Clinical Versus Statistical Prediction:
The Contribution of Paul E. Meehl
ᮢ
William M. Grove
University of Minnesota, Twin Cities Campus
The background of Paul E. Meehl’s work on clinical versus statistical prediction
is reviewed, with detailed analyses of his arguments. Meehl’s four
main contributions were the following: (a) he put the question, of whether
clinical or statistical combinations of psychological data yielded better
predictions, at center stage in applied psychology; (b) he convincingly
argued, against an array of objections, that clinical versus statistical prediction
was a real (not concocted) problem needing thorough study; (c) he
meticulously and even-handedly dissected the logic of clinical inference
from theoretical and probabilistic standpoints; and (c) he reviewed the
studies available in 1954 and thereafter, which tested the validity of clinical
versus statistical predictions. His early conclusion that the literature
strongly favors statistical prediction has stood up extremely well, and his
conceptual analyses of the prediction problem (especially his defense of
applying aggregate-based probability statements to individual cases) have
not been significantly improved since 1954. © 2005 Wiley Periodicals,
Inc. J Clin Psychol 61: 1233–1243, 2005.
Keywords: Paul E. Meehl; clinical psychology; clinical prediction; statistical
prediction, actuarial prediction; data gathering; data combination; MMPI
codebook
A major problem with reviewing a limited area pioneered by a genius is that all the
important, original ideas have already been expounded. My aim in this article is not to
present novelty, but rather to summarize Meehl’s work on clinical versus statistical prediction.
This controversy concerns the comparative accuracy of two ways of combining
predictive data: clinicians’ informal judgments versus statistical (mechanical) combination.
The history of the controversy is outlined. Paul Meehl’s remarkable contributions to
understanding and resolving this controversy are discussed.
This article is dedicated to the memory of P. E. Meehl—mentor, colleague, and friend. I also gratefully acknowledge
the assistance of Leslie J. Yonce and Martin Lloyd in the completion of this article.
Correspondence concerning this article should be addressed to: William M. Grove, Psychology Department,
N438A Elliott Hall, 75 East River Road, Minneapolis, MN 55455-0344; e-mail: grove001@umn.edu
JOURNAL OF CLINICAL PSYCHOLOGY, Vol. 61(10), 1233–1243 (2005) © 2005 Wiley Periodicals, Inc.
Published online in Wiley InterScience (www.interscience.wiley.com). DOI: 10.1002/jclp.20179
The clinical versus statistical prediction debate is central to the assessment and prediction
of human (and organizational) behavior because of the following argument formulated
by Meehl. I have elaborated it slightly, based on discussions with Meehl and on
my own reasoning, the better to exhibit its inexorable logic.
1. Psychologists spend a good deal of time making explicit, or at least implicit,
predictions. For example, “clinical judgments about the therapeutic potential of
cases” are implicit predictions that a patient will do better with treatment A than
they would if they instead got treatment B (bearing in mind that either A or B
could, in fact, represent no treatment—watchful waiting). Decisions about personnel
selection, admission of students to institutions of higher learning, civil
commitment of the mentally ill, eligibility for parole—all these are more or less
explicit predictions that one course of action will turn out better than another in
the future, if not for the client, student, or inmate, then for the institution on behalf
of which predictions are being made.
2. “A . . . distinction is that between the source or type of information employed in
making predictions, and the manner in which this information is combined for
predictive purposes.” (Meehl, 1954, p. 15)
3. “As for the combining method, by mechanical (or statistical) I mean that the
prediction is arrived at by some straightforward application of an equation or
table to the data. [Today, we would add “or computer program.”] . . . The defining
property is that no judging or inferring or weighing [during combination] is done
by a skilled clinician . . . By non-mechanical or informal methods of combining I
mean those of any other sort” (Meehl, 1954, p. 15–16). Note that this way of
framing the distinction suffices to make clinical and statistical prediction mutually
exclusive. If actuarial predictions are synthesized clinically, this is clinical
prediction; if clinical predictions are synthesized statistically, this is statistical
prediction. There is no such thing as a true hybrid. This point has been repeatedly
misunderstood, and in my opinion often tendentiously and misleadingly argued,
by some psychologists. One example is the argument that because a clinician can
integrate the output of a statistical prediction scheme and his or her own judgments,
a hybrid exists. This is false because from a formal standpoint, the clinician
is (as usual) synthesizing two or more potentially disparate items of information
available to them (the statistical prediction, and one or more other items, which
may or may not have entered into the statistical prediction). Clinicians must use
their own judgment to deal with discrepancies in the data, e.g., a statistical prediction
that says a sex offender will recidivate, and a prison psychologist’s statement
that the prisoner likely will not reoffend. This is precisely the sort of thing
Meehl called “clinical data combination.” Another example arises when broad
clinical judgments form at least part of the inputs to a statistical prediction scheme.
