Where are the numbers?

The unfortunate death of Philip Seymour Hoffman seems to have been a catalyst for lots of panicky articles about the heroin epidemic, and from the (admittedly small) sample of articles I’ve seen, calling it an “epidemic” is absurd hyperbole.

I heard a report on NPR last night with statements like “This is not the first time heroin use has skyrocketed in the United States,” descriptions of heroin “flooding” across the border from Mexico and declaration of “stark” statistics.

In the NPR piece, there’s just one number you can call a statistic, and it’s presented without enough context to allow it to support the overblown claims:

“If you look at just the raw statistics,” he says, “over the last four or five years, heroin deaths went up 45 percent.”

Of course, you could have a 45% increase if there were 100 deaths before and 145 more recently. Or if there were 100,000,000 deaths before and 145,000,000 more recently. The percentage increase alone tells us exactly nothing about whether or not there is an epidemic of heroin (ab)use in the US.

This morning, I saw that Kottke links to two stories, neither of which do much better, numbers-wise. The PBS News Hour story says things like

GIL KERLIKOWSKE, U.S. Drug Policy Director: It is a serious problem. We are seeing an increase. I think the concern is always that data usually lacks one or two or sometimes three years, depending on what the survey or what the measure is. But I can tell you, in my travels across the country, and I spoke to the national narcotics officers today at lunch, there is no question we are seeing a resurgence of heroin.

The only numbers that have even a hint of a chance at supporting claims of a serious problem or a heroin resurgence come later, when Mr. Kerlikowske mentions 22 deaths in Western Pennsylvania from heroin laced with other opiates. Of course, his point here isn’t to support the claim of a resurgence, it’s to point out that black market drugs can vary wildly in their contents. In any case, since we don’t have any idea how many people normally die from heroin in Western Pennsylvania, 22 deaths is an utterly uninformative statistic.

The article about the Vermont Governor’s State of the State speech on drug abuse gives us the hardest, and most interpretable, numbers I’ve seen, and they don’t make a good case for claims of an epidemic or floods of heroin washing over the country:

Last year, he said, nearly twice as many people here died from heroin overdoses as the year before. Since 2000, Vermont has seen an increase of more than 770 percent in treatment for opiate addictions, up to 4,300 people in 2012.

The bit about twice as many deaths is, as noted above, not very informative. But the statement that 4,300 people received treatment for opiate addictions (opiates being a superset of heroin, please note) in 2012 finally gives us something to work with.

A quick google search tells us that the population of Vermont is 626,011, so that 770% increase up to 4,300 people in treatment makes a grand total of 0.6% – that’s sixth tenths of one percent – of the population of Vermont.

In the article about Vermont’s Governor, there’s a link to another New York Times article, and it gives us similar numbers for a few more states:

Heroin killed 21 people in Maine last year, three times as many as in 2011, according to the state’s Office of Substance Abuse and Mental Health Services. New Hampshire recorded 40 deaths from heroin overdoses last year, up from just 7 a decade ago. In Vermont, the Health Department reported that 914 people were treated for heroin abuse last year, up from 654 the year before, an increase of almost 40 percent.

Maine has 1,329,000 people, so 0.002% – two thousandths of one percent – of the population died due to heroin in 2012. New Hampshire has 1,321,000 people, so 0.0003% – three thousandths of one percent – of the population there overdosed on heroin and died in 2012. The Vermont numbers in this article show that the people receiving treatment for heroin specifically make up less than 25% of the people receiving treatment for opiates (0.14% of the population, if you do the math).

This is not an epidemic. It’s tragic for the people involved, of course, and I would very much prefer a world in which no one died of heroin overdoses. I can’t imagine the pain of being addicted to heroin, or of having a loved one struggle with or lose their life to such an addiction.

But simply saying it’s an epidemic doesn’t make it true. Nor should it convince anyone that prohibition is the solution to the problem.

Update: Somehow, I had missed this other relevant post by Jacob Sullum, which makes pretty much the same point I made, with similar numbers from other unreliable sources.

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A partially problematic paragraph

I just read an interesting new paper (Hoekstra, et al., 2014) on how people – even those with substantial training in inferential statistics – consistently misinterpret confidence intervals (CIs). Reading this paper got me thinking about CIs in general, and I’ll probably return to this paper and topic again soon, but for now I want to highlight the antepenultimate paragraph of the paper (I’m irrationally happy that the paragraph I want to talk about really did just happen to be the third from the last).

