Monday, August 25, 2014

Review of Philosophy of Science, 81, July, 2014





This issue of Philosophy of Science contains some good, some bad, some odd. It gives evidence that methodology in philosophy of science is pretty much in the doldrums or worse, while good work is being done producing economic models for various ends.


Reject.

This is a very brief rehash of some history of probability, coupled with some remarks on ergodic probabilities, remarks that go nowhere. The piece seems oddly  trivial and unworthy of its distinguished author.  One has to wonder why it was published—or submitted.   Hypothesis: The author is eminent and a colleague of the editors. That sort of thing has happened before in Philosophy of Science, although not that I can think of under the current editors.  But one of the things colleagues should do for one another is discourage the publication of stuff that is trivial or bad in other ways. 

Ben Jantzen,


Accept.

Likelihood has an apparent problem. Suppose you are weighing hypotheses h1 and h2. You know b. You learn e. Should you compare h1 and h2 by

p(e | h1, b) / p(e | h2, b)  or by p(e, b | h1) / p(e, b | h2)?

Which hypothesis is preferred may not always be the same on the two comparisons. Jantzen makes the sensible suggestion that which to use depends on whether you are asking about the extra support e gives to h1 versus h2 in a context in which b is known, or whether you are asking about the total support.  Jantzen’s point is not subtle, but the paper is well done and the examples (especially about fishing with nets with holes too large) are illuminating.

Which reminds me of a deeper problem with likelihood ideas that seem not to be much explored: likelihood doctrine seems to imply instrumentalism. 

Likelihood arguments are used not just to compare hypotheses but to endorse hypotheses, e.g., via maximum likelihood inference.  Consider two principles:

1.      Hypotheses addressing a body of data should be preferred according to the likelihood they give to that data.
2.      A hypothesis should not be endorsed if it is known that there are other hypotheses that are preferred or indifferent to it by criterion 1 above, especially not if there is a method to find such alternatives .

If the data is finite, the hypothesis just stating the evidence has maximum likelihood.  So some additional principle is required if likelihood methodology is to yield anything more than data reports.  The hypothesis space must somehow be restricted.

Try this:

3.      Only hypotheses that make predictions beyond the data are to be
considered.

So suppose there are data e1…en and consider some new experiment or observation e not in the data but for which “serious” hypotheses explaining e1…en gives some probability to the outcomes. Let the outcomes be binary for simplicity and so h gives the probability to be is P(e | h).  Consider the hypotheses:

e1&…&en & argmax<h,> (P(e | h) if argmax<h,> (P(e | h) > argmax<h,> (P(~e | h) ,and e1&…&en & argmax<h,> (P(~e | h) otherwise

This hypothesis meets condition 3 and gives e (or ~e) a likelihood at least as great as any alternative hypothesis.

Ok, try this:

4. Only hypotheses that make an infinity of predictions are to be considered.

But the stupid pet trick above can be done infinitely many times. So try this

5. The hypotheses must be finitely axiomatizable.

 Still won’t do, as (I think) an easy adaptation of) the proof in http://www.jstor.org/stable/41427286 shows.


Lina Jansson


Reject

Both the thesis and the argument of this paper are either opaque or weird; it is difficult to see the warrant for publishing.  Her stalking horses are “causal accounts of explanation.”  On Streven’s account, causal asymmetry is why X explains Y rather than the other way round—Dan Hausman had that idea earlier; on Woodward’s account, X causes Y but Y does not cause X implies that a manipulation of X changes a manipulation of Y, but not vice versa.  So far as I know, neither of them claim that all explanations are causal explanations. But a lot of them are.

Jansson’s argument seems to be as follows:

Leibniz held that Newton’s gravitational theory was not a causal explanation, because causal explanations require mechanisms and no mechanism was given for gravitational attraction. She reads Newton as “causally agnostic” about his laws, which seems to me a very long reach. He was agnostic (publicly) about the mechanisms that produce the laws, but not that the laws imply causal regularities: drop a ball and that will, ceteris paribus, cause it to take up a sequence of positions at times in accordance with the law of gravity.  But suppose, for argument, she is right, then what is the argument?

She writes: “Put simply, the problem of understanding this debate from a causal explanatory perspective stems from the reluctance, on both sides, to take there to be a straightforward causal explanation given by the theory.”  And, a sine qua non of a correct account of explanation is that it be able to “understand the debate. “ 

There is this oddity about universal gravitation and causation. If I drop a ball it causes the ball to fall, the ball’s falling influences the motion of Mars (instantaneously on Newton’s theory), and the change in the motion of Mars influences the course of the ball, also instantaneously. Immediate feedback loop. But Mars influence doesn’t determine the position of the ball after I drop it, and the position of the ball after I drop it doesn’t cause my dropping it.

Anyway, her point is different. Here is the form of the argument. 

Accounts S and W say Newtonian gravitational theory is causal.
Neither the creator of the theory nor its most prominent critic unequivocally said it was causal.

Therefore accounts S and W are false (or inadequate, or something).

Parallels.

A: Chemical changes involve the combination or releases of substances made up of elements.

Lavoisier said combustion involves combination with oxygen.
Priestley said combustion involves the release of phlogiston

Therefore A is false.

The theory of probability specifies measures satisfying Kolmogoroff’s axioms.