Once clinicians have enunciated their judgments (diagnoses, trait ratings, prognostications)
and they have been quantified (even as crudely as “will reoffend”
vs. “won’t”), the statistical formula requires no professional judgment to arrive at
a prediction; this is exactly what Meehl meant by “statistical data combination.”1
1
This sharp demarcation does not prevent discovering that a particular subvariety of clinical prediction, e.g.,
our example of clinical recidivism prediction that is informed by the results of statistical-prediction scales,
outperforms straight statistical prediction. Hence, nothing in terms of finding out how to make the best predictions
is prejudged by making clinical and statistical prediction mutually exclusive, exhaustive categories.
1234 Journal of Clinical Psychology, October 2005
4. “It is obvious . . . that the results of applying these two different [data combining]
techniques to the same data set do not always agree. On the contrary, they disagree
a sizeable fraction of the time. Now if a four-variable regression equation or
. . . actuarial table tells the criminal court judge that this particular delinquent will
probably commit another felony in the next 3 years and if a case conference or a
social worker says he will probably not . . . the plain fact is that [the judge] cannot
act in accordance with both of these incompatible predictions.” (Meehl, 1986,
p. 372)
5. The best prediction scheme is the one that produces the smallest error for each
client. This might involve using clinical prediction in one case and statistical
prediction in another case. However, to choose the data combining method on a
case-by-case method, the overseer of predictions would have to know, in advance,
which combination method would produce the best result for the individual case.
Such information is, as far as I know always lacking. Note that dividing cases into
classes, on the basis of before-the-prediction known characteristics of individuals
or their situations, and using different data combination methods for different
classes, is quite another matter and may prove eminently sound.
6. Barring such impossible-to-apply metarules as “Use the best data combination
method for this particular case,” the best prediction scheme, from the standpoint
of Bayesian decision theory,2
is one that maximizes expected utilities for the
stakeholder on behalf of whom the prediction is made. Consider first yes–no (or
succeed–fail) predictions (e.g., a patient will or won’t soon attempt suicide, if not
hospitalized at once). When relative costs of false positive versus false negative
predictions are unknown, or agreement cannot be reached among stakeholders
about their relative magnitudes, it is not irrational to treat the two kinds of cost as
equal. Under such circumstances, the decision rule that minimizes expected costs
is the one that maximizes the hit rate of predictions.3
For quantitative predictions
(e.g., predicting number of publications in graduate school), minimizing the
expected squared errors of prediction is a generally accepted rule in psychology.
(It corresponds to the optimization criterion in multiple linear regression, for
example.) For such a loss criterion, under- and overpredictions (corresponding to
false negative and false positive yes–no predictions, respectively) of a given magnitude
are treated equivalently.
7. Therefore, in the absence of reliable cost information, the best overall data combination
method is the one with the best overall classification accuracy (hit rate)
or best overall correlation with the criterion.
8. Overseers of prediction (i.e., clinicians making informal predictions, or users of a
computer program making actuarial predictions) are obliged to maximize expected
2
We set aside other decision rules, such as minimizing the maximum loss, because they produce such riskaverse
decisions as to appear unattractive to most decision theorists.
3
Expected disutility for such a decision equals Pr$FP% ϫ costFP ϩ Pr$FN% ϫ costFN , where Pr$FP% is the
probability of a false positive and Pr$FN% that of a false negative; the two costs are disutilities associated with
each possible kind of misprediction. Without loss of generality, we can express this in terms of regrets (actual
cost minus minimum potential cost, for a given state of nature; Blackwell & Girschick, 1954). Similarly, we
can in turn express the decision problem in a metric for which regretFN ϭ 1. Then we want to minimize
Pr$FP%
regretFP
regretFN
ϩ Pr$FN%. When costs (regrets) are unknown and we take the default course (i.e., to act as
if they are equal), then we want to minimize Pr$FP% ϩ Pr$FN% to maximize expected utility. This is the same
as maximizing Pr$TP% ϩ Pr$TN% (true positives and negatives), which in turn, is the same as maximizing the
hit rate.