In discussing the possibility of treating CIs as Bayesian credible intervals, Hoekstra, et al., write (with bracketed numbers inserted by me and corresponding to my subsequent notes):

First, treating frequentist and Bayesian intervals as inter- changeable is ill-advised and leads to bad “Bayesian” thinking [1]. Consider, for instance, the frequentist logic of rejecting a pa- rameter value if it is outside a frequentist CI. This is a valid frequentist procedure with well-defined error rates within a frequentist decision-theoretic framework [2]. However, some Bayesians have adopted the same logic (e.g., Kruschke, Aguinis, & Joo, 2012; Lindley, 1965): They reject a value as not credible if the value is outside a Bayesian credible interval [3]. There are two problems with this approach. First, it is not a valid Bayesian technique; it has no justification from Bayes’s theorem (Berger, 2006) [4]. Second, it relies on so-called “noninformative” priors, which are not valid prior distributions [5]. There are no valid Bayesian prior distributions that will yield correspondence with frequentist CIs (except in special cases), and thus inferences resulting from treating CIs as credible intervals must be incoherent [6]. Confusing a CI for a Bayesian interval leaves out a critically important part of Bayesian analysis—choosing a prior—and, as a result, leaves us with a non-Bayesian technique that researchers believe is Bayesian [7].

Notes:

[1] The immediately preceding discussion isn’t about treating frequentist and Bayesian intervals as interchangeable, it’s about, as mentioned above, treating CIs as Bayesian intervals. Even if you were to treat all frequentist CIs as Bayesian intervals, this still leaves open the possibility that some Bayesian intervals are not frequentist CIs. Not a big error, granted, but this is a basic logical issue: if A implies B, this does not imply that A and B are equivalent.

[2] It’s kind of nice to see hardcore Bayesians give a straightforward description of null hypothesis significance testing that grants that the approach has at least some positive properties (e.g., “well-defined error rates”). I mean, there’s a parenthetical later that describes NHST as “pernicious,” but still.

[3] If this isn’t kosher, maybe a different name would be better for the Bayesian analogs to CIs? Less snarkily, I’m sincerely curious how the authors propose discrete decisions be made based on Bayesian data analysis. What function does a credible interval have if it doesn’t tell us something about parameter (or predicted data) values we should consider inconsistent with our data and model? Even if we treat a credible interval’s measure of uncertainty with regard to a parameter as explicit (and primary), we can’t escape the fact that we’re implicitly (and perhaps secondarily) specifying a set of incredi… er, not credible values, too.

[4] I don’t know what all Berger says in the cited 2006 paper, but I find it hard to believe that even the most hardcore Bayesians do all and only that which is justified by Bayes’ theorem.

[5] This is nonsense. Or at least needs to be spelled out in more detail and justified. If Hoekstra, et al., are defining “noninformative” priors as invalid, then, sure, but then it’s just a tautology. If “noninformative” means something else, then a statement this strong needs to be given some support rather than just asserted. I suppose it’s possible they’re thinking along the lines of Andrew Gelman on this issue, but, for various reasons, I would guess not (e.g., the less-hardcore-Bayesian-than-some position he takes in this paper).

[6] Speaking of incoherent, in the preceding paragraph, the authors write that “frequentist CIs can be numerically identical to Bayesian credible intervals, if particular prior distributions are used.” These must be very special cases indeed if they logically imply incoherence. As with the bit about “noninformative” priors, this kind of assertion needs to be backed up, if only with citations, preferably with a brief discussion in situ. The paper is only eight pages long, after all.

[7] If we can assume, for a moment, that we’re dealing with a coherent case in which a CI and a credible interval are identical, then it’s not clear to me why treating the CI as equivalent to the credible interval is so bad. Why is the act of choosing the prior so important, if, in at least some cases, you can arrive at the same conclusions (with respect to whatever inferences you can or cannot draw from estimated intervals – see [3] above) without having explicitly chosen a prior? Or, from a different angle, if the two are equivalent, and it’s only certain priors that induce this equivalence, haven’t you implicitly chosen a prior by constructing the CI in the first place?

Okay, so the antepenultimate paragraph in this paper is pretty awful. The paper as a whole is interesting, though, so I’ll try to come back to it (and some general thoughts about CIs as a statistical tool) soon.

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Resuscitation of the Demarcation Problem?

An edited volume on (and called) The Philosophy of Pseudoscience (TPoP) came out last year. I would be hard pressed to think of a topic better suited to get me to pony up a few bucks and then spend time reading and thinking about something not directly related to my work.