Bayesians say probability is opinion.
Frequentists say probability is frequency

Therefore the theory of probability is false.

Jansson’s “methodology” assumes that concepts of causation and explanation never change, and that historical figures are always articulate, and never make errors of judgement in the application of a concept, and that if some historical figure would only apply a concept under restrictive circumstances (e.g., no action at a distance), an account of the concept must agree with that judgement or posit a new concept.  Individuation of concepts is a vague and arbitrary matter—are there the concept of causality, Leibniz’s concept of causality, Newton’s concept of causality, etc.?  On her view, so far as I can see, for every sentence about causal relations, general or specific, about which some scientists sometime have disagreed, two new concepts will be needed.  Not much to be learned from that.

Robert Batterman and Colin Rice
Revise and resubmit
Another essay on explanation (will philosophers of science ever let up on this) whose exact point is difficult to identify.
"We have argued that there is a class of explanatory models that are explanatory for reasons that have largely been ignored in the literature. These reasons involve telling a story that is focused on demonstrating why details do not matter. Unlike mechanist, causal, or difference-making accounts, this story does not require minimally accurate mirroring of model and target system.
We call these explanations minimal model explanations and have given a detailed account of two examples from physics and biology. Indeed, minimal model explanations are likely common in many scientific disciplines, given that we are often interested in explaining macroscale patterns that range over extremely diverse systems. In such instances, a minimal model explanation will often provide the deeper understanding we are after. Furthermore, the account provided here shows us why scientists are able to use models that are only caricatures to explain the behavior of real systems."

The idea seems to be that there are theories that find features and relations among them that entail phenomenological regularities, no matter the rest of the features of a system, and no matter whether the features in question are exactly exemplified in a system.  There are two examples, one from fluid dynamics, the other Fisher’s opaque explanation of the 1:1 sex ratio in many species based on the equal effort required to raise males or female offspring, but the differential average reproductive return to raising males if females are in excess or raising females if males are in excess.  I don’t understand the fluid dynamics model, and Fisher’s requires a lot of extra assumptions and ceteris paribus clauses to go through, (grant the equal cost of rearing male and female offspring but imagine that one male can fertilize many females and there is a predator that prefers males exclusively) but never mind.

What I don’t understand about this paper is why most theories in the physical sciences don’t satisfy B and C’s criteria for a minimal model. Thermodynamics? The details of the molecular constitution of a system are largely ignored. Relativity? It doesn’t matter whether the system is made of wood or iron, the Lorentz tranformations still hold; it doesn’t matter how the light is generated, its velocity is still the same. Newtonian celestial mechanics? Doesn’t matter that Jupiter is made of gas, Mercury of rock, and Pluto of ice, still the same planetary motions. Even theories that probe into the internal structure of a system are minimal with respect to some other theories. Dalton appealed only to masses of elemental particles—that, and a few assumptions yields the law of definite proportions. Berzelius added electrical forces between atoms, which were gratuitous for deriving definite proportions.

What is not clear in this paper is how B & C intend to distinguish between minimal models and almost every theory that shows a set of features, individual or aggregate, or approximations to such features, and related laws, of a kind of system suffice for phenomenological relations. That is what physical theories generally do. Their fluid flow example almost suggests that all that is required is an algorithm that generates the phenomena from (perhaps) measurable features a system.  So, considering that example, the authors might have asked: when is an algorithm for generating the phenomena an explanation of the phenomena? They did not.

Dean Peters


Revise and resubmit

Peters’ essay is useful in two respects. First, it treats the question in the title as turning on this: what parts of the data confirm what parts of a theory?  That adds a little structure to the philosophical discussions of realism. And, second, it provides a succinct critical review of bad proposals to answer the question. Peters’ has his own answer, which is not obviously useful. Here it is:

“So, to pick out the essential elements of the theory under the ESSA, start with a subtheory consisting of statements of its most basic confirmed empirical consequences or perhaps its confirmed phenomenological laws. These, after all, are the parts of a theory that even empiricists agree we should be “realists” about. Further propositions are added to this subtheory by a recursive procedure. Consider any theoretical posit not in the subtheory. If it entails more propositions in the subtheory than are required to construct it, tag it as confirmed under the unification criterion, and so add it to the subtheory. Otherwise, leave it out. When there are no more theoretical posits to consider in this way, the subtheory contains the essential elements of the original theory.”

 The proposal as developed is insubstantial: “Consider any theoretical posit not in the subtheory. If it entails more propositions in the subtheory than are required to construct it” – what does “required to construct it” mean? 

In criticizing other proposals, Peters appeals to logical consequences, and proceeds with a distinguished set of “posits”—i.e., axioms.  Hold him to the same standard. Theories can be axiomatized in an infinity of ways. We need an account of the invariance of the result of the procedure—whatever it is—over different axiomatizations, or an account of “natural axiomatizations” and warrant for using them exclusively. The work of Ken Gemes and Gerhard Schurz is relevant here.  So it seems to me that Peters has an idea—conceivably ultimately a good idea—that he did not do the work to make good on.
 
Roger DeLanghe


Accept

This is a very nice essay providing a simple economic model in which there are balancing incentives for scientists to adopt and contribute to an existing theory or to propose a new one.  Lots that might be done to expand the picture for more realism, and it would be nice if those pursuing Kitcher’s original idea assembled some relevant data. 

