop well, and presents mathematical examples that will be unenlightening or worse to most students.

a.     Early on “linearity” is discussed a propos of causal relations, but the author clearly doesn’t mean linearity. It is not clear what he means. Monotonicity perhaps, or non-interaction.

b.     Having introduced conditioning and independence and the common cause principle, there is a rather opaque discussion of Reichenbach’s attempt to define the direction of time by open versus closed “conjunctive forks” but the author fails to note that closed forks become open when common causes are conditioned on.  One question asks students to describe a graphical causal model with a specific probability feature, which would have been straightforward if the reader had been given an illustration of how graphical causal models are parameterized to yield probability relations, but that did not happen.

c.      As an example of uncertain extensions of familiar cases, students are referred to transfinite arithmetic.  Some help.

3.     Some the exposition could be more attractive, notably the explanations of token versus type, singular versus general. Distinctions (never mind notation) from formal logic are suppressed everywhere, even when they would help. The presentation of determinism is unclear and inadequate.

4.     Metaphysical discussions of causality inevitably make claims about what people would say without any consideration of what people do say. The extensive psychological literature on causal judgement, some of which has interesting theories, is entirely ignored.

5.     And sometimes the author says exactly the opposite of what he means—slip of the keyboard?

Ok, nothing is perfect, there could be better textbooks, but this one is usable, which is to say, given the alternatives, outstanding.

Recent Books on Causation, from the Really, Horribly Bad to the So-So to the Pretty Good

There is a bunch of books on causation recently. I expect to review them all here in due time. At least one is so bad that it does not deserve reviewing, let alone having been published, but at least there should be a warning somewhere. So here.

 

I. The Worst: Stephen Mumford and Rani Lill Anjum, Causation, A Very Short Introduction, Oxford, 2013

  Causation is meant to be a quick introductory text surveying contemporary and historical views of causation. For an astute reader, it would be very quick, stopping at, say, page 12. Should in misplaced charity that reader venture on, she would find chapters badly organized, missing their targets (e.g, "finding causes" is reduced to an uninformative mention of randomized, controlled trials), historically uninformed, and terribly referenced. But, as I say, any reader on cortical alert would throw the book away around page 12. There, the authors address Russell's early argument that causes cannot be fundamental because causes are asymmetrical and the fundamental laws of physics are symmetrical equations.

Russell is wrong they say, because "equations have at least some directionality." Here is their argument:

"We say that 2 + 2 = 4, for instance, which is to say that each side is of equal sum. But is is less obvious that 4 = 2 + 2 insofar as 4 can also be the sum of 1 + 3. The point is that 2 +2 can equal only one sum 4, whereas 4 can be the sum of several combinations (2 and 2,  1 and 3, 10 minus 6, and so on). And in this respect there is at least some asymmetry." (pp 12-13)

Somewhere, in Norway or Nottingham, the transitivity of equality, and Russell's point, was missed. 

Then, in nice condescension, the authors write that 

"Second, Russell's account was based on his understanding of the physics of 1913. There have been a number of attempts by physicists to put asymmetry back into physical theory. One such notion is entropy, which an irreversible thermodynamic property."

The  last clause of the last sentence is a bit of nonsense, --it's not the property that is irreversible, it's changes in it, but more importantly the idea of entropy, and the word, had been in physics for about 50 years when Russell wrote.   In 1913, Russell didn't understand the physics of 1913, and neither, apparently, did the authors in 2013.

The ;Nonsense of "The Stone"

The New York Times occasional philosophy column, The Stone, has built a reputation for unilluminating heat, slovenly inference and wanton accusations.  Almost any column would do as an example. I will take a recent reflexive example, “When Philosophy Lost its Way” in the January 11, 2016 Times.

First, what way did philosophy lose?  The high moral ground, for one thing, say the Texan authors. Philosophers of yesteryear (before the 19^th century) showed integrity and selflessness. Our contemporaries by and large do not.  The study of philosophy, in yesteryear, elevated those who pursued it.  Of old, philosophers were concerned with human functions and purposes. Now they are not. Philosophy was a quasi-priesthood, a vocation. Now it’s just a job. Philosophy of old was spread among the professions, the idle rich, etc. Now it’s confined to philosophy professors.

