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Piaget worked out his logical theory of cognitive development,
Köhler the Gestalt laws of perception, Pavlov the principles of
classical conditioning, Skinner those of operant conditioning, and Bartlett
his theory of remembering and schemata  all without rejecting
null hypotheses. But, by the time I took my first course in psychology
at the University of Munich in 1969, null hypothesis tests were presented
as the indispensable tool, as the sine qua non of scientific
research. PostWorld War 2 German psychology mimicked a revolution of
research practice that had occurred between 1940 and 1955 in American
psychology.
What I learned in my courses and textbooks about the logic of scientific
inference was not without a touch of morality, a scientific version
of the 10 commandments: Thou shalt not draw inferences from a nonsignificant
result. Thou shalt always specify the level of significance before the
experiment; those who specify it afterward (by rounding up obtained
p values) are cheating. Thou shalt always design thy experiments so
that thou canst perform significance testing.
The Inference Revolution
What happened between the time of Piaget, Köhler, Pavlov, Skinner,
and Bartlett and the time I was trained? In Kendall's (1942) words,
statisticians "have already overrun every branch of science with
a rapidity of conquest rivalled only by Attila, Mohammed, and the Colorado
beetle" (p. 69).
What has been termed the probabilistic revolution in science
(Gigerenzer etal., 1989; Krüger, Daston, & Heidelberger, 1987;
Krüger, Gigerenzer, & Morgan, 1987) reveals how profoundly
our understanding of nature changed when concepts such as chance and
probability were introduced as fundamental theoretical concepts. The
work of Mendel in genetics, that of Maxwell and Boltzmann on statistical
mechanics, and the quantum mechanics of Schrödinger and Heisenberg
that built indeterminism into its very model of nature are key examples
of that revolution in thought.
Psychology did not resist the probabilistic revolution, and psychologists
in turn actively contributed to the growth of statistics. But psychology
is nonetheless a peculiar case. In psychology and in other social sciences,
probability and statistics were typically not used to revise the understanding
of our subject matter from a deterministic to some probabilistic
view (as in physics, genetics, or evolutionary biology), but rather
to mechanize the experimenters' inferences  in particular,
their inferences from data to hypothesis. Of course, there have been
several attempts to revise our theories as wellfor example, to transform
Piaget's logical determinism into a more Darwinian view, where variability
and irregularity are seen as the motor of evolution rather than as an
annoyance (Gruber, 1977; Gruber & Vonèche, 1977), or to transform
Skinner's theory into a probabilistic learning theory (Estes, 1959).
But the real, enduring transformation came with statistical inference,
which became institutionalized and used in a dogmatic and mechanized
way. This use of statistical theory contrasts sharply with physics,
where statistics and probability are indispensable in theories about
nature, whereas mechanized statistical inference such as null hypothesis
testing is almost unknown.
So what happened with psychology? David Murray and I described the striking
change in research practice and named it the inference revolution
in psychology (Gigerenzer & Murray, 1987). It happened between approximately
1940 and 1955 in the United States, and led to the institutionalization
of one brand of inferential statistics as the method of scientific
inference in university curricula, textbooks, and the editorials of
major journals.[1]
The figures are telling. Before 1940, null hypothesis testing using
analysis of variance or t test was practically nonexistent: Rucci and
Tweney (1980) found only 17 articles in all from 1934 through 1940.
By 1955, more than 80% of the empirical articles in four leading journals
used null hypothesis testing (Sterling, 1959). Today, the figure is
close to 100%. By the early 1950s, half of the psychology departments
in leading U.S. universities had made inferential statistics a graduate
program requirement (Rucci & Tweney, 1980). Editors and experimenters
began to measure the quality of research by the level of significance
obtained. For instance, in 1962, the editor of the Journal of Experimental
Psychology, A. W. Melton (1962, pp. 553554), stated his criteria
for accepting articles. In brief, if the null hypothesis was rejected
at the .05 level but not at the .01 level, there was a "strong
reluctance" to publish the results, whereas findings significant
at the .01 level deserved a place in the journal. The Publication
Manual of the American Psychological Association (1974) prescribed
how to report the results of significance tests (but did not mention
other statistical methods), and used, as Melton did, the label negative
results synonymously with "not having rejected the null" and
the label positive results with "having rejected the null."
It is likely that Piaget's, Köhler's, Bartlett's, Pavlov's, and
Skinner's experimental work would have been rejected under such editorial
policies  these men did not set up null hypotheses and try to
refute them. Some of them were actively hostile toward institutionalized
statistics. For his part, Skinner (1972) disliked the intimate link
Fisher established between statistics and the design of experiments:
"What the statistician means by the design of experiments is design
which yields the kind of data to which his techniques are applicable"
(p. 122). And, "They have taught statistics in lieu of scientific
method" (p. 319). Skinner continued to investigate one or a few
pigeons under wellcontrolled conditions, rather than run 20 or more
pigeons under necessarily less wellcontrolled conditions to obtain
a precise estimate for the error variance. In fact, the Skinnerians
were forced to found a new journal, the Journal of the Experimental
Analysis of Behavior, in order to publish their kind of experiments
(Skinner, 1984, p. 138). Their focus was on experimental control, that
is, on minimizing error beforehand, rather than on large samples, that
is, on measuring error after the fact.