Clinical Versus Statistical Prediction 1235
utility for a relevant stakeholder.4
This is what it means to have a fiduciary responsibility
(“Principle A, Beneficence and Nonmaleficence”; American Psychological
Association [APA] Council of Representatives, 2002).
9. The principle of beneficence therefore generally requires psychologists to choose
and use the prediction method that yields the most accurate predictions. This
method may differ from class to class of prediction situations. “It is foolish, and
I would say even immoral, for a trusted . . . expert . . . to employ a method which
has a lower hit-frequency than another available method.” (Meehl, 1956b, p. 163)
When first presented, perhaps fewer psychologists found this argument compelling
than would find it so today. It is worthwhile to examine work predating Meehl’s book to
understand the context in which Meehl’s contribution entered the field.
How Meehl Found the Controversy, Circa 1954
The first empirical work known to me is Burgess’ 1928 study of parole failure prediction.
There were theoretical debates, and there had been an APA symposium (chaired by
E. L. Kelly, mentioned in Meehl, 1986). The principal protagonists of actuarial prediction
were Lundberg (1926, 1941) and then Sarbin (1941, 1942, 1944), the latter beginning
with his work at the Elgin State Hospital (where one of the early actuarial prediction
studies was done). Lundberg and Sarbin were advancing a much stronger thesis than that
actuarial prediction typically outperforms clinical prediction. Instead, Sarbin argued that,
as Meehl paraphrased it, “the clinician is always predicting actuarially and from classes
whether he knows it or not” (Meehl, 1954, p. 29). There had also been published a limited
number of empirical comparisons of clinical and statistical prediction, almost all of them
significantly methodologically flawed. The most comprehensive review (Sarbin, 1944)
covered only four studies.
The essence of Sarbin’s theoretical position was that the clinician operates as an
empiricist, gathering impressions of the past that allow prediction of the future. The
clinician is forming, in essence, S–R bonds that link assessment data on the S side to
predictions on the R side. All such bonds are inherently probabilistic and are based on the
comparison of the current data with past data, making a prediction for the current case
that is similar to that for a past case with similar data. According to Sarbin, single-case
probability statements are unverifiable; hence, they are meaningless (at least according to
Peirce’s empirical-conditions-of-verification theory of meaning). For example, suppose
one says, “The probability that Professor A will attend the movies tonight is .7.” Now,
either A will attend, or she will not attend; no sensible measure of attendance can yield
the value .7, no matter what A does. Hence (on the Peirceian theory), the statement is
meaningless. Sarbin followed Reichenbach (1938) by identifying the rationality of singlecase
probability statements with their value for deciding on action. Clinicians simplify
their cognitive task by (in principle) putting stimuli (assessment data) into equivalence
classes and predicting like outcomes for members of the same class. Naturally, this is not
supposed to be a complete rendition of what clinicians actually do. In fact, due to human
cognitive limitations (e.g., on memory) they imperfectly approximate the behavior of an
actuarial table. It was for this reason that Sarbin held that clinicians could not, in principle,
outperform an actuarial table—the table engenders residual predictive error (to the
4
We neglect situations where there are multiple stakeholders whose utility assessments conflict. As far as I
know, this does not tilt the balance in favor of, or against, either clinical or statistical prediction.
1236 Journal of Clinical Psychology, October 2005
extent that the table isn’t a perfect predictor of behavior), whereas the clinician’s head
also engenders recollection error, misconstrual, and other errors.
Against this background, Meehl began thinking about the prediction problem, the
nature and proper role of clinical inference, and formal prediction methods in the 1940s.
After about a decade wherein he spent a substantial part of his working hours applying
his capacious intellect to these problems, he published Clinical Versus Statistical Prediction.
He had to offer it to three publishers to get it in print, because editors were sure it
would not sell. (The first two publishers made clinical judgment errors—the book went
through seven printings and, after being out of print for a time, is again selling well;
Meehl, 1996. It has a phenomenally high ongoing citation rate, when one considers it is
almost 50 years old.)
What Meehl Accomplished in His 1954 Book
Meehl made four major contributions in his famous little book (and subsequent related
work). The first and most essential of these was to draw a sharp distinction between data
gathering (e.g., interview, psychometrics, behavioral observation) from data combination,
with a subsequent focus almost exclusively on the latter (Meehl, 1954, p. 18). He
identified statistical, actuarial, or formal prediction with procedures that required no professional
judgment; they could be carried out by a clerk (today, we would say by a computer
program). Clinical, informal, or impressionistic prediction includes everything else.
