Derner Institute of Advanced Psychological Studies,
Although Paul E. Meehl demonstrated the limits of informal aggregation
of data and prognostication by presumed experts, he remained convinced
that clinical experience confers expertise of some kind. The authors explore
this forgotten side of Meehl’s legacy by reconsidering the validity of clin-
ical judgment in its natural context, everyday clinical work. Three domains
central to clinical practice are examined: diagnosis, interpretation of mean-
ing, and intervention. It is argued that a more sanguine picture of clinical
expertise emerges when the focus shifts from prediction at high levels of
inference to (a) judgments at a moderate level of inference, (b) contexts for
which clinical training and experience are likely to confer expertise, and (c)
conditions that optimize the expression of that expertise (e.g., use of instru-
ments designed for expert observers). The authors conclude by examining
domains in which clinical judgment could prove useful in knowledge gen-
eration (e.g., hypothesis generation, identification of falsifying instances,
item development). © 2005 Wiley Periodicals, Inc. J Clin Psychol 61:
Keywords: Paul E. Meehl; clinical prediction; statistical prediction; clinical
judgment; clincial decision making; diagnosis
Few of us will live long enough, or write anything of sufficient profundity, to see our
work cited or assigned to graduate students 50 years later. Yet Meehl’s work from a
half-century ago remains central to the canon of our discipline. At the heart of this work
was his book on clinical and statistical prediction (Meehl, 1954/1996), in which he first
Correspondence concerning this article should be addressed to: Drew Westen, Department of Psychology,
Emory University, 532 Kilgo Circle, Atlanta, Georgia 30322; e-mail: firstname.lastname@example.org
JOURNAL OF CLINICAL PSYCHOLOGY, Vol. 61(10), 1257–1276 (2005)
Published online in Wiley InterScience (www.interscience.wiley.com). DOI: 10.1002/jclp.20181
© 2005 Wiley Periodicals, Inc.
demonstrated the relative superiority of actuarial to informal modes of aggregating data,
and his blistering critique of sloppy clinical thinking in “Why I Do Not Attend Case
Conferences” (Meehl, 1973). This one–two punch, combining a devastating quantitative
jab with a qualitative right hook, staggered the emerging field of clinical psychology,
and stands to this day as a testament to the rightful place of hubris among the deadly
sins. Psychologists have revisited the question of clinical versus statistical prediction
many times since Meehl’s book (e.g., Dawes, Faust, & Meehl, 1989; Holt, 1958; Sarbin,
1962; Sawyer, 1966), but the weight of the evidence remains the same as it was a half-
century ago: Those who believe they can “beat the odds” of a well-developed, well-
validated formula would do well to keep their wagers small (Grove, Zald, Lebow, Snitz,
& Nelson, 2000).
Meehl’s work on clinical–statistical prediction is often understood as a condemna-
tion of clinicians and their characteristic modes of thought and belief. However, from the
start, Meehl and his collaborators (Dawes et al., 1989; Grove & Meehl, 1996; Grove
et al., 2000) distinguished what they meant by clinical (an informal, subjective, nonquan-
titative mode of aggregating observations to make predictions) from its broader conno-
tation (pertaining to the judgments, inferences, observations, beliefs, or practices of
clinicians; Westen & Weinberger, 2004). In fact, Meehl was driven to write his book on
clinical–statistical prediction by what he described in its preface as a conflict confronting
anyone who practices both research and psychotherapy, between the subjective certainty
that clinical experience, like other forms of experience, surely must confer expertise, and
the disappointing findings on the reliability and validity of diagnostic judgments and
prognostications by purported experts.
Meehl argued persuasively that informal aggregation of data leaves clinicians (and
other experts) open to the same kinds of judgmental biases and heuristics subsequently
identified by Kahneman and Tversky (1973), Nisbett and Ross (1980), and others as
characteristic of everyday cognition.Yet he never abandoned his belief in clinical knowl-
edge, judgment, or expertise. For example, he patiently awaited data supporting clini-
cally based hypotheses about the pervasiveness, complexity, and patterning of unconscious
processes as he practiced psychoanalysis into his 80s (see Meehl, 1983). In Meehl’s own
[P]sychologists who visit Minneapolis for the first time and drop in for a chat with me gen-
erally show clinical signs of mild psychic shock when they find a couch in my office and a
picture of Sigmund Freud on the wall. Apparently one is not supposed to think or practice
psychoanalytically if he understands something about philosophy of science . . . [M]y local
psychonomic brethren find it odd that I should be seriously interested in the interpretation of
dreams. (1973, pp. 225–226)
Meehl had a strong distrust for clinical theories and research that did not reflect
immersion in clinical work and (referring to himself in the third person), “When he was
chairman of the psychology department he had a policy of not hiring faculty to teach
courses in the clinical and personality area unless they were practitioners and either had
the ABPP diploma or intended to get it” (p. 226).
Our goal in this article is to revisit this largely forgotten side of Meehl’s attitude
toward clinicians and the clinical enterprise, examining the circumstances under which
clinicians can make valid inferences. We are convinced, as was Meehl, that informal,
subjective prognostication is not the forté of clinicians, for precisely the reasons he and
others have elucidated: Optimal prediction requires a standard set of predictor variables
and regression weights iteratively selected and cross-validated across multiple data sets,
selected for their validity in predicting known outcomes, and aggregated statistically.
Journal of Clinical Psychology, October 2005
However, except in the courtroom (where prognostications of presumed experts can be
notoriously unreliable) and in the mass media (where clinicians with a passion for the
limelight and limited self-control often opine about the diapers of snipers), such prog-
nostications are not (and should not be) the stuff of everyday clinical practice and hence
may not be the decisive test of clinical judgment.
To put it another way, the clinical–statistical prediction debate in psychology gener-
ally assumes a particular goal of clinical observation: prediction of behavior.1(It has also
historically included psychiatric diagnosis, although, as we argue below, prognostication
and diagnosis may have very different properties vis-à-vis the clinical-statistical debate.)
In one sense, this is eminently reasonable, given that clinicians make predictions all
the time, at least implicitly, as when they choose a particular avenue for intervening
at a given point in a session with a particular patient. However, except in specific
medical–legal situations (predicting suicidality or homicidally) or subspecialties (e.g.,
forensics), clinical training is typically not devoted to prediction, and clinical experience
does not confer many benefits in predicting behavior, particularly without the kind of
systematic feedback that is essential for self-correction (and built into regression equa-
tions). Much of clinical training is devoted instead to what clinicians need to know to do
their work: how to diagnose personality and psychopathology, how to understand what
their patients are doing or saying (or not saying), and how to intervene to help alleviate
their patients’ problems.