This is not an isolated case, nor one peculiar to behaviorists. The
Journal of Mathematical Psychology is another. One of the reasons
for launching this new journal was again to escape the editors' pressure
to perform institutionalized null hypothesis testing.[2]
One of its founders, Luce (1988), called the institutionalized practice
a "wrongheaded view about what constituted scientific progress"
and "mindless hypothesis testing in lieu of doing good research:
measuring effects, constructing substantive theories of some depth,
and developing probability models and statistical procedures suited
to these theories" (p. 582).
Who is to blame for the present state of mindless hypothesis testing?
Fisher was blamed by Skinner, as well as by Meehl: "Sir Ronald
has befuddled us, mesmerized us, and led us down the primrose path.
I believe that the almost universal reliance on merely refuting the
null hypothesis ... is ... one of the worst things [that] ever happened
in the history of psychology" (Meehl, 1978, p. 817).
I share the sentiments expressed by Luce and Mechl. But to blame Fisher,
as Meehl and Skinner did, gives us at best a spurious understanding
of the inference revolution. Fisher declared that a significance test
of a null hypothesis is only a "weak" argument. That is, it
is applicable only in those cases where we have very little knowledge
or none at all. For Fisher, significance testing was the most primitive
type of argument in a hierarchy of possible statistical analyses (see
Gigerenzer et al., 1989, chap. 3). In this chapter I argue the following
points:
1. What has become institutionalized as inferential statistics
in psychology is not Fisherian statistics. It is an incoherent mishmash
of some of Fisher's ideas on one hand, and some of the ideas of Neyman
and E. S. Pearson on the other. I refer to this blend as the "hybrid
logic" of statistical inference. Fisher, Neyman, and Pearson would
all have rejected it, although for different reasons.
2. The institutionalized hybrid carries the message that statistics
is statistics is statistics, that is, that statistics is a single
integrated structure that speaks with a single authoritative voice.
This entails the claim that the problem of inductive inference in fact
has an algorithmic answer (i.e., the hybrid logic) that works
for all contents and contexts. Both claims are wrong, and it is time
to go beyond this institutionalized illusion. We must write new textbooks
and change editorial practices. Students and researchers should be exposed
to different approaches (not one) to inductive inference, and be trained
to use these in a constructive (not mechanical) way. A free market of
several good ideas is better than a state monopoly for a single confused
idea.
3. Statistical tools tend to turn into theories of mind. We can find
the dogma "statistics is statistics is statistics" reappearing
in one of the most interesting research areas in cognitive psychology:
intuitive statistics and judgments under uncertainty. One statistical
theory is confused with rational inductive inference per se.
The"Parents" and Their Conflicts
In order to understand the structure of the hybrid logic that has
been taught in psychology for some 40 years, I briefly sketch those
ideas of Fisher, on the one hand, and Neyman and Pearson on the other,
that are relevant to understanding the hybrid structure of the logic
of inference.
Fisher's first book, Statistical Methods for Research Workers,
published in 1925, was successful in introducing biologists and agronomists
to the new techniques. It had the agricultural smell of issues like
the weight of pigs and the effect of manure, and, such alien topics
aside, it was technically far too difficult to be understood by most
psychologists.
Fisher's second statistical book, The Design of Experiments,
first published in 1935, was most influential on psychology. At the
very beginning of this book, Fisher rejected the theory of inverse probability
(Bayesian theory) and congratulated the Reverend Bayes for having been
so critical of his own theory as to withhold it from publication (Bayes'
treatise was published posthumously in 1763). Bayes' theorem is attractive
for researchers because it allows one to calculate the probability P(H
D) of a hypothesis H given some data D, also known as inverse
probability. A frequentist theory, such as Fisher's null hypothesis
testing or NeymanPearson theory, however, does not. It deals with the
probabilities P(DH) of some data D given a hypothesis
H, such as the level of significance.
Fisher was not satisfied with an approach to inductive inference based
on Bayes' theorem. The use of Bayes' theorem presupposes that a prior
probability distribution over the set of possible hypotheses is available.
For a frequentist, such as Fisher, this prior distribution must theoretically
be verifiable by actual frequencies, that is, by sampling from its reference
set. These cases are rare. But if we are ignorant and have no a priori
distributional information, then every researcher can express that ignorance
in different numbers leading, for Fisher, to an unacceptable subjectivism.