The basic idea motivating the book is that Larry Laudan was wrong (or at least premature) in announcing The Demise of the Demarcation Problem. The Demarcation Problem is, in case you don’t know, the problem of differentiating between science and non-science or between science and pseudoscience (and maybe also between non-science and pseudoscience). As it happens, I’ve blogged about this Laudan essay before, though in a way that isn’t directly addressed at this new book, so in this post, I’ll review the basics of Laudan’s argument. I’ll follow up in later posts with reviews of the first few chapters of TPoP.

Spoiler alert: I remain unconvinced by the arguments in TPoP that Laudan is wrong. In order to see why (I think) they’re wrong, it will be useful to make reference to Laudan’s original essay. I’ve got it as a hard copy of a book chapter, and I can’t find it in freely-available digital format (here it is behind a rather pricey paywall, and here is most, but not all, of it on google books), so I will cover the main points made in a highly abbreviated format (and organized using a subset of Laudan’s section headers).

The Old Demarcationist Tradition

Ancient concerns with knowledge/reality vs opinion/appearance lead to Aristotle arguing that scientific knowledge is certain, deals in causes, and follows logically from first principles, which are themselves derived directly from sensory input. Thus, Laudan writes that, according to Aristotle, “science is distinguished from opinion and superstition by the certainty of its principles; it is marked off from the crafts by its comprehension of first causes.” (p. 212)

In the 17th century, the latter criterion fell out of favor. Many of the people we think of as the founding fathers of modern science (e.g., Galileo, Newton) explicitly repudiated the idea that a science necessarily addresses causes. By the 19th century, certainty was discarded, as well: “the unambiguous implication of fallibilism is that there is no difference between knowledge and opinion: within a fallibilist framework, scientific belief turns out to be just a species of the genus opinion.” (p. 213)

With certainty and causation no longer able to demarcate science from non-science, folks turned methodology to (try to) do the job. In order for methodology to do the job, philosophers had to establish that there is a single, unified scientific method and that this method is epistemically better than other, non-scientific methods. Attempts to establish the unity and epistemic superiority of method led to disagreement about what the one, true method is and ambiguity or outright falsity with respect to whether or not practicing scientists actually employ any particular proposed method.

A Metaphilosophical Interlude

Laudan says that we should ask three questions (quoted verbatim from the essay):

  1. What conditions of adequacy should a proposed demarcation criterion satisfy?
  2. Is the criterion under consideration offering necessary or sufficient conditions, or both, for scientific status?
  3. What actions or judgments are implied by the claim that a certain belief or activity is ‘scientific’ or ‘nonscientific’?

With respect to #1, Laudan argues that a demarcation criterion should (a) accord with common usage of the label ‘science’ – it should capture the paradigmatic cases of science and non-science, regardless of how it deals with more difficult, borderline cases; (b) identify the epistemic and/or methodological properties that science has and that non-science does not; and (c) be precise enough so that we can, in fact, use it to demarcate science and non-science.

With respect to #2, Laudan argues that a demarcation criterion must provide both necessary and sufficient conditions. Necessary conditions alone will only allow us to say if something isn’t science, but do not allow us to say if something is, while sufficient conditions alone only allow us to say if something is science, but do not allow us to determine what is not scientific.

With respect to #3, Laudan points out that, because it will have numerous social, political, and, in general, practical implications, “any demarcation criterion we intend to take seriously should be especially compelling.”

The New Demarcationist Tradition

More recent efforts to develop demarcation criteria have focused on what Laudan calls potential epistemic scrutability rather than actual epistemic warrant. Verificationist, falsificationist, and various approaches based on testability, well-testedness, the production of surprising predictions, and so forth, all serve very poorly as demarcation criteria for various reasons, including their frequent failure to serve as both necessary and sufficient conditions for demarcation. Plenty of obviously scientific claims aren’t verifiable, and plenty of obviously non-scientific claims are; plenty of obviously scientific claims aren’t falsifiable, and plenty of obviously non-scientific claims are. And so on.