In this article, we address the validity of clinical judgment in its natural context,
everyday clinical work, examining three domains: diagnosis, interpretation of meaning,
and intervention. We focus on clinical judgment at moderate levels of inference (e.g.,
whether a patient is rejection sensitive, irresponsible, remorseless, or has difficulty imag-
ining what other people feel) rather than on broad, unstructured prognostications (e.g.,
whether the person is likely to succeed in the army or to become manic at some point in
the future), because this is the level of inference most germane to everyday clinical work
and hence the most appropriate test of the validity of clinical judgment. Prognostications
at higher levels of inference inherently confound two variables: the nature of the observer
(clinician vs. lay) and the way the observer is trying to answer the question (statistically
or intuitively) (Westen & Weinberger, 2004). If we know that statistical aggregation is
generally superior to informal, subjective guesswork in predicting relatively broad or
distal outcomes, we will readily conclude that clinicians lack expertise if predicting such
outcomes is the measure of their expertise. If we want to see whether experienced prac-
titioners accrue knowledge by virtue of their training and experience, there we would do
better to focus on indices sensitive to the kind of expertise we might expect them to have
(and to discourage them from making the kinds of predictions neither experts nor lay-
people are likely to be able to make with any accuracy). We conclude by briefly revisiting
the question of what clinicians might be able to contribute to knowledge generation
(theory and research—that is, whether clinical experience might be not only clinically
but scientifically useful.
Clinical Judgment and Clinical Diagnosis
When Meehl (1954/1996) first penned his critique of clinical prediction, the scope of his
critique included clinical diagnosis, which had proven hopelessly unreliable. In retro-
spect, diagnosis using the DSM-I and DSM-II (Diagnostic and Statistical Manual of
1More broadly, “clinical prediction” in Meehl’s use of the term could include predictions made by other experts,
such as stock market forecasts by mutual fund managers.
In Praise of Clinical Judgment
Mental Disorders, first and second editions; American Psychiatric Association, 1952,
1968) could not have been otherwise. The first two editions of the DSM were coding
manuals without coding rules, supplying broad diagnostic categories with no specific
criteria or decision rules for adjudicating borderline cases. Like subsequent editions of
the DSM, these early editions of the diagnostic manual also asked clinicians to make
binary (present/absent) decisions about diagnostic variables (global diagnoses in DSM-I
through DSM-II, individual diagnostic criteria in DSM-III through DSM-IV) that are
more often than not continuously distributed in nature (see Westen & Shedler, 1999a;
Widiger & Clark, 2000).
With the advent of DSM-III (1980), replete with highly specific, operationalizable
diagnostic criteria, research surged ahead of practice in diagnostic reliability. Despite the
ubiquitous focus in clinical training on DSM (or International Classification of Diseases;
ICD) categories and criteria, clinicians still frequently do not know the criteria for par-
ticular disorders, do not use the diagnostic algorithms spelled out in the manual, and rely
only loosely on the manual to make diagnoses (Garb, 1998; Jampala, Sierles, & Taylor,
1988). These facts have led many researchers to conclude that clinicians should abandon
their preferred clinical interviewing and diagnostic practices in favor of structured research
interviews so that they can make proper diagnoses (e.g., Basco et al., 2000; Segal, Cor-
coran, & Coughlin, 2002).
That the use of structured interviews would improve reliability of diagnosis in every-
day practice is manifestly true. What is seldom recognized, however, is that this is true by
definition. To make a reliable DSM-IV diagnosis, one must make hundreds of highly
specific, often arbitrary decisions (one for each criterion for each disorder). This can only
be done by systematically inquiring about every sign and symptom in specific ways
required to decide whether the patient meets what are usually arbitrary cut-offs for “case-
ness” (e.g., whether the patient has binged and purged twice per week on average rather
than once per week). It is difficult to imagine how one could make even moderately
reliable diagnostic judgments using the diagnostic algorithms specified in the DSM-IV
without administering a structured interview.
The fine-grained distinctions required to obtain reliability using the DSM-IV may be
essential for researchers trying to identify homogeneous patient groups, but such distinc-
tions are arguably of little relevance to clinicians, for whom the nature and goals of
classification overlap with, but are not identical to, those of researchers. From a strictly
empirical perspective, we are aware of no evidence that patients who fall just below or
just above threshold for the categorical diagnosis of any DSM-IV diagnosis respond dif-
ferently to any form of treatment, have different etiologies, or differ in any other impor-
tant respect. The DSM-III, which first imposed the complex diagnostic decision rules
characteristic of subsequent editions of the manual, was a direct outgrowth of the Research
Diagnostic Criteria (RDC; Spitzer, Endicott, & Robins, 1978; emphasis added). The
purpose of the RDC was to operationalize diagnoses so that researchers could know, at
least by convention, that when they were studying patients with a particular diagnosis
(e.g., major depression) in one hospital they would likely obtain similar data in another
hospital. The hope was that this procedure would ultimately lead to better understanding
of psychiatric disorders and better treatment.
In this sense, the RDC and its descendants, DSM-III through DSM-IV, have been a
resounding success. However, from a clinical point of view, whether a patient with an
eating disorder purges (e.g., through self-induced vomiting) once a week, twice a week,
or sometimes once and sometimes twice is often of little consequence. Knowing that she
has been purging once or twice a week for the last 2 years is usually good enough, and
trying to pin her down on exactly how many times she has purged per week for a precise
number of months so that one can decide whether she “really” has bulimia nervosa is
Journal of Clinical Psychology, October 2005
arguably not a responsible use of clinical time. The more important diagnostic questions,
from a clinical standpoint, often center on issues about which DSM-IV diagnosis is silent,
such as the circumstances that elicit purging in this particular patient, the extent to which
the patient can control her tendency to purge, the extent to which she can take her purging
or her beliefs about her body as an object of thought (rather than assuming them to be
true), the extent to which her purging has become medically dangerous, the extent to
which it is related to other forms of impulse dysregulation to which she may be prone,
and so forth (see Westen & Bradley, 2005; Westen, Heim, Morrison, Patterson, & Camp-
To what extent clinicians can reliably answer the kinds of diagnostic questions that
are most useful in clinical practice is unknown.As a field, we have paid surprisingly little
empirical attention to identifying the kinds of information clinicians might find useful in
guiding interventions and in ways to optimize reliability and validity of those judgments.