A second contribution was to recognize that, thus put, the clinical versus statistical
prediction distinction is unavoidable. In 1986, he made explicit what was, to some extent,
implicit in 1954:
Some critics [of my 1954 book] asked a question that Dr. Holt still asks, and which I confess
I am totally unable to understand. Why should Sarbin and Meehl be fomenting this needless
controversy? Let me state as loudly and as clearly as I can manage . . . that Sarbin and I did not
artificially concoct a controversy . . . between two methods that complement each other and
work together harmoniously. I think this is a ridiculous position when the context is the pragmatic
context of decision making. You have two quite different procedures for combining a
finite set of information to arrive at a predictive decision. . . . [These two procedures] disagree
a sizeable fraction of the time. . . . The plain fact is that [a decision maker] cannot act in
accordance with both of [two] incompatible predictions. Nobody disputes that it is possible to
improve clinicians’ practices by informing them of their track records actuarially. Nobody has
ever disputed that the actuary would be well advised to listen to clinicians in setting up the set
of variables. (Meehl, 1986, p. 372)
A third contribution was his subtle and engaging treatment of the problems and
processes of clinical judgment. He was very sympathetic to the clinician, as one might
expect. (Paul was a practicing psychotherapist who favored psychodynamic and rationalemotive
methods.) Of the book’s 10 chapters, the second through seventh concerned
clinical judgment, with titles like “The Special Powers of the Clinician,” “The Problem
of the Logical Reconstruction of Clinical Activity,” and “Remarks on Clinical Intuition.”
In the fifth chapter, he argued that Sarbin was mistaken in contending that clinicians can
in principle, do no more than imitate actuarial tables. Paul colorfully paraphrased Sarbin’s
position as “the clinician is a second-rate substitute for a Hollerith machine” (Meehl,
1954, p. 76).
A central part of the discussion of limitations on actuarial prediction accuracy stems
from Paul’s insights about predicting behavior from class frequencies. This led to Paul’s
famous “broken leg case” example, which incidentally shows how actuarial prediction is
Clinical Versus Statistical Prediction 1237
not limited to making judgments about groups of individuals. Suppose we observe Professor
A, and find he regularly goes to the movies on Tuesday nights. Our actuarial table,
built on what may be years of observation says, “If it’s a Tuesday night, then Pr$Professor
A goes to movies% ϭ .9.” But suppose we also know that on Tuesday morning Professor
A broke his leg; his hip cast will not allow him to fit into a theater seat. (This example was
concocted circa 1954, before handicapped-accessibility laws!) Any human judge with a
modicum of sense will not say that Pr$goes to movies% for that night equals .9, or anything
like .9; they’ll predict a probability in the neighborhood of zero. This is one of
Paul’s “special powers of the clinician.”
As was typical for Paul, he identified this critical problem with actuarial prediction,
and then he went further, demonstrating the central flaw in the critique as follows. First,
the base rate of people breaking a leg is low, and so “broken leg cases” need not substantially
decrease the accuracy of statistical predictions. Second, in the broken leg example,
we have a highly reliable theory allowing us to predict clinically that Professor A has a
very small probability of going to the movies; the theory rests on the physics of fitting a
person with a hip cast into a 1954 movie seat. However, behavioral science theories are
extremely seldom as well corroborated as those of physical mechanics. Third, the broken
leg in Meehl’s example reduces the probability of movie attendance to zero, or some
figure close to it. By contrast, when rare events occur in applied psychology, the event
seldom guarantees that a person will, or will not, engage in the behavior of interest.
Indeed, human behavior is so multidetermined that even unusual events typically change
the probabilities modestly, or at most moderately. In sum, it is easy to see that “broken leg
cases” exist and offer an opportunity for the clinician to do what the formula cannot.
However, as Paul always maintained, it is very difficult to know whether a given case is
a bona fide broken leg case, i.e., whether the clinician should overrule the actuarial
prediction for a particular individual, or follow it.