Marius Stan

Unity for Kant’s Natural Philosophy

I have no opinion about this essay, which is on how Kant might have sought, although he did not, synthetic a priori grounds for Euler’s torque law. Nor do I see why anyone should care. Clearly, some do.

Carlos Santana

Accept

This well argued and lucid essay shows that there is a model in which agents with ambiguous signaling (under replicator dynamics) invade a population of unambiguous signalers, but not vice-versa. Despite the considerable empirical evidence the author (a graduate student at Penn) gives for the insufficiency of other explanations of the frequency of ambiguity in human and animal communication, I am worried by the following thought. The evolution of language—or at least signaling-- we expect to have gone from the very ambiguous to the more precise. That is what syntactic structure and an expanded lexicon afford. So if signaling by ambiguous strategies cannot be invaded by signaling by “standard” (i.e., perfectly precise) strategies, how did more precise, if still ambiguous in some respects, signaling systems evolve?  It strikes me that the author may have proved the wrong result.



Saturday, August 16, 2014

The Fortress of Metaethics: Reviews of Thomas Scanlon, What We Owe to Each Other and Being Realistic about Reasons.




Metaethics is about what ethical claims mean, how they can be “justified,” and how ethical reasoning ought to be conducted.  Thomas Scanlon’s writing on metaethics has become a verbal icon for the enterprise. Scanlon now has two books elaborating his views, What We Owe to Each Other and Being Realistic about Reasons.  The first was reviewed with applause in literary venues where philosophy is seldom seen, and one can only expect the same of the second. Each book is a theoretical disappointment—no, the second is a disaster--the first from lacunae the second tries to fill, the second from the filling.[1]

In What We Owe to Each Other Scanlon’s stalking horse is utilitarianism. The many variants of utilitarianism share this much: they are voting theories, and so is Scanlon’s alternative, absent some key features. In utilitarianism, every sentient creature, or at least every human, has a stock of interests. Properly scaled, those are voting stocks. Anyone’s action predictably affects some of the interests, or the well-being, of some creatures. An action is permissible only if, among the alternative available actions, it maximizes some aggregate of the interests of all who may be affected by any of the available actions, so far as the actor can estimate.  That is the utilitarian schematic for how the affected stocks are to be weighed in moral assessment of action.  The specifics are contentious. How are pains and pleasures and sorrows and joys to be compared across persons, let alone persons and other animals, so that they can be aggregated?  That issue aside, suppose we have a number for each human state or well or mal being that takes account the diverse interests of each human being. Should one try to maximize the total, the average, the median well-being over all persons? Minimize the variance? Maximize something under a constraint (e.g., a bound on the variance, or the Difference Principle)? Count only changes to an individual’s interests that are above a certain threshold?  Order interests by type, higher type trumping lower, as one might read Mill to suggest? The utilitarian literature from Bentham on has this virtue: it takes these questions seriously and offers answers, not the same answers, of course. These are philosophers after all.

Scanlon’s theory is one piece of a different voting theory.  For any action one might do, the deliberator and others may have reasons, conscious or not, why it should or should not be done. The best of those reasons is decisive. Reasons are not to be aggregated; the best reason wins, no matter how few people have it. Which reasons count? Scanlon offers only this in general: We should seek to act only in accord with principles that other people could not reasonably reject if they too sought principles others could not reasonably reject.  A reason has moral bearing only if it is an application of such a principle.

One catch to Scanlon’s general schema for moral principles is “reasonably,” which in this context is particularly flabby. We have pretty clear notions of reasonable views in mathematics, less definite notions in science, but in ethics “unreasonable” is more a slur than a methodological complaint. Does Scanlon imagine a negotiation about which principles meet his criteria, or a social survey to find nearly universal principles (they would be few), or does he imagine principles that someone sincerely thinks others ought to share? In the latter case, utilitarian principles have a vote. No one thinks that the only reasons I can have for or against an action must be exclusively about me. Indeed, if by the proper weighting of principles and reasons utilitarian principles and reasons are the best, then Scanlon is committed to utilitarianism, one step back.

So what then are the principles of ordering of reasons or principles, and why? Scanlon does not say, only, examples aside, that the best reason wins, winner take all.  What then individuates reasons: if your action will impoverish me and cause me an illness besides, is that one reason or two? Scanlon doesn’t say, but in his voting scheme it matters.  The basic elements of the theory are unspecified: by what clear principles are reasons to be weighed, and why, what counts as a reason, how are reasons individuated? Almost all you might want in a theory is unspecified. One would not want election rules so vaguely posted.

The book has any number of appeals to quotidian examples where one would not consider global consequences, or global good, or aggregate harms and benefits. There are old saws: If a broadcasting engineer is painfully and continuously injured by continuing shock during the broadcast of a sports game—say Argentina versus Germany in the World Cup--and the only way to stop his agony is to interrupt the electric current that is necessary to broadcast the game, shouldn’t that be done—aren’t the enormous sum of annoyances to the passions of millions of soccer fans outweighed by the one engineer’s acute pain?  But what would be said in this kind of case by versions of utilitarianism in which what counts has thresholds, or versions in which there are layers of goods and bads that trump others? Should we not consider the number of people who might be killed in mad rages and riots were the television to go off in the midst of the game? In any case these examples can be bought cheap by either side. Being murdered is worse than not having children. If you met a person with a remarkably infectious, uncurable disease that renders all who catch it permanently sterile but is otherwise asymptomatic, and you could not capture him and isolate him before he spread it to the entire human population, would you kill him if you could?