It’s worth quoting from Laudan’s conclusion at length (emphasis in the original):

Some scientific theories are well-tested; some are not. Some branches of science are presently showing high rates of growth; others are not. Some scientific theories have made a host of successful predictions of surprisingly phenomena; some have made few if any such predictions. Some scientific hypotheses are ad hoc; others are not. Some have achieved a ‘consilience of inductions'; others have not. (Similar remarks could be made about several nonscientific theories and disciplines.) The evident epistemic heterogeneity of the activities and beliefs customarily regarded as scientific should alert us to the probable futility of seeking an epistemic version of a demarcation criterion. Where, even after detailed analysis, there appear to be no epistemic invariants, one is well advised not to take their existence for granted. But to say as much is in effect to say that the problem of demarcation… is spurious, for that problem presupposes the existence of just such invariants.

Laudan ends the essay with a brief discussion of the sorts of things that philosophy of science should be focused on, given his dismissal of the demarcation problem. The last couple pages are available in google books, but I’ll quote him here again:

It remains as important as it ever was to ask questions like: When is a claim well confirmed? When can we regard a theory as well tested? What characterizes cognitive progress?

He is, at least in part, making a semantic argument that the class of things appropriately labeled ‘science’ (and its counterparts in the classes of things labeled ‘non-science’ and ‘pseudoscience’) just isn’t particularly (philosophically) interesting. One last quote, from the concluding paragraph:

…we have managed to conflate two quite distinct questions: What makes a belief well founded (or heuristically fertile)? And what makes a belief scientific? The first set of questions is philosophically interesting and possibly even tractable; the second question is both uninteresting and, judging by its checkered past, intractable.

It’s interesting to note, given his conclusions here, that Laudan has more recently been focusing on legal epistemology, which is to say that he’s been pursuing his ‘first set of questions’ in a non-scientific area. It was also interesting to note that the essay immediately following the Demise essay in the book I have (a critique of a judicial decision about teaching creationism in Arkansas schools) kind of foreshadows this move. But I digress.

Next up: summaries and discussion of the first few essays in TPoP.

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More on (moron!) bad pop science

Blogging clearly isn’t my priority lately (I have some great posts planned, though, I swear!), but nothing beats dumb pop science writing for generating a quick post. I’m sure I’ve missed some since my last post on the topic a month ago, but I just saw a new example (via the science subreddit) that I can’t resist responding to.

From the pop science article:

Although more research is necessary, the results suggest that spirituality or religion may protect against major depression by thickening the brain cortex and counteracting the cortical thinning that would normally occur with major depression.

And from the Results and Conclusions and Relevance sections of the publicly available journal page for the publication:

… We note that these findings are correlational and therefore do not prove a causal association between [religious/spiritual] importance and cortical thickness….

A thicker cortex associated with a high importance of religion or spirituality may confer resilience to the development of depressive illness in individuals at high familial risk for major depression, possibly by expanding a cortical reserve that counters to some extent the vulnerability that cortical thinning poses for developing familial depressive illness.

It’s a subtle issue, I know, but there is a logical distinction between, on the one hand, spirituality protecting against depression by making brains thick and, on the other, thick brains protecting against depression and simultaneously being statistically associated with (self-reported importance of) spirituality.

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On bad pop science

I just love this kind of writing about abstruse, abstract physics for a lay audience:

A team of physicists has provided some of the clearest evidence yet that our Universe could be just one big projection.

In 1997, theoretical physicist Juan Maldacena proposed that an audacious model of the Universe in which gravity arises from infinitesimally thin, vibrating strings could be reinterpreted in terms of well-established physics. The mathematically intricate world of strings, which exist in nine dimensions of space plus one of time, would be merely a hologram: the real action would play out in a simpler, flatter cosmos where there is no gravity.

[snip]

In two papers posted on the arXiv repository, Yoshifumi Hyakutake of Ibaraki University in Japan and his colleagues now provide, if not an actual proof, at least compelling evidence that Maldacena’s conjecture is true.

[snip]

Neither of the model universes explored by the Japanese team resembles our own, Maldacena notes.

Excellent.

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A quick pfisking

The first link in this week’s “This week in stats” (by Matt Asher) post leads to a fairly silly rant (by a Wesley) about p-values. I feel like it deserves a quick (but partial, because I don’t disagree with everythingfisking, in addition to reiterating the point made by Mr. Asher that, whatever problems p-values have, no solutions are on offer here (though I know at least a dozen or so people who would argue against his claim that no one has come up with a satisfactory substitute to p-values). Anyway:

Wesley: P-values … can also be used as a data reduction tool but ultimately it reduces the world into a binary system: yes/no, accept/reject.