Another important part of Paul’s third contribution was his rebuttal of Sarbin. Briefly,
he pointed out that Sarbin did not “distinguish carefully between how you get there [i.e.,
to a certain judgment] and how you check the trustworthiness of your judgment” (Meehl,
1954, p. 31). Second, Sarbin mistook the form of predictions, by putting them in singlestatement
form, <Student X has one chance in 6 of meeting the standards of competition
in the university>, whereas they actually involve two statements, the first of which is the
actual prediction, “<The student X will not succeed at the university>” (Meehl, 1954,
p. 32). The second statement quantifies the uncertainty of the prediction: <The probability
that the prediction is correct is five in six.> (Note that I have used Quine corners to clarify
the extents of statements, instead of nesting quotation marks.) Sarbin’s way of collapsing
the two statements had the effect of tendentiously making the clinician sound like an
unreliable actuary; Paul rejected this conflation. Paul also criticized Sarbin’s implicit
position that there is a single true probability of student X succeeding, to which the
clinician only approximates. Instead, on a frequentist view (Reichenbach, 1938; or even
better, Kyburg, 1974) there are as many true probabilities as there are reference classes to
which X belongs.
Finally, in his chapter on the logic of clinical activity, Meehl delivered his strongest
argument against Sarbin’s central thesis. He proposed an analogy that shows clinicians
can in fact, be doing something in principle different from counting up frequencies in
reference classes. The analogy involves a box repairperson (the “clinician”) who is presented
with an opaque box with push-on buttons on one side and lights on the other. One
can press buttons and then observe what, if any, lights come on. The way these boxes are
constructed is generally similar, but wiring details vary from box to box. Our repairperson
knows this fact from examining many such boxes inside and out. Given all this, our
1238 Journal of Clinical Psychology, October 2005
repairperson may press shrewdly chosen combinations of buttons, observe the results,
and then concoct a structural-dynamic theory of how a particular box is wired. A few
more presses may suffice to test the theory. If the repairman’s theory is essentially correct,
it will generally yield quite accurate predictions. Now, clinicians could at least
sometimes be doing something of this sort when they examine clients and think about
them. If they do something of this kind, they are not just counting up frequencies for S–R
connections.
Many people who claim acquaintance with the book seem only to know about chapter
8, which systematically examines 20 empirical studies comparing clinical to statistical
prediction.Abox score approach was used, effectively counting tied performances between
clinical and statistical prediction as “wins” for the actuary. This review was the fourth
major accomplishment of Meehl in his book. It was also the locus of the only flat-out
error in the book that is known to me. In discussing Hovey and Stauffacher’s (1953) study
of clinical versus actuarial MMPI interpretation, Paul did not detect a mistake (pointed
out by McNemar, 1955) that the original authors made in computing the degrees of
freedom on a test. When Meehl (1986) said he would change at most 5% of the book, he
wasn’t referring to unambiguous error. Instead, he meant that, in retrospect, it seemed he
had overemphasized the advantage configural judgment would afford clinicians.
The book closes by making a point that depends on his earlier delineation of two uses
of statistics: structural versus discriminative (Meehl, 1954, pp. 11–15). Statistics are used
structurally when one models the nature and relationships of entities and events, e.g.,
when a factor analysis is conducted to explain the correlations between cognitive test
scores, or when a prediction formula is developed. Statistics are used discriminatively to
test whether, for example, one type of fertilizer gives better crop yields than another
fertilizer, or clinician-generated predictions are more accurate than actuarial ones. Meehl
points out that if the clinician eventually proves to be more accurate than the actuary is,
this can only be demonstrated by the discriminative use of statistics. In that sense, “always
the actuary will have the final word.” (p. 138)
What Meehl accomplished in his 1954 book was remarkable. By my estimation, he
gave himself a very tough act to follow. Because he got so much right so early, he did not
have occasion to publish fundamentally new or substantially changed views on the subject,
though he continued thinking and writing about this topic throughout his career.
Meehl’s Work on Clinical Versus Statistical Prediction After 1954
From 1954 until late in his life, Paul collected numerous articles concerning clinical
judgment and clinical versus statistical prediction, many of them sent to him by scholars
around the country. Those that contained empirical comparisons between the two methods
he summarized narratively on 66 tapes (originally onto magnetized belts—“dictabelts”)
for use in a second and enlarged edition of his book—which was, alas, never written.
These summaries were the springboard for my own meta-analysis of studies concerning
this controversy.