However, an emerging body of evidence using quantified clinician-report measures,
designed using the same psychometric principles Meehl and others pioneered and per-
sonality and clinical researchers have applied successfully for 50 years to self-reports,
suggests that clinicians can answer many kinds of clinically meaningful diagnostic ques-
tions with considerable reliability and validity if given the means for quantifying their
observations (Dutra, Campbell, &Westen, 2004;Westen &Weinberger, 2004). For exam-
ple, clinicians can make highly reliable diagnostic judgments about complex personality
patterns using a 200-item Q-sort (e.g., Westen & Muderrisoglu, 2003; Westen & Shedler,
1999a, 1999b; Westen, Shedler, Durrett, Glass, & Martens, 2003). A Q-sort is a simple
ranking procedure whereby an observer, in this case a clinician, rank-orders a set of items
by sorting them into piles based on the extent to which they are descriptive of a target, in
this case, a patient (see Block, 1978). Interestingly, Meehl himself mused about such a
possibility: “It is also possible that interview-based judgments at a minimally inferential
level, if recorded in standard form (for example, Q-sort) and treated statistically, can be
made more powerful than such data treated impressionistically as is currently the prac-
tice” (Meehl, 1959, p. 124).
A Q-sort procedure might be useful in clinical practice when clinicians find them-
selves confronting a confusing diagnostic picture or when they must answer a precise,
clinically or socially important question, such as whether the patient is a high suicide risk
or a likely recidivist for a particular offense, for which researchers could develop empir-
ical prototypes or algorithms that could allow more accurate statistical prediction. Clini-
cians’ responses to Q-sort items written at a level likely to tap clinical expertise and
amenable to statistical aggregation could be a powerful tool in such situations.
In everyday clinical practice, however, clinicians may be able to make reasonably
reliable and valid diagnostic judgments at a moderate level of generality using a much
simpler procedure. Westen, Shedler, and colleagues have been experimenting with a sim-
ple prototype-matching approach to diagnosis of both Axis I and Axis II syndromes that,
for routine clinical purposes, might serve as a proxy for more precise Q-sort diagnoses
and might represent a compelling alternative to the complex decision rules embodied in
the DSM-IV (Westen & Bradley, 2005; Westen et al., 2002; Westen & Shedler, 2000).
Using this approach, the clinician compares the patient’s clinical presentation with a set
of paragraph-long syndrome descriptions and makes a 1–5 rating of degree of match to
each prototype, where a rating of 1 means “no match” and a rating of 5 means “proto-
typical case” (Figure 1). Rather than counting criteria assessed independently of one
another, the clinician’s task is to judge the goodness of fit between the prototype taken
as a whole, or as a gestalt, and the patient’s symptom picture. This approach has the
advantage of providing both continuous and categorical diagnostic judgments:Arating of
4 or 5 constitutes, for purposes of communication among clinicians and researchers, a
In Praise of Clinical Judgment
categorical diagnosis, and a rating of 3 denotes “features” of the disorder. For patients
who receive a rating of 3 or higher on a given diagnosis, the clinician would make
secondary ratings on such variables as age of onset and severity of symptom constella-
tions that have proven empirically predictive or clinically useful (e.g., depressed mood,
vegetative signs, suicidality) or that help distinguish genuinely taxonic from nontaxonic
cases (see Meehl, 1995a).
Westen and colleagues have now applied this approach in several studies and are
obtaining a consistent portrait of the reliability and validity of experienced doctoral-level
clinicians’diagnostic judgments when using a diagnostic approach that makes better use
of clinical judgment. Across a range of disorders, including personality, eating, mood,
and anxiety disorders, prototype diagnosis appears to perform as well or better in predic-
tion than application of DSM-IV diagnostic algorithms; reduces artifactual comorbidity;
and is rated by clinicians as substantially more clinically useful, relevant, and efficient.
In one set of studies (Westen, Shedler, & Bradley, 2004), clinicians rated the extent
to which a randomly selected patient in their care resembled single-paragraph prototype
descriptions of the Axis II Cluster B (dramatic, erratic) personality disorders (antisocial,
borderline, histrionic, and narcissistic) or prototypes of the same disorders derived empir-
ically using Q-factor analysis in a prior study. Clinicians also completed a checklist of all
the criteria for each of the DSM-IV Axis II disorders, which allowed the investigators to
generate both categorical diagnoses and dimensional diagnoses (number of criteria met
per disorder) for each disorder by using DSM-IV algorithms for diagnoses (e.g., presence
of five of nine criteria).
Both sets of prototypes yielded substantially reduced estimates of comorbidity as
well as higher ratings of clinical utility than diagnosis using DSM-IV decision rules.
Perhaps most striking, however, was that prototype diagnosis consistently performed as
well or better than both categorical and dimensional (number of criteria met) DSM-IV
diagnoses in predicting external criteria widely viewed as central to the validity of a
diagnostic system (see Robins & Guze, 1970), such as family history and adaptive
Patients who match this prototype tend to be deceitful, and tend to lie and mislead others. They take
advantage of others, have minimal investment in moral values, and appear to experience no remorse for
harm or injury caused to others. They tend to manipulate others’ emotions to get what they want; to be
unconcerned with the consequences of their actions, appearing to feel immune or invulnerable; and to
show reckless disregard for the rights, property, or safety of others. They have little empathy and seem
unable to understand or respond to others’ needs and feelings unless they coincide with their own.
Individuals who match this prototype tend to act impulsively, without regard for consequences; to be
unreliable and irresponsible (e.g., failing to meet work obligations or honor financial commitments); to
engage in unlawful or criminal behavior; and to abuse alcohol. They tend to be angry or hostile; to get
into power struggles; and to gain pleasure or satisfaction by being sadistic or aggressive toward others.
They tend to blame others for their own failures or shortcomings and believe that their problems are
caused entirely by external factors. They have little insight into their own motives, behavior, etc. They
may repeatedly convince others of their commitment to change but then revert to previous maladaptive
behavior, often convincing others that “this time is really different.”
Figure 1. Prototype description for empirically derived antisocial personality disorder.