Second, how did philosophy lose its way?  It became part of the university.  That removed philosophers from “modern life.” (I wonder where the philosophy professors live who don’t: pay taxes, have illnesses, worry for their children, hold political views, fall in and out of love, get divorced, give to charities, etc. Maybe it’s North Texas.)  In the good old days, lots of people with different interests were philosophers, but after the 19^th century they all became academics. lost their virtue and their connection with human concerns.  That’s the story.

Unlike the Texas philosophers, I am loathe to defame the integrity or selflessness of contemporary philosophers. I have met a few really vile ones, but mostly they have seemed pretty ordinary folk on moral dimensions.  But I am not so sure that philosophers of old were selfless and notably different in integrity from their contemporaries. It reads to me as if the Texans have been taking The Apology as the common standard of philosophers before philosophers became professors.  Was Aristotle, who left a contentious democracy to educate the mad son of a monarch, selfless?  Was Plato, the Athenian aristocrat, selfless?  Moving up, what was selfless about Leibniz—did he sacrifice himself in some way for others?  Few characters in intellectual history seem less selfless or charitable than Hobbes and Newton, who saw personally to the mutilation of coin clippers. Integrity (and courage)? You won’t find it uncompromised in Locke, who contributed (albeit on tolerance) to the Fundamental  Constitution of Carolina,  an oligarchy ruling over indentured servants that violated both letter and spirit of Locke’s 2^nd treatise—which treatise Locke made sure not to publish while he lived.

There are lots of examples of 20^th century philosophers who acted with selflessness and integrity.  Bertrand Russell, who went to prison over his opposition to World War I; David Malament, who did the same over his opposition to the Vietnam War; Paul Oppenheim and Carl Hempel, who helped Jews out of Germany during the Third Reich; Albert Camus, who was part of the French underground. Philosophers not engaged with modern life? Read Philip Kitcher, read Daniel Dennett’s more recent works, read just about anything by Peter Singer. Are there no 20^th century philosophers who were not professors? Alan Turing was one of the most influential philosophical writers of the 20^th century—among other things of course. He held an academic position only in the last years of his life.  Camus was a journalist. Paul Oppenheim was a businessman. John von Neumann, who stimulated both the philosophy of quantum theory and computation, was a mathematician.  Russell spent most of his career outside of the academy. Lawrence Krauss, a physicist, is a metaphysician as well. 

What is true is that as universities spread and secularized, a lot more people became “philosophers” and a lot of them are very ordinary people with ordinary minds. The same is true of lots of disciplines I expect, say physics.

What is the author’s remedy? Simple: philosophers should get out of universities. The authors teach at the University of North Texas.

Causal Decision Theory and Conditioning: a Primer

Standard Savage decision theory as well as Richard Jeffrey’s alternative, address a normative problem for an odd doxastic condition.  an agent fully believes:

·      a set of all of the available, mutually exclusive actions;

·      a set of exhaustive and mutually exclusive possible states of the world;

·      a set of consequences—outcomes—of each possible state of the world/action pair.

and the agent:

·      Has coherent degrees of belief in the possible states of the world;

·      Has utilities (or in Jeffrey’s version, desirabiities) for the outcomes.

The normative question is which action the agent ought to take. The answer offered is the action, or one of them, that maximizes the expected utility, where the expectation is with respect to the degrees of belief in the states of the world.

From an ideal Bayesian perspective, what is essential is the distinction between actions and outcomes and their costs or values.  The ideal Bayesian knows which actions have the maximal expected utility. The states of the world are gratuitous.  Followers of Savage, or Jeffrey’s in effect assume the agent only obtains the expected utilities by calculating them using the specified states of the world and probabilities of outcomes, given the various possible states of the world and actions.

What is odd is that no epistemological problem is considered about how an agent knows, or could know, or rationally assess, the possible states of the world and their probabilities, the possible actions, or the probabilities of outcomes effected by alternative actions in the several possible states of the world.  a thorough subjectivist such as Jeffrey would answer these questions: all that is relevant are the agent’s degrees of belief about actions, states of the world,and outcomes and their desirabilities.  Epistemology reduces to observing, Bayesian updating, and rather trivial computation. Be that as it may, or may not, causal decision theory considers two kinds of complications.