As we shall see, however, Fisher wanted to both reject the Bayesian
cake and eat it, too.
Fisher proposed several alternative tools for inductive inference. In
The Design of Experiments, he started with null hypothesis
testing, also known as significance testing, and he gave
that tool the most space in his book. It eventually became the backbone
of institutionalized statistics in psychology. In a test of significance,
one confronts a null hypothesis with observations, to find out whether
the observations deviate far enough from the null hypothesis to conclude
that the null is implausible. The specific techniques of null hypothesis
testing, such as the t test (devised by Gossett, using the pseudonym
"Student", in 1908) or the F test (F for Fisher,
e.g., in analysis of variance) are so widely used that they may be the
lowest common denominator of what psychologists today do and know.
The topic of this chapter is the logic of inference rather than
specific techniques. Just as with Bayes' theorem, the problems we encounter
do not concern the formula  the theorem is a simple consequence
of the definition of conditional probability. The problems arise with
its application to inductive inference in science. To what aspect of
inductive inference does a particular algorithm, or technique, refer?
What do the calculations mean? These are questions that pertain to what
I call the logic of inference.
Concerning my account of Fisher's logic of significance testing, one
thing must be said in advance: Fisher's writings and polemics had a
remarkably elusive quality, and people have read his work quite differently.
During Fisher's long and acrimonious controversy with Neyman and Pearson,
which lasted from the 1930s to his death in 1962, he changed, and sometimes
even reversed, parts of his logic of inference. Thus, the following
brief account of Fisher's logic of inference represents one possible
reading (for a more detailed analysis, see Gigerenzer et al., 1989,
chap. 3).
How do we Determine the Level of Significance?
In the Design, Fisher suggested that we think of the level
of significance as a convention: "It is usual and convenient
for experimenters to take 5 per cent as a standard level of significance,
in the sense that they are prepared to ignore all results which fail
to reach this standard" (1935/1951, p. 13). Fisher's assertion
that 5 % (in some cases, 1 %) is a convention that is adopted
by all experimenters and in all experiments, and nonsignificant results
are to be ignored, became part of the institutionalized hybrid logic.
But Fisher had second thoughts, which he stated most clearly in the
mid1950s. These did not become part of the hybrid logic. One of the
reasons for that revision was his controversy with Neyman and Pearson,
and Neyman's (e.g., 1950) insistence that one has to specify the level
of significance (which is denoted as a in NeymanPearson theory) before
the experiment, in order to be able to interpret it as a longrun frequency
of error. Neyman and Pearson took the frequentist position more seriously
than Fisher. They argued that the meaning of a level of significance
such as 5% is the following: If the null hypothesis is correct, and
the experiment is repeated many times, then the experimenter will wrongly
reject the null in 5% of the cases. To reject the null if it is correct
is called an error of the first kind (Type I error) in NeymanPearson
theory, and its probability is called alpha (a). In his last
book, Statistical Methods and Scientific Inference (1956), Fisher
ridiculed this definition as "absurdly academic, for in fact no
scientific worker has a fixed level of significance at which from year
to year, and in all circumstances, he rejects hypotheses; he rather
gives his mind to each particular case in the light of his evidence
and his ideas" (p. 42). Fisher rejected the NeymanPearson logic
of repeated experiments (repeated random sampling from the same population),
and thereby rejected his earlier proposal to have a conventional standard
level of significance, such as .05 or .01. What researchers should do,
according to Fisher's second thoughts, is to publish the exact level
of significance, say, p = .03 (not p < .05), and communicate
this result to their fellow research workers. This means that the level
of significance is determined after the experiment, not, as Neyman
and Pearson proposed, before the experiment.
Thus the phrase "level of significance" has three meanings:
(a) the standard level of significance, a conventional standard
for all researchers (early Fisher), (b) the exact level of significance,
a communication to research fellows, determined after the experiment
(late Fisher), and (c) the alpha level, the relative frequency of
Type I errors in the long run, to be decided on using costbenefit
considerations before the experiment (Neyman & Pearson).
The basic difference is this: For Fisher, the exact level of significance
is a property of the data (i.e., a relation between a body of data and
a theory); for Neyman and Pearson, alpha is a property of the test,
not of the data. Level of significance and alpha are not the same thing.
Neyman and Pearson thought their straightforward longrun frequentist
interpretation of the significance test  and the associated concepts
of power and of stating two statistical hypotheses (rather than only
one, the null)  would be an improvement on Fisher's theory and
make it more consistent. Fisher disagreed. Whereas Neyman and Pearson
thought of mathematical and conceptual consistency, Fisher thought of
ideological differences. He accused Neyman, Pearson, and their followers
of confusing technology with knowledge: Their focus on Type I and Type
II errors, on costbenefit considerations that determine the balance
between the two, and on repeated sampling from the same population has
little to do with scientific practice, but it is characteristic for
quality control and acceptance procedures in manufacturing. Fisher (1955,
p. 70) compared the NeymanPearsonians to the Soviets, their 5year
plans, and their ideal that "pure science can and should be geared
to technological performance." He also compared them to Americans,
who confuse the process of gaining knowledge with speeding up production
or saving money. (Incidentally, Neyman was born in Russia, and went
to Berkeley, CA, after Fisher made it difficult for him to stay on at
University College in London).