Journal of Clinical Psychology, October 2005
functioning. These single-item ratings were slightly superior to DSM-IV diagnosis in
predicting efficacy of both psychotherapy and antidepressant medication. (In all cases,
the empirically derived prototypes outperformed all of the alternative diagnostic sys-
tems.) In data analyses just completed (in preparation), clinicians’ prototype ratings of
single-sentence summaries of each of the 10 personality disorders taken from the text of
the DSM-IV outperformed their own diagnostic judgments when adhering to DSM-IV
decision rules (evaluating each symptom and counting the number of criteria met for each
Similar findings have been obtained with prototype ratings of mood, anxiety, and
eating disorders, suggesting that the advantage of simple prototype ratings over complex
symptom-counting algorithms are not specific to personality disorder diagnosis (Westen,
Bradley, & Thompson-Brenner, 2004). Research just completed suggests that clinicians’
prototype ratings may not only be valid predictors of external criteria but may also be
made with substantial reliability in everyday practice. In a preliminary, small N study
(N ? 37), Westen, Bradley, and Hilsenroth (2005) asked advanced graduate student psy-
chotherapists to make prototype ratings of personality disorder diagnoses derived empir-
ically using Q-factor analysis (Westen & Shedler, 1999b) after their first 4 hours of
clinical contact with the patient. A second advanced graduate student then watched the
same 4 hours on videotape and made independent prototype ratings. Convergent validity
correlations (e.g., histrionic ratings made by the therapist and the second rater) ranged
from r ? .54 to .89, with a median of .69, suggesting substantial agreement using a
single-item measure applied to relatively unstructured (psychotherapy) data. Discrimi-
nant validity coefficients (e.g., the association between the therapist’s ratings of histri-
onic personality features and the second observer’s ratings of narcissistic features) hovered
around zero. Intraclass correlation coefficients were in the same range, suggesting that
clinicians could agree not only on the rank-ordering of patients on each prototype but on
the absolute magnitude of resemblance to each prototype.
These data are clearly preliminary, and they do not tell us whether less-experienced
clinicians could have done as well. However, taken together with the studies described
above (and with other studies suggesting the possibility of reliable prototype ratings of
this sort; e.g., Burisch, 1984; Elkin et al., 1995), they suggest that clinicians may be able
to make reliable diagnostic judgments, and that these judgments are predictive of a range
of variables supporting their validity across multiple samples and diagnostic classes.
Clinical Judgment and the Interpretation of Meaning
We turn now to a very different but central goal of clinical judgment, interpretive under-
standing. In a central tract on the philosophy of the social sciences, Max Weber (1949)
distinguished what he called “adequacy at the level of meaning” (interpretative under-
standing of the subjective meaning of an action to a person or group) and “adequacy at
the level of explanation” (what today we would call statistical prediction). He argued that
a science devoted to the study of a meaning-making species such as our own must achieve
both an understanding of the internal experience that leads people to do what they do,
which inherently involves interpretation, and causal explanation, which is most convinc-
ing when it is probabilistic and predictive. From Weber’s point of view, being able to
predict the relation between two variables without understanding the subjectivity of the
actor that mediates the relation is a useful step, just as being able to interpret the meaning
of a psychological event without being able to make any probabilistic statements is use-
ful, but each form of understanding is ultimately inadequate without the other.
In psychology, with our emphasis on significance testing and preferential tolerance
for Type II over Type I errors, we have tended to judge theories and methods only on the
In Praise of Clinical Judgment
basis of Weber’s second criterion. In many respects, this is sensible. An empirical disci-
pline with quantifiable variables, effect sizes, and confidence intervals that can be esti-
mated with some precision is an unwelcome host for the postmodern plague that has
infected much of the humanities, cultural anthropology, and some circles in psychoanaly-
sis. Disciplines for which hermeneutic exegesis of texts is a central component tend to be
vulnerable to a proliferation of alternative exegeses, none of which can claim any truth
value above the others, and hence to postmodern epistemological nihilism.
Although Meehl understood well the biases to which an interpretive mind is prone
(and the indeterminacy of interpretive understanding), we suspect he would not have
preferred a formula that could predict the number of first-person pronouns in Shakes-
peare’s King Lear from the number in Othello and Richard III to the thoughtful analysis
of a genuine expert on Shakespeare—unless of course, the latter was opining on the
number of pronouns in Lear. Developments in the neurosciences suggest why Meehl
never, in fact, jettisoned his belief in the value of interpretive understanding: Much of
who we are and what we do resides in implicit cognitive–affective–motivational net-
works whose meaning is inaccessible to introspection and can only be accessed indirectly
(Weinberger, in press; Westen, 1998).
Where networks are shared, researchers can observe their functioning using implicit
tasks that minimize interpretive activity. For example, to the extent that bird and robin are
associatively linked for most English speakers, we can reliably assess that linkage using
priming tasks with reaction-time as a dependent variable. Where associations are idio-
syncratic, however, as they are for everyone to some degree and particularly vis-à-vis
psychopathology (which is why the behavior appears “abnormal”), we need to identify
and chart the topography of networks that diverge from the ordinary—that is, to observe
the idiosyncratic rather than the shared networks of thought, feeling, and motivation that
regulate the person’s mental life and behavior (see Westen, 1998; Westen, 1999; Westen,
Feit, & Zittel, 1999). This, we suspect, is the reason for Meehl’s tenacious belief (Paul E.
Meehl, personal communication, May 2002) in the importance of eliciting patients’asso-
ciations in therapeutic work. We can certainly establish group differences using such
paradigms as emotional Stroop and lexical decision tasks (e.g., between depressed and
nondepressed individuals, or between snake phobics and spider phobics; see, e.g., Teach-
man, Gregg, & Woody, 2001), but to understand this particular depressed person, the
devil is in the details, and the details are often in associative links that take time and
expertise to identify.
To what extent particular kinds of clinical training and experience foster the ability
to “read” implicit associational networks (or, more broadly, to increase this aspect of
“emotional intelligence”) is an empirical question, but the fact that clinicians took the
existence of such networks as axiomatic and tried to develop strategies for understanding
and changing them a century before researchers did should give us pause before dismiss-
ing the interpretive activity of the clinician. Irrespective of the babble of (explicit) theo-
ries generated from clinical observation over the last century, from everything we know
about implicit procedural learning, it is difficult to imagine that over years of clinical
experience clinicians fail to encode some important regularities of their environment in
implicit “grammars” of interpretation.
We will never be able to eradicate the fallibility (or artistry) inherent in interpretive
understanding in psychotherapy, any more than we can eradicate it in musical perfor-
mance. But we can improve the probability of valid interpretive activity in the clinical
setting, in three ways. The first is to test and refine the theoretical frameworks that guide
interpretative activity (e.g., testing hypotheses about how associations work; about how
particular kinds of attachment experiences in childhood shape subsequent patterns of
Journal of Clinical Psychology, October 2005
thought, feeling, or interpersonal behavior; about how people regulate their emotions).
As Kurt Lewin (1951, p. 169) said, there is nothing as practical as a good theory.
The second is to assess the validity of aggregated variables (e.g., diagnostic judg-
specific inference. To put it another way, rather than assuming error-free clinical “items”
of interviewing practices used by experienced clinicians (Westen, 2003), experienced
even if they never ask patients if they are grandiose, entitled, readily enraged by feeling
slighted, and so forth (Westen & Muderrisoglu, 2003, in press). The interview requires an
experienced clinical interviewer to elicit narratives and observe the patient’s behavior.