Meehl followed up the book with practical, if preliminary, first steps on the path
suggested by the data. His student Hallbower (1955) had completed a dissertation concerning
actuarial prediction from the MMPI by assigning profiles configurally to classes
based on combinations of several high (and, more rarely, low) clinical scale scores; a
manual giving probabilistic predictions about individuals having each of these “code
types,” but based on limited Ns for each type, was provided. Meehl discussed this work
and its implications in Wanted—A Good Cookbook (Meehl, 1956a). This led to a cottage
industry of researching and cataloging MMPI, and now MMPI-2, code types (Gilberstadt
Clinical Versus Statistical Prediction 1239
& Duker, 1965; Gynther, Altman, & Sletten, 1973; Lachar, 1974; Marks, Haller, & Seeman,
1997; Marks & Seeman, 1963; Marks, Seeman, & Haller, 1974; McGrath & Ingersoll,
1999), the most thoroughgoing and successful application of actuarial prediction in
clinical psychology.
In 1957, Paul again addressed the vexing “broken leg problem” in “When Should We
Use Our Heads Instead of the Formula?” He established four points about his “broken
leg” example that differ markedly from typical occasions when a clinician is moved to
countervail an actuarial prediction:
1. A broken leg is “an objective fact, determinable with high accuracy”;
2. the “correlation [of a broken leg] with relative immobilization is near perfect,
based on a huge N, and attested by all sane men . . .”;
3. Interaction effects between a broken leg and various other factors that influence
going to the movies “are conspicuously lacking”—hence, the broken leg fact can
be considered in isolation; and
4. “the prediction [that a hip-casted professor will not go to the movies] is mediated
without the use of any doubtful theory . . . ” (Meehl, 1957, p. 85)
These conditions are not met when Dr. Smith decides, based on his “gut” feeling, that
Ms. Jones has a markedly hysteroid personality and so won’t do well in insight-oriented
psychotherapy, despite an actuarial prediction that she will. Alas, Meehl did not give a
convincing analysis of when, if ever, clinicians are justified in departing from actuarial
predictions under less than “broken leg” circumstances. Meehl emphasized that this is
not, primarily, a conceptual problem. It is mostly a matter of the rarity of exceptions,
which make us reasonably want to “break the actuarial rules,” and the consequent paucity
of good outcome data on clinicians’ success rates when they do break those rules.
In 1965 (“Seer over Sign: The First Good Example”), Paul mentioned, but did not
fully present, 51 studies on clinical versus statistical prediction, which tended toward the
same conclusion he reached in 1954. The main point of this article, however, was his
belief that he had found a clinical prediction notably superior to actuarial schemes. This
time the evidence came from two studies, both involving the detection of homosexual
orientation from the Thematic Apperception Test. However, as with Hovey and Stauffacher
(1953) before, this sanguine view was subsequently corrected (Goldberg, 1968). It
seems that Paul neglected to notice, or failed to give sufficient weight to, the fact that
across two studies, no clinical judge showed sustained performance superior to the actuary.
The clinicians in Study I who outperformed statistical prediction showed inferior
accuracy in Study II, and vice versa. As a result, sampling error is a plausible explanation
for any apparent superiority of clinical prediction.
Meehl’s 1986 “Causes and Effects of My Disturbing Little Book” article, written for
a symposium on the 40th anniversary of his original book, relates a bit of history of
Meehl’s beginning interest in this topic, and the considerable difficulty he had in publishing
it. It is here that he explicitly refutes Zubin’s (1956) and Holt’s (1958) claims that
this is a false controversy, or based on a misunderstanding. Zubin (1956), for example,
stated, “the distinction between actuarial and clinical prediction is heuristic rather than
basic” (p. 627). Zubin also states that from his chosen point of view, “the question of
whether the actuarial approach is superior to the clinical is tantamount to asking whether
the sperm is more important than the ovum” (p. 627). The point of view of which Zubin
speaks is the advancement of our knowledge about the prediction of human behavior. But
this is not the problem Meehl tried to solve; his problem was to pick the right tool for the
practical task at hand. If by “heuristic” Zubin meant “pragmatic,” then he and Meehl
1240 Journal of Clinical Psychology, October 2005
were, this far, in agreement. When presented with a current need to make predictions for
a series of cases, clinical and statistical prediction methods do not cooperate like a ratchet
wrench and its socket set, let alone an ovum and a sperm. Instead, they compete like
screwdriver and pry bar, as ways to open a can of paint.