If the aim is to articulate standards for correct norms, why trifle with mundane examples, unless one is doing moral sociology from an armchair? That question takes us to Scanlon’s more recent book, a defense of putting weight on such examples, and, more broadly, a defense of metaethics as a serious enterprise.  Scanlon does not fill all the gaps his first book left, but he addresses two major ones. The claims of Being Realistic about Reasons come down to these: there are true normative principles that are not just about the best means to ends, and there is a method for discovering them.  What is the argument?

Scanlon claims that there are various “domains” of inquiry. Each domain has its own standards for seeking the truth in its domain. Mathematics has its methods, empirical science has its methods, and, lo, normative matters, moral matters in particular, have theirs. One domain may not contradict, or, presumably, undermine, the methods and conclusions of another.  They are separate empires, contractually at peace. This last I call Scanlon’s Rule. He continues with implausible parallels between set theory (Scanlon was a logician in his youth) and normative reasoning.  Just as set theorists may debate and disagree about, say, Zorn’s Lemma, so metaethicists may debate and disagree fine points of the correct normative principles. Can one seriously think that the reasoning in ethics and metaethics has the rigor of mathematics? I can’t, and I doubt Scanlon does. Scanlon’s thesis is that they share the same style, the same form viewed with sufficient abstraction. So, with sufficient abstraction, do science and Cargo Cults.  The intellectual legitimacy of metaethics needs a better bolster.

The crucial point is Scanlon’s Rule. Scanlon’s Rule is pure defense, a paper wall to keep out critics. Mathematics and logic may be immune to contradiction from physics (although Hilary Putnam once thought otherwise, and presumably Mill would have allowed the possibility, and certainly the status of geometry has been altered by physics—and the status of metaethics is what is at stake here), but ethics is not immune to contradiction from other “domains.” Is religion a domain? Theological reasoning is more like metaethics than is set theory, and theology most definitely intrudes on ethics and on metaethics. Empirical science may not directly contradict normative claims, but it can surely undermine them. Once upon a time it was widely thought that there are particularly evil people, sorcerers and witches, who had made contracts with the most evil entity, Satan, and should be killed. Science has convinced the civilized that there are no witches and no sorcerers and no Satan. Once upon a time, it was thought that living beings have a superphysical constitution, that their chemicals are not the ordinary, “inorganic” stuff, and that living beings possess an unphysical “vital force” that guides evolution. Science has convinced us (Tom Nagel perhaps aside) otherwise. Science bids fair to do the same with the Will, and Autonomy, and Agency, and as, and if that more fully comes about, the idea of true, moral principles will go the way of true principles of witchcraft.

So what about the methods of ethics? Scanlon’s is “reflective equilibrium,” I think first proposed in Rawl’s essay “Outline of a decision procedure for ethics.”  Rawls imagined a panel of moral experts (much of his essay is about the qualifications for membership) who report on the moral statuses of sundry actions. The ethical theorist takes their pronouncements as data—putative moral facts—and attempts to form a general theory that accounts for them. Rawls allowed that on reflection one might reject a few of the experts’ decisions if accounting for them required excessive complexity in the theory, arbitrary exceptions and so on. The procedure came to be called “reflective equilibrium.”  That is Scanlon’s method, with the panel of experts replaced by one’s own judgements and the judgements of those whose ethical perspicuity one respects. His explanation of the reliability of its data sounds very much like Descartes “clear and distinct ideas”:

“In order for something to count as a considered judgment… It is necessary also that it should be something that seems to me to be clearly true when I am thinking about the matter under good conditions for arriving at judgments of the kind in question.”  Scanlon, T. M. (2014-01-06). Being Realistic about Reasons (p. 82). Oxford University Press, USA. Kindle Edition.   (Italics are Scanlon’s)

I have no doubt that some very thoughtful people, no doubt Scanlon himself, form their moral views in this way. I even think it’s a good way. But I have no doubt, either, that in many other “domains” something similar is often followed. It is general and vague enough to characterize both the process of Islamic jurisprudence and the quasi Bayesian process often at work in science in which data are thought to come with probabilities of error and the sufficiently low posterior of a datum conditional on a hypothesis of sufficiently high probability is reason to reject the datum, or even to reject an entire set of measurements. But these examples are exactly the problem.  In Bayesian statistics one can prove that under specified, general assumptions, application of Bayes rule converges to the truth. One can do the same for modifications, perhaps even considered variants of the one I suggest off-hand above. In statistical estimation and machine learning (the latter of which Rawls, in keeping with the opinion of his time, announced was impossible) proofs are given that under very general assumptions search methods converge on the truth, and methods are provided for testing the assumptions. Nothing like that can be done for Islamic jurisprudence, and nothing like that can be done for Rawl’s decision procedure for ethics or Scanlon’s variant. That one can apply a vaguely specified procedure in a domain is no argument, no evidence, that the procedure finds the truth in that domain, or that there is any truth there to be found.  