What is striking about these findings is that clinicians can achieve high reliability across
cases even when the questions they ask vary from patient to patient as long as they use a
standard item set (e.g., a Q-Sort) to quantify and aggregate their inferences.
We do not believe, however, that clinicians only become capable of aggregating data
at this level of inference if given a particular item set. Rather, we suspect that good
clinicians practice a kind of “intuitive psychometrics” all the time: They discard infer-
ences about the meaning of an idiosyncratic word choice, or about an unusual interper-
sonal interaction, if similar phenomena do not emerge with some regularity. In other
words, they try to identify the central tendency in a sea of error and to assess internal
consistency of their observations using what one might think of as an “intuitive alpha,”
which indexes the extent to which they can have confidence in inferred symptoms or
personality attributes.2Of course, intuitive calculations of this sort can never be as accu-
rate as the more precise calculations necessary for research. However, by quantifying
clinicians’judgments using appropriate instruments, we can obtain more exact estimates
of reliability and correlate these quantified observations with external criteria (e.g., indi-
ces of adaptive functioning, pooled informant reports) to assess the validity of a given
clinician’s judgments or a set of interpretive procedures.
This leads to the third way that we can test and improve the validity of clinical
interpretive activity: by identifying those clinicians whose inferences, quantified reliably,
show the strongest, most predictable pattern of correlates. We can then apply an expert
systems approach to try to identify the procedures they are using, whether or not they
themselves have explicit access to these procedures, and to teach other clinicians how to
make similar inferences. We suspect that certain personality attributes are also predictive
of the capacity for interpretive accuracy and hence useful in selecting potential clinicians,
such as general (or perhaps verbal) intelligence, empathy, access to emotion, complexity
of mental representations of people and relationships, and openness to experience.
Clinical Judgment and Therapeutic Intervention
In the most general sense, the practices evolved by clinicians over the last century “work”:
The effect size first estimated by Smith and Glass (1977) for general psychotherapy
2Clinicians may even not be aware of doing so. Work on implicit learning (e.g., Lewicki, 1986; Weinberger, in
press) indicates that adults and children extract such central tendencies all the time in complex social situations.
It would be surprising if practicing clinicians were inferior to 5-year-old children in this capacity. Indeed, as
Goldberg (1991) has shown, one can often derive from clinicians’judgments regression equations that capture
many of the rules they are using to make these judgments and then outperform the same clinicians by applying
these equations without error to new cases.
In Praise of Clinical Judgment
effectiveness as compared with control conditions (roughly .85 in SD units) has stood the
test of time and compares favorably to many other medical procedures (see Meyer et al.,
2001; Wampold, 2001). This effect size is within the range (and generally in the middle
of the confidence intervals) of effects obtained in randomized controlled trials (RCTs) for
many disorders (see Westen, Novotny, & Thompson-Brenner, 2004).
The extent to which clinicians should rely on statistical algorithms rather than clin-
ical judgment in selecting interventions with a given patient is the latest incarnation of
the clinical–statistical debate and probably the most hotly contested version of that debate
since the firestorm set off by Meehl’s (in his words) “disturbing little book” written in
1954 (Meehl, 1954/1996).Advocates of the empirically supported therapies (EST) move-
ment argue that we now have enough data to distinguish empirically supported from
unsupported therapies for the most prevalent DSM-IV disorders (at least those coded on
Axis I), and that clinicians should therefore limit their interventions to those on the EST
list (Chambless & Ollendick, 2000). The EST movement has had a substantial impact on
clinical training and practice, with many institutions now instructing doctoral students,
interns, and postdoctoral fellows exclusively in techniques that have passed muster in
controlled clinical trials or even in the implementation of the specific manuals used in
these studies. Declarations of “treatment of choice” are common in the literature, with
many suggesting that clinicians who do not follow these guidelines are providing poor
care or perhaps even behaving unethically.
No one cognizant of the clinical–statistical debate (and of the cornucopia of fringe
therapies available to an unwitting public) can doubt the importance of applying quanti-
tative methods to treatment decisions in mental health (or any other health discipline).
One can, however, question whether the EST movement represents the “statistical” side
of the clinical–statistical debate as well as many of its advocates claim. Critics have
raised a number of objections, the most important on empirical grounds. We will not
attempt to adjudicate any of these issues here, but will simply present them in bulleted
• A positive therapeutic alliance and other common factors (mechanisms of thera-
peutic action common to virtually all therapies) tend to account for substantially
more variance in outcome than specific treatment effects for most disorders stud-
ied (see Lambert & Bergin, 1994; Weinberger, 1995).
• Meta-analytic data consistently find that comparisons of two or more active treat-
ments tend to produce modest effect sizes (absolute value around d ? .20),
particularly when both treatments are bona fide treatments (rather than pseudo-
treatments designed as sparring partners for “real” contenders; see Luborsky,
Barton, & Luborsky, 1975; Luborsky et al., 2002; Wampold et al., 1997).
• Much of the variance in outcome widely attributed to specific treatment effects can
be accounted for by allegiance effects, such that the treatment preferred by the
investigator in a given study virtually always “wins” (Luborsky et al., 1999).3
• Most studies in the EST literature have applied extensive and idiosyncratic screen-
ing criteria that excluded many or most patients who presented with the symptom
3One might legitimately question whether some part of this variance accounted for by investigator allegiance
can in fact, be attributed to investigators developing allegiances to treatments they have observed to work.
However, empirically, one can list on the fingers of one hand the number of treatment researchers who have
fundamentally changed their treatment orientation based on the results of their own clinical trials. Interestingly,
we can think of many more clinicians who have fundamentally changed their views based on the data of clinical
observation, such as Aaron T. Beck and Albert Ellis, who developed cognitive approaches to psychotherapy
based on their clinical observation as psychoanalysts.
Journal of Clinical Psychology, October 2005
or syndrome under investigation, rendering generalizability uncertain (Westen &
• Researchers have systematically avoided comparing experimental treatments with
treatments widely used in the community (or treatments provided by clinicians
identified empirically as those who obtain the best outcomes on average or clini-
cians nominated by their peers as experts), so that we do not know whether ESTs,
which generally lead to improvement and recovery rates of 20 to 50 percent, are
superior to outcomes in clinical practice (Westen, Novotny, et al., 2004, 2005).
From the point of view of the clinical–statistical debate, four points are of note here.