Noah: Given that p-values are but one part of a statistical analysis in the frequentist hypothesis testing tradition, I have a hard time seeing why this is so problematic. A calculated test statistic either exceeds a criterion or it doesn’t. This doesn’t tell the whole story of an data set, but it’s not meant to.

W: Below is a simple graph that shows how p-values don’t tell the whole story.  Sometimes, data is reduced so much that solid decisions are difficult to make. The graph on the left shows a situation where there are identical p-values but very different effects.

N: I don’t understand what Wesley means when he links data reduction and decision-making difficulty, so I’ll leave that one alone. I’ll also not go into depth about why I think these graphs kind of stink (to mention maybe the worst thing about the graphs: they’re mostly just white space, with the actual numbers of interest huddled up against the [unnecessary] box outline).

Anyway, it’s not at all clear how the two “effects” in the left panel could be producing the same p-value (and the code from the post isn’t working when I try to run it – the variable effect.match is empty, since the simulation with the minimum CI difference isn’t in the set of p-values that match, i.e., logical indexing fails to produce a usable index – so I can’t reproduce the plot). Contra my intuition when first seeing the graph, it is not illustrating a paired t-test, but, rather, two single-sample t-tests. I gather that each of these red dots is illustrating a mean, and each vertical line is illustrating an associated confidence interval, and that the means are being compared to zero. Given that one (CI) line covers zero and the other does not, the p-values shouldn’t be the same.

W: The graph on the right shows where the p-values are very different, and one is quite low, but the effects are the same.

N: I disagree that the effects are the same. Sure, the means are the same (by design), but the data illustrated on the right is much more variable than the data illustrated on the left.

W: P-values and confidence intervals have quite a bit in common and when interpreted incorrectly can be misleading.

N: I agree, but this is a pretty anodyne statement. Now back to the fisking.

W: Simply put a p-value is the probability of the observed data, or more extreme data, given the null hypothesis is true.

N: Close, but nope. A p-value is the probability of an observed or more extreme test statistic, not the data. It’s an important distinction, and it’s related to the conflation of “effects” with “means” and the different p-values for identical means with different variability around the means in the figure above.

So, anyway, none of this is meant to imply that p-values don’t have limitations. Of course they do. And understanding these limitations is worthwhile. But posts like Wesley’s don’t, in my opinion, do much to foster such understanding.

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Something old, something new, two somethings under review

I’ve recently revised a manuscript that had been posted on my CV page for a while. It’s a rather technical paper on optimal response selection and model mimicry in Gaussian general recognition theory. In its previous state, it was all and only technical information on these topics. Now, thanks to the urging (and encouraging) of my co-author, it has an introduction and conclusion that actually relate the technical information to a (slightly) wider body of work. It’s here, if you’re interested.

I’ve also recently revised a manuscript that, until today, had never been exposed to public scrutiny. It’s from work I did while at CASL on individual differences in non-native perceptual abilities and how these abilities relate to second language learning of (slightly) higher-level linguistic structure. It feels very nice to finally have it written up and ready for public consumption. It’s here, if you’re interested.

Both papers are under review at, I hope, suitable journals. I mean, the first is under review at pretty much the only journal I can even begin to imagine it being published in. I’m reasonably confident that it will, eventually, be published there. On the other hand, I could see the second fitting in okay in a number of different journals. The one I submitted it to is fairly high-profile (and high impact factor!), though, so it would be nice to get it published there.

That’s all for now.

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Quotation of a day

Following (i.e., stealing the idea from) Don Boudreaux, who posts interesting and thought provoking “quotations of the day” (e.g., today’s post on evolution), here’s an amusing bit from page 72 of Hamming’s Digital Filters:

The relationship of formal mathematics to the real world is ambiguous. Apparently, in the early history of mathematics the mathematical abstractions of integers, fractions, points, lines, and planes were fairly directly based on experience in the physical world. However, much of modern mathematics seems to have its sources more in the internal needs of mathematics and in esthetics, rather than in the needs of the physical world. Since we are interested mainly in using mathematics, we are obliged in our turn to be ambiguous with respect to mathematical rigor. Those who believe that mathematical rigor justifies the use of mathematics in applications are referred to Lighthill and Papoulis for rigor; those who believe that it is the usefulness in practice that justifies the mathematics are referred to the rest of this book…. Furthermore, since we are interested in the anatomy of the mathematics, we shall ignore many of the mathematically pathological cases. The fact that we are dealing with samples of a physical function implies that we are trying to understand a reasonable situation.

It makes on feel downright Newtonian. If it works, use it, foundations be damned.