The least attention to the world shows that the range of considered moral judgements is incompatible with any unified theory of morality.  Scanlon will have to discard many of the moral judgements of most people in the world. He should, but he should not claim that in doing so he is exercising a method for finding truth. Scanlon has only two responses. Those who want to (and do) crucify Christians and behead Jewish journalists and do other atrocities are not in “good conditions” for such judgements;  and that ethics and metaethics have their own standards for concluding what is true--outside standards and alien practices, however common, are irrelevant. 

There is plenty of work for metaethics to do: systematizing vague strategies of inference—Nozick’s efforts were a good start[i]--finding and recognizing contradictions, figuring out how principles apply in morally difficult cases, contrasting misweighings of moral importance, finding agreements and disagreements in clarified moral perspectives, tempering ethical demands to human capacities, and so on, all without Scanlon’s truth claims. Scanlon’s redoubt is a parochial fortress, impenetrable to the forces of science or to the objections of the world outside and its domains.




[1] I write this and what follows with some regret, since Scanlon was my closest friend when we were colleagues. This blog may lose me a lot of friends.


[i] Nozick, Robert, "Moral Complications and Moral Structures" (1968). Natural Law Forum. Paper 137.
http://scholarship.law.nd.edu/nd_naturallaw_forum/137

Monday, August 11, 2014

Low Bars: Reviews of Four Semi-Recent Books in Philosophy of Science






I take a dyspeptic look at four recent books, one of which, Kyle Stanford’s Exceeding Our Grasp, has previously been reviewed with praise in several places.  And now, a second, Paul Churchland’s Plato’s Camera, reviewed with praise in Mind and Machines.

Paul  Churchland, Plato’s Camera, MIT Press, 2012


As his title indicates, Paul Churchland is a man of big metaphors. He is a man of big ambitions as well, not for himself but for his theory. He thinks that that neuroscience will provide—and is well on the way to providing --a complete logic and philosophy of science. Academic philosophers have missed the boat, or the bandwagon, whichever metaphor you prefer. Neuroscience provides “a competing conception of cognitive activity, an alternative to the “sentential” or “propositional attitude” model that has dominated philosophy for the past 2,500 years.” (14) “these spaces [of synaptic weights and patterns of neural activation] specify a set of ‘nomically possible worlds…these spaces hold the key to a novel account of both the semantics and the epistemology of modal statements, and of counterfactual and subjective conditionals.” (18). “Notably, and despite its primacy, that synapse-adjusting space-shaping process is almost wholly ignored by the traditions of academic epistemology, even into these early years of our third millennium.” (13)


A little potted history will put Churchland’s book in context. The great philosophers joined theories of mind with theories of method for acquiring true beliefs.  For Leibniz and Hobbes and even Hume, logic was the algebra by which the mind constructs complex concepts, or ideas, from simpler ones. George Boole realized that whatever the laws of thought may be, they are not in necessary agreement with the laws of logic. People make errors, and some people make them systematically. Logic, semantics, causality, probability have their relations, the mind has its relations, and the twain shall sometimes, but not always, meet.

Sparked by Ramon y Cahal’s discovery of the axon-dendrite structure of neural connections, suggesting that the nerve cell is an information processing unit and the synaptic connection is a channel, in the last quarter of the 19th century avante-garde speculation turned to how the distribution of “excitation” and its transfer among cells might produce consciousness, thought and emotion. Connectionist neuropsychology was born in the writings of Cahal, Sigmund Exner and, yes, Sigmund Freud.  Exner, like Freud, was as an assistant to the materialist physiologist Ernst von Brucke, and Freud’s neuropsychological speculations from1895 elaborate (one might say exaggerate) lines suggested in Exner’s 1891 Entwurf zu einer physiologischen Erklärung der psychischen Erscheinungen, both inspired in a general way by Hermann von Helmholtz, with whom Freud once proposed to study.  In Freud’s Entwurf einer Psychologie—still in print in English translation as Project for a Scientific Psychology--the neurons are activated by stimuli from the sense organs, or by chemical sources internal to the body. Neurons pass activation to those they are connected with in the face of some resistance, which is reduced by consecutive passage (an idea now called, with historical injustice, the “Hebb synapse”) and eventually produce a motor response. Depending on the internal and external stimuli that result from motion, a feedback process occurs which eventuates in a semi-stable collection of facilitations among nerve cells that constitute our general knowledge of the world—what Freud called the “reality principle.” The particular neural activations of memory and momentary experience occur within those learned constraints captured by the facilitations. Logic, the subject–predicate logic Freud had learned from Franz Brentano–is at once created (as thought) and realized (as model) by the synaptic connections.

That is pretty much Churchland’s theory. There are modern twists, of course—Cajal and Exner and Freud had no computers with which to do simulations or make analogies, and they had a different data set—and Churchland has all sorts of terminological elaborations. But, other than a review of connectionist computing and some modern neurobiology, and of course a host of new metaphors—“sculpting the space” of activation connections and so on, what is new in Churchland’s book? What he says:  “a novel account of both the semantics and the epistemology of modal statements, and of counterfactual and  subjunctive conditionals” as well as a novel account of synonymy and an explanation of scientific discovery and intertheoretical reduction and more.  In sum, Churchland shares the aim of the Great Philosophers to produce a unified account of mind, meaning and method, but this time founded on the neuroscience of neural processes rather than on Hume’s introspective science of impressions and ideas or Kant’s a priori concepts.