First, given the lack of consensus in the literature, and the strong empirical arguments on
both sides of the EST debate, the decision to use a formula in a given clinical instance
to select an intervention is as “clinical” in Meehl’s sense of the term (informal, subjec-
tive) as the decision to reject it. For example, EST researchers have come to the consen-
sus that if a patient presents with depression, the appropriate psychosocial treatment is
16 sessions of cognitive or interpersonal therapy (Hollon, Thase, & Markowitz, 2002).
Yet the average study of ESTs for depression has excluded over two thirds of the
patients who presented for treatment, including those with suicidal ideation, substance
abuse, and a range of other common features and comorbid conditions (Westen & Mor-
rison, 2001). So how does a clinician decide whether this body of literature applies to this
An EST advocate would suggest that, because some data are better than no data,
clinicians should start with what has been validated and figure out what to do next if none
of the extant ESTs works. Yet the available data suggest that the majority of carefully
selected patients who undergo 16 sessions of cognitive or interpersonal therapy for depres-
sion (the treatment length prescribed in the manuals) administered by highly trained and
supervised therapists in clinical trials fails to improve, remains symptomatic at termina-
tion, and relapses or seeks further treatment within 18 months (Westen & Morrison,
2001). In light of these dismal outcome statistics, and the fact that no one has ever
compared these treatments with treatment in the community by expert practitioners, the
assertion that clinicians should start with one of these manuals seems to us a “clinical”
judgment with a low probability. It is unfortunate that researchers made the collective
decision over the last 20 years to study only brief trials of only two treatments for a subset
of poorly specified depressed patients and to avoid comparing them with treatments
provided by experienced practitioners, because doing so has rendered the question of
how to treat any given depressed patient in practice largely a matter of faith and opinion.
Second, advocates of ESTs often liken the choice of using versus not using an EST to
statistical versus clinical prediction (e.g., Wilson, 1998), with the former relying on rep-
licable research and the latter reflecting clinical opinion. However, one of the conditions
Meehl (1954/1996) outlined in which statistical prediction will not outperform intuitive
judgments by presumed experts is when a formula would be premature because of inad-
equate knowledge of relevant variables. To date, researchers have tested a very limited
subset of possible interventions, namely those most congenial to brief treatments and to
investigators whose theoretical meta-assumptions led them to believe (unlike Meehl) that
psychopathology is highly malleable, distinct from personality, and hence likely to respond
to brief treatments (Westen, Novotny, et al., 2004). Thus, a typical formula would include
only three or four dichotomous variables (presence or absence of exposure, other tech-
niques aimed at behavior change, cognitive restructuring, and interpersonal interven-
tions), which only occasionally predict differences in treatment response.
An alternative strategy, truer to the spirit of Meehl’s argument and the research
literature on statistical prediction, would extend the range of scientific method to the
In Praise of Clinical Judgment
selection of interventions to test, measuring outcome and interventions strategies in large
samples of patients treated in the community (as well as in the laboratory). Using an
instrument with a sufficient number of intervention variables (e.g., the Psychotherapy
Process Q-set; Ablon & Jones, 2002), one could then identify variables that predict pos-
itive outcomes for patients sharing a common problem (e.g., clinically significant
depression) at clinically meaningful follow-up intervals. Researchers could use these
findings to develop treatment protocols empirically and then subject them to experimen-
tal investigation. Using clinical practice as a natural laboratory in this way would trans-
form the large variability of intervention strategies in the community from a source of
realistic concern to a source of hypotheses and statistical knowledge linking interventions
Athird point worth noting regarding the applicability of the clinical–statistical debate
to the EST debate pertains to the “clinical” nature of research decisions that have shaped
psychotherapy research over the past two decades. Until the last decade, psychotherapy
researchers considered the manipulation used in a given study to be one among a large
number of possible ways to operationalize a principle or technique (e.g., exposure). As
in most experiments, the particular manipulation chosen represented a sample of a broader
population of possible operationalizations of a construct. In the EST era, however, man-
uals are viewed as defining treatments, not exemplifying them (see Westen, Novotny,
et al., 2004). Clinicians are then exhorted to use the manual as written, not to draw
inferences about general principles that might be applied in different ways to different
patients or problems (see Beutler, 2000; Rosen & Davison, 2003). Often this exhorta-
tion includes the warning that clinicians should fight the impulse to choose from differ-
ent manuals or improvise around a manual to fit a given patient, given that the clinical–
statistical prediction literature has shown that such clinical judgments are generally
In fact, however, researchers generally solidify the interventions embodied in treat-
ment manuals long before testing them, using precisely the kinds of intuitive, informal
processes Meehl termed clinical. That is, they use their best hunches to decide what
interventions to include, how to operationalize them, how long treatment should last, and
so forth, before ever conducting their first controlled trial. Only rarely do manuals undergo
much significant change after their first successful clinical trial because no one wants to
alter the “formula” that produced success, and the data often do not allow the researcher
to identify which of many interventions that constitute the “package” (delivered in only
one of multiple possible orders) were responsible for the obtained outcomes. Whether the
empirically tested clinical hunches of a handful of like-minded researchers are better than
the untested clinical hunches of several thousand experienced full-time clinicians is
unknown. Personally, we would bet on reliability theory that the aggregate outcome of a
thousand clinicians will outperform the aggregate outcome of treatments devised by a
small number of researchers,4except where the researchers made creative use of basic
science research unknown to most clinicians to generate a truly novel clinical innovation
(e.g., Barlow’s Panic Control Therapy; Barlow, 2002).5This is particularly the case given
that researchers have generally imposed on themselves one of the same handicaps that
severely limits clinical prediction, namely the lack of self-correcting feedback, in their
failure to follow up their samples at intervals (e.g., 2 or 3 years) appropriate for disorders
that are often slow to change or recurrent by nature.
4This is assuming, of course, that their errors are, if not randomly distributed, at least not correlated extremely
highly. Given the multitude of theories guiding even clinicians who share a theoretical orientation, we suspect
this assumption is reasonable enough.
5Fortunately, there is no need to bet; this is an empirical question that could be readily tested.
Journal of Clinical Psychology, October 2005
That the advantage of laboratory-generated treatments based on creative application
of basic science may largely emerge only when researchers do something novel—that is,
when they do not follow a formula—leads us to a paradox, because, as we have argued
elsewhere (Westen & Weinberger, 2004), the advantage of statistical over informal, sub-
jective decisions applies as much to experienced researchers as to experienced practition-
ers (who are both clinicians in Meehl’s terms, i.e., purported experts). Meehl mercilessly
attacked the foibles of clinicians, but we suspect he could have equally focused on the
foibles of researchers. Indeed, if we were to apply the widely believed take-home mes-
sage of the clinical–statistical debate (and the EST movement) to research, we would
straightjacket researchers, requiring them to avoid creative application of scientific method
in any given study in favor of manipulations or measures shown in prior research to be
successful, given that any given hunch about why “this study is different” is vulnerable to
all the biases involved when a clinician imagines that “this case is different.” Unfortu-
nately, there is no statistical algorithm for determining when to abandon a given algo-
rithm or search for new ones. Had Einstein accepted formulas that had worked reasonably
well for over a century, we would still be Newtonians.And we would argue, as suggested
above, that the rote application of a set of methodological choices believed by researchers
to have “worked” in psychotherapy research (and the enforcement of such choices through
restriction of the kinds of studies that could obtain funding) has set back scientific knowl-
edge about effective treatments for disorders such as depression by decades.