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More than who in the what now?

Kirk Goldsberry explains an interesting new basketball shooting statistic he and a colleague have developed today. I’ll be discussing two strange statements that Mr. Goldsberry made. One is strange for logical reasons, and the other is strange for syntactic reasons.

In the introduction of the article, Goldsberry is expressing an amazing fact about LeBron James:

…However, consider the following ridiculous statistical couplet:

No player scored more points close to the basket than LeBron James last season.

No player converted a higher percentage of his shots near the basket than LeBron James last year.

Think about that. Not only did he outscore every player in the entire league within the NBA’s most sacred real estate, he converted his shots at the highest rate, too.

Okay, I’ve thought about it, and I don’t find it ridiculous at all. Unless James took substantially fewer shots close to the basket than did other NBA players (which even someone as NBA ignorant as me knows just can’t be the case), the fact that he was more accurate makes it essentially a mathematical necessity that he would outscore everyone else. This seems like an oddly innumerate bit in an otherwise relatively statistically sophisticated article.

The syntactically strange sentence is more fun. Goldsberry writes:

No player accumulated more points than expected than James.

It’s clear what he means – no one exceeded the number of expected points to a greater degree than did James – but, as written, this sentence is meaningless. I mean, I can garner some meaning from it, but it seems ill-formed for expressing that meaning (or any other).

It reminds me of the plausible Angloid gibberish sentences “More people have been to Russian than I have” and “In Michigan and Minnesota, more people found Mr Bush’s ads negative than they did Mr Kerry’s.

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Picking some more nits

Geoffrey Pullum has an interesting recent essay on the difficulties of pinning down exactly how old the cognitive revolution is. Naturally, I won’t be focusing directly on this topic.

Rather, I’d like to take this opportunity to bemoan the fact that Pullum is uncritically invoking Kuhnian philosophy of science:

Maybe revolution is not quite the right metaphor. I know Thomas Kuhn taught us that science develops through revolutions, the detailed work being done under the assumptions of the last one during periods of “normal science.” And it’s an exciting thought, the idea of an annus mirabilis when the whole conceptual world turns upside down, and what was formerly nonsense becomes accepted science (and vice versa), and old guys who don’t get with the program are left to face an embittered retirement. But I’m inclined to think it isn’t quite like that in this case.

I’d give him credit for challenging the idea that “it isn’t quite like that in this case” if I wasn’t already convinced that it’s never quite like that. As Larry Laudan wrote in 1986 (for the record, that’s 27 years ago) in Science and Values (p. xii, in the preface; emphasis mine):

In sum, this is a book about the role of cognitive values in the shaping of scientific rationality. Among recent writers, no one has done more to direct our attention to the role of cognitive standards and values in science than Thomas Kuhn. Indeed, for more than two decades, the views of Thomas Kuhn – and reactions to them – have occupied center stage in accounts of scientific change and scientific rationality. That is as it should be, for Kuhn’s Structure of Scientific Revolutions caused us all to rethink our image of what science is and how it works. There can be no on active in philosophy, history, or sociology of science whose approach to the problem of scientific rationality has not been shaped by the Gestalt switch Kuhn wrought on our perspective on science. This debt is so broadly recognized that there is no need to document it here. Less frequently admitted is the fact that, in the twenty-two years since the appearance of The Structure of Scientific Revolutions, a great deal of historical scholarship and analytic spadework has moved our understanding of the processes of scientific rationality and scientific change considerably beyond the point where Kuhn left it.

Indeed, we are now in a position to state pretty unequivocally that Kuhn’s model of scientific change, as developed in Structure and elaborated in The Essential Tension, is deeply flawed, not only in its specifics but in its central framework assumptions. It is thus time to acknowledge that, for all its pioneering virtue, Kuhn’s Structure ought no longer be regarded as the locus classicus, the origin and fount, for treatments of these questions. It is time to say so publicly and openly, lest that larger community of scientists and interested laymen, who have neither the time nor the inclination to follow the esoteric technical literature of these fields, continues to imagine that Kuhn’s writings represent the last (or at least the latest) word on these matters.

Some simple math puts the origins of Kuhn’s ideas right around the time the so-called cognitive revolution began (though, as argued by Pullum, it’s not clear exactly when the cognitive revolution started, or even if it has a discernible beginning). It seems that Laudan’s nearly thirty year old call to move past Kuhn’s Structure either wasn’t heard or wasn’t heeded.

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