Historians and philosophers of science have written reams about how Darwin came to the view that species formed and evolved by spontaneous variation and natural selection, what knowledge and arguments and hypotheses he had available when he embarked on the voyage of the Beagle, what he was convinced of by what he saw in those passages, what the collections and notes with which he returned taught him, what influences his subsequent reading and conversation and correspondence bore.  Churchland’s explanation of Darwin’s discovery
can be Bowdlerized but not summarized:

“The causal origins of Darvin’s explanatory epiphany resided in the pecular modulations, of his normal perceptual and imaginative processes, induced by the novel contextual information brought to those processes via his descending or recurrent axonal pathways…A purely feed forward network, once its synaptic weights have been fixed, is doomed to respond to the same sensory inputs with unchanging and uniquely appropriate cognitive outputs…A trained network with a recurrent architecture, by contrast, is entirely capable of responding to one and the same sensory input in a variety of very different ways..As those states meander, they provide an ever changing cognitive context into which the same sensory subject-matter, on different occasions, is constrained to arrive. Mostly, those contextual variations make only a small and local difference in the brain’s subsequent processing of that repeated sensory input. But occasionally they can make a large and lasting difference. Once Darwin had seen the now-famous diversity of finch-types specific to the environmentally diverse Galapagos Islands as being historically and causally analogous to the diversity of dog-types specific to the selectionally diverse dog-breeding kennels of Europe, he would never see or think of the overall diversity of biological forms in quite the same way again. And what gave Darwin’s conceptual reinterpretation here the lasting impact that it had on him was precisely the extraordinary explanatory power that it provided…The Platonic camera that was Darwin’s brain had redeployed one of its existing ‘cognitive lenses’ so as to provide a systematically novel mode of conceptualization where issues of biological history were concerned.” (191-200).

 A lot has gone wrong here. How the output (the realization of explanatory power) “sculpts the space” of neural connectivities anew is unexplained. The “recurrent neural network” and “descending axonal pathways” stuff has nothing to do specifically with Darwin. It could as well be said of the epiphanies of Newton or Einstein or the fantasies of Erich van Dalen. When Churchland wants actually to engage Darwin, he has to step out of the neurological generalities and into the actual history, and he has to appeal to a notion, “extraordinary explanatory power” taken from old-fashioned philosophy of science. And that is because he knows nothing specific about what neural processes took place in Darwin, and nothing about what neural processes constitute the realization of explanatory power, or what about the neural processes themselves distinguishes genius from crank from paranoid. He is not to blame for that, but it shows the impotence of his framework for elucidating much of anything about scientific discovery, let alone for providing guidance to it.

It is the same everywhere with Churchland. He is not to be faulted for want of theoretical ambition. Take the question of inter-theoretic reduction. After whipping off criticisms—the quality of which I have not space to pursue--of various accounts, Churchland offers this:

“A more general framework, G, successfully reduces a distinct target framework, T, if and only if the conceptual map G, or some part of it, subsumes the conceptual map T, at least roughly… More specifically
(a) the high-dimensional configuration of prototype-positions and prototype-trajectories with in the sculpted neuronal-activation space that constitutes T (a conceptual map of some abstract feature-domain) is (b) roughly homomorphic with
(c) some substructure or lower-dimensional projection of the high dimensional configuation of prototype-positions and proto-type trajectories within the sculpted neuronal activation space that constitues G (a conceptual map of some more extensive abstract feature-domain.)” (210-211).

Good. Now does statistical mechanics reduce thermodynamics? Does quantum theory reduce classical mechanics? Or what? Consult prototype positions in sculpted neuronal activation space. I will skip the details of Churchland’s account of “homorphisms between sub-structures of configurations of prototype-positions and proto-type trajectories.” Suffice that is an ill-defined attempt at a little mathematics, so odd as perhaps to have been whimsical.

About meaning relations, the general idea seems to be that one thinks counterfactually or hypothetically by activating patterns that are neither sensory responses nor exact reproductions of previous activation patterns—not memories, which, less the ‘activiation patterns’ is precisely Hume’s account. Nothing particular is established, and we are left to wonder what constraints on our meandering activations incline us to think that if, necessarily if p then q, then if necessarily p then necessarily q. What distinguishes the hypothetical from the counterfactual, the entertained from the believed, the supposition from the plan, the wish from the fear from the doubt from the conviction--is unexplained, and it seems doubtful that Churchland can do better than Hume on imagination.

When it comes down to it, Churchland does not want to explain propositional attitudes, he wants to do away with them.  Some reasons are given in his argument against one propositional attitude, the analysis of knowledge as true, justified belief. He notes the usual Gettier problems but that is not what bothers him. We, and infants and animals, have he says, a-linguistic knowledge. Beliefs are attitudes to propositions and truth is a property of sentences, so to attribute them to much of what we know and other animals know is a category mistake. And so, for much of what is known but is not, or cannot, be said, justification is impossible and to ask for it is likewise a kind of category error.