Conclusions: The Role of Clinical Judgment in Knowledge Generation
We have focused in this article on what clinicians may be able to do in everyday practice
and have suggested that if we shift our focus from prediction at high levels of inference
to (a) judgments at a moderate level of inference, (b) contexts in which clinicians are
likely to develop expertise (diagnosis, interpretation of meaning, and intervention), and
(c) conditions that optimize the expression of that expertise (e.g., use of psychometric
instruments designed for expert observers), we may begin to see why Meehl never aban-
doned his belief in clinical expertise despite its vulnerabilities to all manner of mental
shenanigans. We have suggested, in fact, that Meehl could not abandon the uncertainties
of clinical judgment in the consulting room for the same reason researchers cannot aban-
don the uncertainties of “clinical” (i.e., expert, informal, subjective) judgment in the
laboratory: Truth does not reveal itself without interpretation. The choice of what hypoth-
eses to pursue, using what methods, is inherently a clinical decision, however informed
(as it should be informed) by the available quantitative evidence. In this sense, the clinical–
statistical debate is a particular incarnation of a central question of epistemology: how an
imperfect mind can distinguish with any probability its own workings from the object of
its investigations (see Meehl, 1983). Meehl’s tentative solution, as an empiricist as well
as an admirer of both Sigmund Freud and Albert Ellis, was to recommend that we stay
abreast of the available data while remaining vigilant to both the emotional and cognitive
biases to which human minds, including clinical minds, are prone.
We cannot conclude, however, without addressing one last context in which clini-
cians have laid claim to expertise: in generating psychological knowledge (see also Meehl,
1967,6on theory mediation). A century ago, Freud derived a theory of personality, psy-
chopathology, and treatment largely from a clinical observation, and many approaches to
psychotherapy today remain moored primarily in clinical judgment. Our goal in these
6This article was originally reprinted in Meehl, P.E. (1973). Psychodiagnosis: Selected papers (pp. 165–173).
Minneapolis: University of Minnesota Press. The book itself was reprinted as Meehl, P.E. (1977). Psychodiag-
nosis: Selected papers. New York: Norton.
In Praise of Clinical Judgment
final pages is not to revive unbridled clinical theory-building, but to suggest several ways
clinical observation may indeed have a place at the scientific table. We focus on six
contexts in which clinicians may contribute to psychological knowledge: hypothesis gen-
eration, coherence testing, relevance testing, identification of disconfirming instances,
item generation, and quantified observation. We cannot describe any of these in detail but
will simply lay out some of the relevant issues.
The first way clinicians may contribute to psychological science is through hypoth-
esis generation. It seems to us highly unlikely that people bright enough to get into highly
competitive doctoral programs in clinical psychology learn nothing of consequence from
their clinical training and develop nothing but self-sustaining biases from mucking around
in the minds of other people for months or years at a time. Empirically, perhaps the best
evidence is the fact that clinicians assumed the pervasiveness and significance of uncon-
scious processes a century before researchers grudgingly admitted their existence; wrote
about the complexity and importance of mental representations of the self and others in
ing the schema concept to self-representations; Sandler & Rosenblatt, 1962; Westen,
1992); and understood that attitudes can be complex, ambivalent (associated with multi-
ple affects, and not just positive or negative valence), and primed outside of awareness
long before researchers who spent their lives studying attitudes did (Westen, 1985).
No doubt clinicians of every theoretical persuasion engage their patients in what
could be described from one point of view as shaping and from another as a folie à deux,
in which clinicians selectively reinforce their patients for accepting the wisdom of their
theoretical biases. This surely limits what both members of the therapeutic dyad learn
from clinical hours, just as researchers’ tendency to test only hypotheses they believe to
be true at a subjective probability of, say, p ? .05, limits what they learn, and it certainly
sets severe constraints on the clinic as a venue for hypothesis testing. (Personally, we
keep waiting for the good fortune of encountering one of those patients, widely presumed
to be ubiquitous, who are so pliable, and whose pocketbooks so plentiful, that they believe
everything we tell them and are willing to stick around for the duration of the loans on our
BMWs to explore the vagaries of their Oedipus complex.) Vis-à-vis hypothesis genera-
tion, however, it is hard to imagine a better perch for observation than clinical practice
(see Meehl, 1995b). And empirically, most important constructs in clinical psychology
and psychiatry had their roots in clinical immersion (e.g., major depression, schizophre-
nia, anorexia nervosa, personality disorders, cognitive therapy).
The second way clinicians may contribute to psychological science is through what
might be called coherence testing. The philosopher and cognitive scientist Paul Thagard
(2000) has used the term “explanatory coherence” to describe the way people (including
scientists) equilibrate to judgments or solutions to problems that maximize goodness of
fit with the totality of cognitive constraints on what they might believe. The “hardest”
constraints in science are hard data (e.g., the presence of certain findings in methodolog-
ically strong studies), but other constraints include less-definitive data (e.g., from case
studies, or from correlational studies that do not definitively establish causation) and
webs of related observations and hypotheses that make more or less sense in light of one
or another potential solution to the problem at hand. Thagard has developed computa-
tional models that successfully simulate both everyday and scientific judgment using this
approach, derived from connectionist models in cognitive science.
With respect to explanatory coherence, clinical observation, particularly when cou-
pled with knowledge of relevant scientific literatures (e.g., basic science on emotion), has
the strong advantage of providing a contextual “forest for the trees.” For example, during
the behaviorist era, most clinicians rejected out of hand the metatheoretical assumption
Journal of Clinical Psychology, October 2005
that thoughts and emotions are irrelevant or epiphenomenal because this principle had
minimal explanatory coherence in the context of all they observed in the consulting
room. Researchers, in contrast, could draw only on their everyday experiences to provide
a broader context (or counterweight) for judging the viability of the hypotheses they were
testing in the laboratory and correspondingly took 50 years to recognize the limitations of
Or consider the cognitive revolution that followed the behavioral one in psychology.