1.     The agent believes that the action chosen will influence the state of the world.

2.     The agent believes that the state of the world will influence the action chosen;

This is already a conceptual expansion for the agent, to include causal relations and probabilities of actions.

In case 1, how should the agent take account of the belief that the choice of action will be influenced by the state of the world?  For simplicity, first assume the outcome is a deterministic function of the action, a, and the state, s, of the world, and the utility is U(o(a, s) where o is some function actions and states.

Proposal 1:  Calculate the expected utility for each action as the sum over states of the world of the utility of each action in that state of the world multiplied by the probability of that state of the world given the action:

(1) Exp(U(a))  = Σs U(o(a,s)) Prob(s | a)

In Savage theory the last factor on the right hand side of (1) and (2) is just Prob(s)

One “partition question” concerns whether the action that maximizes utility is the same depending on how the set of states is “partitioned.” Let S be a variable that ranges over some finite set of values, s1,…,sn.  a coarsening of S is a set S1 = {{s1 v..v sk}, {sk +1 v …v sm},….{sm v…v sn}}, etc. a refinement is the inverse.

Coarsening can change the probability of an outcome on an action. Let S = {s1, s2, s3} and suppose S’ is a coarsening of S to {(s1 v s2), s3}. For all outcomes o and actions a, let o and a be independent conditional on s1 and likewise on s2 and s3, but S not be independent of A.  Then for any outcome in O:

P(O | a, (s1 v s2)) = P(O, | (a,s1 v a,s2) = P (O, a, (s1 v s2)) / (P(a,s1 v a,s2))  =

P((O, a, s1) v  P(O, a, s2)) / (P(a,s1 v a,s2)) =

P(O, a, s1) + P(O, a, s2) / ((P(a,s1) +P( a,s2)) =

[P(O | a, s1) P(a, s1) + P(O | a, s2)] / ((P(a,s1) +P( a,s2)) =

[P(O | s1) P(a, s1) + P(O | s2) P(a, s2)] / ((P(a,s1) +P( a,s2)) =

(P(a) [P(O | s1) P(s1 | a) + P(O | s2) P(s2 | a)]) / (P(a)( (P(s1 | a) +P(s2) | a)) =

[P(O | s1) P(s1 | a) + P(O | s2) P(s2 | a)] / (P(s1 | a) + P(s2) | a))

The probability distribution of 0 given the state s1 v s2 in S’ varies as the conditional probabilities of s1 and, respectively, of s2 vary with the value of A they are conditioned on, and O and A are not independent in S’ but they are independent—by assumption—in S.  

For case 2, the results and the argument are similar.  The general point is an old one, Yule’s (on the mixture of records).

The partitioning problem does not apply to Savage’s theory—it makes no difference how the range of possible state values are cut up into new coarsened variables.  

So decision theory when the actions influence the states or the states influence the actions is up in the air—the right decision depends on the right way to characterize the states.  Various writers, Lewis, Skyrms, Woodruff and others, have proposed vague or ad hoc or infeasible solutions. Lewis proposed to chose the most specific “causally relevant” partition, which I take to mean the finest partition for which there is a difference  in elements of the partition in the probabilities of outcomes conditional on actions. Skyrms objects that this is often unknowable, and proposes an intricate set of alternative conditions, which Woodruff generalizes. The general strategy is to embed the problem in a logical theory of conditonals, and entwine it with accounts of “chance”and relations of chance and degrees of belief, e.g., the principal principle. The general point is hard to extract.

When states influence actions Meek and Glymour propose that there are two theories. One simply calculates the expected values of the outcomes on various actions as with Jeffrey’s decision theory, the other assumes that a decisive act is done with freedom of the will, represented as an exogenous variable, that breaks the influence of the state on the act.  

Appealing as the second story may be to our convictions about our own acts as we do them, or deliberate on what to do, it is of no avail when the actions influence the states, not vice-versa. For that case, one either knows the total effect of an action on the outcome, or one doesn’t, and if one doesn't, there is nothing for it except to know what the states are that make a difference.  One would think serious philosophy would have focused then on means to acquire such knowledge. One would be wrong.