There is something to this, but only a little. There is implicit knowledge, exhibited in capacities, which someone can have and yet have no awareness of, no thought of.  The psychologist evoking the capacity can generally state what her subject implicitly knows. She may even claim to know in a general way how the subject came to know it, and so find it justified and true. Whether such implicit knowledge is a belief of the knower is the hard question. Churchland would I think say not; Freud, who lived on the premise of unconscious beliefs, would have had no trouble allowing it. We have thoughts we never formulate in language—we can think we see a familiar face in a crowd and automatically look again, testing the thought before it takes, even to ourselves, a linguistic form. Evidence of a-linguistic thought is all around anyone who lives with dogs or cats or even a closely watched cow. But I do not see why such thoughts cannot be believed or had with surprise or fear by those entities that have them, why they cannot be the objects of the very attitudes that philosophers call propositional. There is generally a proposition that approximately expresses them even if their possessor cannot formulate it.  However this may be, it remains that our thoughts are not on a par. There is a difference between formulating a plan, an intention, and entertaining a possibility, and Churchland’s framework has no place for it. Perhaps one could be made, but for that one would have to want to allow something very much like propositional attitudes.

On technical points, the book is a mixture. Lots of things are explained vividly and correctly, some not so much.  For example, recurrent networks have a problem with long term memory. A class of algorithms Churchland does not discuss, Long Short Term Memory (S. Hochreiter  and J. Schmidhuber. Long short-term memory. Neural Computation, 9(8):1735–1780, 1997) do better.  He is a bit weak on biology. Churchland dismisses innateness hypotheses on the grounds that genes would have to specify synaptic connections, and there are billions of those and only 30,000 or so genes. He forgets (I know he forgets, because once I told him) that a person’s liver cells and neurons have the same genes but very different forms and functions--cellular form, function and location involve gene expression, and it isn’t just one gene-one expression, one protein, one synaptic connection. The combinatorics are enormous. He writes metaphorically of “sculpting activation space” but fails to note that nerve connections are physically pruned—literally destroyed--from infancy to maturity.  Remarkably, the book entirely ignores the growing neuropsychological research on predicting an agent’s environment from indirect measurements of brain physiology—the very work that comes closest to realizing Churchland’s vision. 

The real problem with Churchland’s book is too long an arm, a lengthy overreach. One can grant the general Cajal-Exner-Freud connectionist framework. It provides a theoretical position from which to do research and that research is prospering. A few professional philosophers have contributed, Stephen Quartz for example with fMRI experiments, and Joseph Ramsey with improvements in fMRI methodology. But decorating the framing assumptions of scientific research in neuroscience with metaphors, accounts of computer simulations, and vacuous applications neither helps with our problems in philosophy of science nor contributes to methods for effectively carrying out that research.


 P. Kyle Stanford, Exceeding Our Grasp, Oxford University Press, 2012

Banality, Nelson Goodman once said, is the price of success in philosophy. Here is a banality: One cannot think of everything, and if a truth is something one cannot think of, then one will not believe that truth. 

That is the fundamental substance of Stanford’s thesis, elaborated with brief discussions of some of the philosophy of science literature on theoretical equivalence, underdetermination, and confirmation, and with a more extended discussion of examples in the history of science. More elaborately, the thesis is that historical scientists did not, and could not, think of the alternatives to their theories that later explained their evidence in different ways; so, too, our contemporaies are unable to think of such alternatives that may lurk in Plato’s heaven. Hence we should not believe our current theories. The conclusion does not follow. Perhaps one ought to believe, of the hypotheses one can conceive and analyze, those best supported by current evidence. The general agnostic will never believe the truth; those who believe on their best evidence and available conceptions at least have a shot. Even so little strategic  reflection is not to be found in Stanford’s essay.

Much of Stanford’s philosophical argument is negative: there are no general characterizations of theoretical equivalence even assuming a definite space of possible data; there are no general theories of what parts of a theory are confirmed by what data.  One could apply his argument reflexively: there may be possible characterizations of such relations that have not been thought of, in which case perhaps we should be agnostic about being agnostic about our theories. I don’t know if agnosticism is transitive. The rest of his argument consists of historical discussions about what various scientists thought that turned out to be wrong, for example what they thought were the indisputable parts of their theories. Here the absence of any normative theory in the book collides with the historical exegesis: why should we think that various historical figures, Maxwell, for example, were right about what they thought were the indubitable, or best confirmed, aspects of their theories?  More than that, Stanford’s histories neglect historical stability. Two centuries later, the atomic weight of oxygen is still greater than the atomic weight of hydrogen.

Logic is also neglected in Stanford’s effort to make novelty out of banality. Stanford’s discussion of Craig’s theorem, for example, is odd. He takes it as establishing that a theory has a perfectly observationally equivalent instrumentalist ghost, and of no further significance for theoretical equivalence. But what the theorem establishes is that if there is a recursively enumerable linguistic characterization of the possible data for a theory, then there is an infinity of theories that entail the same possible data. Under mild assumptions, there is an infinity of finitely axiomatizable, logically inequivalent such theories, and there is no logically weakest finitely presentable theory. 