For 30 years, researchers pursued a serial-processing approach to memory and problem
solving (i.e., a model positing that mental contents are processed one at a time in short-
term memory) that largely ignored the role of emotion in both driving and distorting
decision making. Although researchers have jettisoned pure serial processing models,
and have expended considerable energy studying cognitive biases that can affect reason-
ing, the virtual absence of the word “affect” from the most recent reviews of the litera-
tures on cognition, judgment, and decision making in the Annual Review of Psychology
(e.g., Hastie, 2001) is a striking omission. Most clinicians would find most contemporary
decision-making models uncompelling despite the strong empirical evidence supporting
them, because such models would not allow them to generate reasonable hypotheses with
explanatory coherence for the most basic clinical phenomena (e.g., how people choose
whether to stay in relationships about which they are conflicted, how they recount and
shake one’s finger in consternation at clinicians for not reading the Annual Review of
Psychology, we would suggest, equally, that researchers who want to understand decision
making might gain something from talking to people who study it in real time, in real life,
40 hours a week.
A third and related context in which clinicians might contribute to psychological
knowledge is through what might be called relevance testing. We suspect that many
treatment researchers could have gained substantially from talking with, rather than deval-
uing, clinicians over the last 20 years. Although part of the reason clinicians have been
equal blame can be laid at the doorstep of researchers, who never bothered to ask clini-
cians basic questions that might have been of use to them, such as what problems their
patients actually bring to treatment, whether most patients meet criteria for a DSM-IV
Axis I disorder, whether their patients tend to have multiple problems rather than a single
disorder, how long it generally takes to treat various disorders successfully, and so forth.
This could have been done quantitatively, by asking clinicians to describe, for example,
their most recently terminated patient of a certain sort (e.g., a patient who presented with
depression as an initial complaint), to minimize biases in sampling or reporting (see, e.g.,
Morrison, Bradley, & Westen, 2003; Thompson-Brenner & Westen, in press-a,b). The
failure to do so has led to treatments that many clinicians consider of little relevance for
most of their patients (see Westen, Novotny, et al., 2004).
A fourth role of clinicians in knowledge generation is the identification of discon-
firming instances. As Hume noted years ago, all knowledge is probabilistic, and a single
disconfirming case can provide extremely useful information for the refinement or dis-
confirmation of hypotheses. Hume noted how observation of a single black swan could
shatter a compelling probabilistic hypothesis that all swans are white even after observ-
ing 100 consecutive white swans. As one of us observed in the heyday of the attribu-
tional reformulation of the helplessness theory of depression (Westen, 1985, 1991),
depressed narcissists (e.g., middle-aged narcissists coming to grips with the reality that
their grandiose dreams will never come true) are the “black swans” of learned helpless-
ness theories. Treatment barely begins with narcissistic patients until they start to attribute
In Praise of Clinical Judgment
the causes of their misfortunes to their own stable traits, rather than blaming their dif-
ficulties on others.
Afifth context in which clinicians can contribute to knowledge generation is through
item generation.7Just as clinical observation can be a wonderful vista from which to
frame hypotheses, it can also be a useful vantage point for generating items for measures
Revised (PCL-R; Hare, 2003). Not only the construct of psychopathy, but the items from
the PCL-R were derived directly from the work of Cleckley (1941) based on his immer-
sion in unstructured clinical observation of psychopaths. The same is true of many widely
used instruments, such as the Beck Depression Inventory (Beck et al., 1961). By defini-
tion, the more one structures the context (as in an experiment) or the response options of
respondents (as in a questionnaire), the less one can learn about things one did not already
believe to be important or true (see Westen, 1988; Westen & Gabbard, 1999). Conversely,
the less one structures the situation (as in immersion in clinical hours), the less one can
conclude about causation or even patterns of covariation (as in the subsequent empirical
finding, which could not have been readily known by Cleckley, that psychopathy is a
multifactorial construct). This is precisely why clinical observation can be useful in the
context of scientific discovery but much less useful in the context of scientific justifica-
tion (hypothesis testing).8
A final way clinicians may contribute to psychological knowledge is as informants,
through quantified observation. We will not belabor the point, which we have made
extensively elsewhere (e.g., Westen & Shedler, 1999a), but in relying primarily on the
self-reports of undergraduates, psychiatric patients, and other lay informants, as a field
we may have ignored one of the most useful sources of information about patients’
psychopathology—experienced clinicians who know them well. Ironically, part of the
reluctance to quantify the observations of experienced clinical observers using psycho-
metric procedures that have proven so useful in quantifying the observations of lay
informants reflects a misunderstanding of the clinical–statistical debate, most impor-
tantly a confusion of the nature of the informant (clinician vs. lay self-report) with a
method of aggregating data (subjective vs. statistical) (Westen & Weinberger, 2004).
These two variables—informant and method of aggregation—constitute orthogonal axes,
each of which has “clinical” at one pole; this has led, we believe, to considerable con-
fusion. As we have tried to show, clinicians do appear to be able to make reliable and
valid judgments at moderate levels of inference if given appropriate methods of quan-
tifying their judgments.
The passing of one of the brightest lights ever to shine (and, if the reader will excuse
a clinical prediction, ever likely to shine) on our profession seems an appropriate time to
rethink the question of what clinicians should and should not be able to do. Our goal in
this article was not to excuse clinicians for their failure to heed Meehl’s warnings about
the limits of clinical judgment, which they do at their own peril and that of their patients.
Nor was it to pillory researchers for falling prey to many of the same biases (e.g., con-
firmation biases), and displaying much of the same hubris that is widely attributed to
clinicians.We suspect that on the bell curves of foolishness and narcissism, clinicians and
researchers probably show relatively similar means and dispersions (although this is
7Meehl himself believed in the importance of clinical immersion for item generation. When one of us (D.W.)
once wrote him to ask for his comments on a draft of a clinician-report instrument designed to assess subtle
forms of subpsychotic thought disorder, he responded, after reading the items, that the item content could only
have been generated by a seasoned clinician. (We believe he meant this in a positive light, but that, of course,
is a clinical judgment.)
8As Meehl put it, “The clear message of history is that the anecdotal method delivers both wheat and chaff, but
it does not enable us to tell which is which” (1995b, p. 1019).
Journal of Clinical Psychology, October 2005
an empirical question). Rather, our goal has been to resurrect the less-studied pole of
Meehl’s conflict about research and practice. If, after 50 years of research, we have
largely failed to identify manifestations of expertise in the only domain ever studied in
which experience appears to lead to the accretion of little more than bias and error,
the flaw may lie not only in the mental habits of clinical practitioners but in our own
biases or lack of creativity as practitioners of scientific method.
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