I quoted Meehl’s answer to such claims earlier in establishing the controversy’s
importance. Suppose one grants, as I would not, that the distinction between clinical and
statistical classes of prediction methods is in some ways conventional, rather than objectively
deriving from two crucial, linked facts—nonmechanical prediction schemes require
subjective judgments, and as such always lack complete reproducibility. Even granting
ex hypothesi that the distinction is not written in stone, this would not diminish the
importance of answering the question: “For a given prediction problem, which of these
‘conventionally’ distinguishable methods yields at present the more accurate predictions?”
Meehl made much the same point about the non-artificiality of the controversy in
Grove and Meehl (1996).
An article in Science by Dawes, Faust, and Meehl (1989) referred to an in-process
meta-analysis of comparison studies of clinical versus statistical prediction. That metaanalysis
(Grove, Zald, Lebow, Snitz, & Nelson, 2000) summarized results from 136
studies concerning the prediction of human health and behavior. Dawes et al. (1989)
speculate as to why so few practitioners seem to have changed practice habits in the face
of such an increasingly massive and consistent body of evidence. This same topic was
treated in Grove and Meehl (1996), wherein a preliminary analysis of effect sizes from
the meta-analysis was reported. (Meehl wrote well over half of this paper, but we flipped
a coin to establish the authorship order.) Meehl also very carefully analyzed numerous
objections to the meta-analytic results, or to the imperative that actuarial prediction be
used much more often. Paul’s final noteworthy writing on the topic was his new forward
to the 1996 reprint edition of his 1954 book (Meehl, 1954/1996, pp. v–xii). There, he
refuted several “legends” about him and his views, which try (or tend) to undercut the
perception that he approached this issue with an open mind.
Clearly, Paul’s views of major issues in the clinical versus statistical prediction controversy
changed little over the years. No great theoretical breakthroughs, radically
improved prediction methods, or momentously different empirical outcomes emerged
after 1954. However, this did not have the effect of making Meehl’s ideas “old hat” or
reducing his contribution to an historical footnote. Indeed, to this day, applied and cognitive
psychologists find his writings fresh, insightful, unusually clear and careful, and
engagingly presented.
Importance of Paul’s Ideas and Conclusions Today
As just noted, none of Paul’s “disturbing little book” needs to be retracted and little even
needs significant modification. Over time, it became clear that in 1954, he was somewhat
too sanguine about clinicians’ abilities to process configurations of (nonlinear interactions
among) assessment data. Nevertheless, he was prescient about how the studies
would turn out, extrapolating rather accurately from 20 mostly not very good studies, to
over 160 often well-conducted comparisons.
In 1954, there were few prediction problems whose features were likely to enable
clinical predictions to shine. A half-century later, clinicians still operate at a decided
disadvantage in psychology (and to a slightly smaller extent, in medicine as well). There
are two main reasons for the enduring intractability of clinical prediction. First, we lack
well-corroborated, comprehensive nomothetic (let alone idiographic) theories of how the
Clinical Versus Statistical Prediction 1241
mind works, which allow accurate theory-mediated individual predictions. Second, the
cost of clinical judgments is a bigger issue than ever.
In contrast, the application of statistical prediction has grown, albeit slowly and
perhaps more outside of mainstream psychology than within it. First, actuarial MMPI
interpretation has been conspicuously successful since the 1960s. Second, the prediction
of criminal recidivism, one of the earliest applications, has likewise grown (e.g., Hanson
& Thornton, 2000). Third and finally, the use of automated decision rules and aids in
medicine has been adopted with moderate enthusiasm as one aspect of “Evidence Based
Medicine” (Elstein et al., 1996).
It remains important for applied psychologists in general and cognitive psychologists
in particular, not just clinical psychologists, to familiarize themselves with Meehl’s
thinking on the clinical versus statistical prediction debate. Although his writings are
peppered with references to philosophy of science and formal logic, they are quite accessible
to any competent student of psychology who will take the trouble to read them with
care. Until the day when a more exact, well-corroborated psychological theory of clinical
judgment becomes available, his analyses (and even his speculations) will remain valuable.
Unless and until the very unlikely happens, and a body of evidence emerges that
overturns the massive set of published studies favoring statistical prediction, his substantive
conclusions regarding the prima facie best approach to predicting human behavior
will stand indefinitely. The sheer intellectual pleasure to be had by reading Meehl’s uniquely
styled, engaging presentations of the fruits of his considerable intellect will, I am sure,
never dissipate.
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