Some years ago I attended lectures by a prominent philosopher and by the late Allen Newell. The prominent philosopher went on for two lectures to the effect that some features of cognition are “hard wired” and others not. Having enough of this, Newell asked what the philosopher’s laboratory had discovered about which cognitive features are “hard-wired.”  Flustered, the philosopher appealed to “division of labor” between philosophy and psychology. To which Newell observed privately that if that was the philosophers’ labor, psychologists could do it themselves, thank you.  And there is the trouble with Stanford’s book. It is a lazy effort. If there are theories we cannot think of, or have not thought of, in some domain, and surely in many domains there are a great many, by all means help us find ways to survey and assess them. That is what machine learning is about. Stanford has nothing to say. If we need a reliable means to assign credit or blame among the many claims entailed by a theory, seek for one. Stanford has nothing to say. The main thing he has to say you knew before opening his book.

Sandra Mitchell, Unsimple Truths, University of Chicago Press, 2012


Sandara Mitchell’s book is more shadow than smoke. Try to catch some definite, original content is like grasping a shadow, but the shadow is always there, moving with your grasp. Mitchell rightly observes that contemporary science proceeds across different “levels,” that many relations are not additive (she says not “linear”), that many phenomena, especially biological and social phenomena, have multiple causes, and that much of contemporary science is addressed to finding regularities that are contingent, or impermanent, or not general (she doesn’t distinguish these) . One wonders for whom this is news.  No one I know. No doubt she gets around more.

She argues for “emergence” rather than “reduction” and proclaims a “new epistemology”: integrated pluralism. One might hope that this is the definite, original part, but it turns out not to be so.

Epistemology comes in two phases: analyses: “S knows that P” and such; and method: how S can come to know that P, and such.  There is no concrete thought in this book on either score that is helpful, either to philosophy or to science. Modern systems biology and neuropsychology have lots of problems about “high dimensional, low-sample size” data. She has nothing to offer. Social epidemiology has a hoard of problems about measurement, sampling and statistical inference. She has nothing to offer. Cancer has complex interactive causes hard to establish, and so do lots of social and cognitive phenomena. She observes that there are problems, but has nothing helpful to offer.

Mitchell’s  discussion of emergence and reduction is a bit bewildering. On the one hand, she allows that no one seriously thinks we are actually going to deduce social patterns from facts about fundamental particles—and if some should try, let them go to it but don’t pay them. So there is no methodological issue, only a metaphysical one.  On the other hand, she does not dispute that, at the basis of nature, it’s physics. She isn’t arguing for any transcendent powers. So what’s left? Apparently only this: one language can’t express everything, so no language for physics can express everything. Something will be left out. She offers no candidates for the omitted, but suppose she were right. Suppose for any physical theory there are aspects of the physical world that theory does not capture—not even logically, let alone practically. Proving, rather than merely asserting, as much would be an impressive achievement merely as a theoretical exercise, but what’s the point for “integrative pluralism”? I see no implication whatever for the conduct of science. Whether we think there is a theory of everything is possible or not, the scientific community will still measure the large and the small, try to separate phenomena into multiple aspects, look for mechanisms and try to separate their components, suffer with interaction, with the limits of predictability, computational complexity and the rest. Makes no difference to any of it whether the language of physics is finally complete or finally completable.

To judge from the blurb on the book jacket, scientists may like reading this stuff, but if so that can only be because it is an aid to their vanity, not to their science.

Bill Harper, Isaac Newton’s Scientific Method, Oxford University Press, 2012.


Much of this book is about another, Books I and III of the Principia. Harper details, almost lovingly, the theorems from Book I and how they are used in the argument for universal gravitation in Book III, and on that account the book is worth reading—with a copy of the Principia to hand.  But the question of  Harper’s book is : What was Newton’s method? It was more than theorems.

Any reader of the first pages of Book III should get the general idea of Newton’s argument. Starting with Kepler’s laws and using theorems of Book I that are consequences of the three laws of motion, Newton proves that for each primary in the solar system with a satellite, there exists an inverse square force attracting the satellite to its primary. He then shows that the motion of the moon can be approximately accounted for the combination of two such forces, one directed to the sun and one directed to the Earth. He then engages in a hypothetical, or suppositional exercise, counting the acceleration the moon would have at the surface of the Earth. Using experiments with pendulums, he shows that the acceleration of the bob is independent of the mass and equals the suppositional acceleration of the moon at the Earth’s surface, and infers that the acceleration produced in one body by another is proportional to the mass of the acting body and independent of the mass of the body acted upon. Applying his rules of reasoning, he identifies the force of the Earth on the moon with terrestrial gravity, and likewise the forces that solar system primaries exert on their satellites, and concludes that gravitational force is universal. 

There are lots of details, many of which Harper carefully goes through. But that leaves open the question at issue, what is the general form of Newton’s method? Newton expresses the same themes of “general induction from the phenomena” at the end of the Opticks but we still want a general, precise account of the method, whatever it is. How would we apply it or recognize it in other cases? I essayed an account I called bootstrapping to which various philosophers have offered objections I will not consider here.  Others, Jon Dorling for example, have offered reconstructions. Harper discusses mine and rejects it citing the various criticisms without further assessment. That’s ok, but what we should expect is an alternative. Harper’s only suggestion is that Newton’s hypotheses are “subjunctive.” We are left to wonder how that helps. Is Newton’s method “subjunctive bootstrapping,” whatever that is, and, to engage the subjunctive, what would that be and how could we recognize it or apply it in other cases?

Harper resorts to vagaries, the substance of which is ostensive: Newton’s method is like that. We should expect more from philosophical explication than demonstratives.