What Does a Significant Result Mean?
The basic differences are these: Fisher attached an epistemic interpretation
to a significant result, which referred to a particular experiment.
Neyman rejected this view as inconsistent and attached a behavioral
meaning to a significant result that did not refer to a particular experiment,
but to repeated experiments. (Pearson found himself somewhere in between.)
In the Design, Fisher talked about how "to disprove"
a null hypothesis (e.g., pp. 1617). Whatever the words he used, he
always held that a significant result affects our confidence or degree
of belief that the null hypothesis is false. This is what I refer to
as an epistemic interpretation: Significance tells us about the
truth or falsehood of a particular hypothesis in a particular experiment.
Here we see very clearly Fisher's quasiBayesian view that the exact
level of significance somehow measures the confidence we should have
that the null hypothesis is false. But from a more consistent frequentist
viewpoint, as expressed by Neyman, a level of significance does not
tell us anything about the truth of a particular hypothesis; it states
the relative frequency of Type I errors in the long run.
Neyman (1957) called his frequentist interpretation behavioristic:
To accept or reject a hypothesis is a decision to take a particular
action. Imagine a typical application of NeymanPearson theory: quality
control. Imagine you have chosen the probability of Type I errors (false
alarms) to be . 10 and that of Type II errors (misses) to be .01, because
misses are much more costly to your firm than false alarms. Every day
you take a random sample from the firm's production. Even if the production
is normal, you will expect a significant result (false alarm) in 10%
of all days. Therefore, if a significant result occurs, you will act
as if the null hypothesis were false, that is, stop the production and
check for a malfunction; but you will not necessarily believe that it
is false  because you expect a lot of false alarms in the long
run.
Fisher rejected Neyman's arguments for "inductive behavior"
as "childish" (1955, p. 75), stemming from "mathematicians
without personal contact with the Natural Sciences" (p. 69). And
he maintained his epistemic view: "From a test of significance
... we have a genuine measure of the confidence with which any particular
opinion may be held, in view of our particular data" (p. 74). For
all his antiBayesian talk, Fisher adopted a very similarsounding line
of argument (Johnstone, 1987).
Does "Significant" Imply that There Is a
Causal Effect?
Of course not. It is useful to distinguish between the statistical
null hypothesis and the substantive null hypothesis.[3]
Only the latter refers to the absence of a particular cause. What is
rejected in significance testing is the statistical hypothesis, not
the existence or absence of a cause. But in Fisher's writings we can
read both "yes" and "no" as answers to the aforementioned
question. Sometimes Fisher formulated the null hypothesis as "the
treatment has no effect, period," whereas in other places he formulated
it as a statistical null hypothesis (see Gigerenzer et al., 1989, pp.
9597). In the famous TeaTasting Experiment in the Design, for instance,
he stated clearly that we cannot conclude from a significant result
(disproving the null) that the opposite hypothesis (which is not formulated
as an exact statistical hypothesis in null hypothesis testing) is proven.
(This experiment was designed to test a lady's claim that she could
tell whether the milk or the tea infusion was first added to a cup.)
That is, we cannot infer the existence of a causal process from a significant
result  here, that the lady can discriminate between whether
the milk or the tea infusion was first added to the cup. For instance,
there exist other causal mechanisms (someone told the lady in which
cups the tea infusion had been poured first) that are consistent with
rejecting the null hypothesis.
What Does a Nonsignificant Result Mean?
In the Design, Fisher proposed asymmetry: A null hypothesis
can be disproved, but "never proved or established" (p. 16),
so "experimenters . . . are prepared to ignore all [nonsignificant]
results" (p. 13). This has been understood by many textbook writers
as saying that no conclusions can be drawn from a nonsignificant result.
And several textbook authors laid down the commandment that I was taught
"Thou shalt not draw inferences from a nonsignificant result."
This made nonsignificance appear a negative, worthless, and disappointing
result. In NeymanPearson theory, in contrast, there is symmetry, and
a conclusion is drawn from nonsignificance: Act as if the null hypothesis
were true. The reason is that Neyman and Pearson start with a disjunction
of two symmetric hypotheses (either H0 or H1
is true), and proceed by induction through elimination.
Fisher (1955) again had second thoughts: "It is a fallacy ... to
conclude from a test of significance that the null hypothesis is thereby
established; at most it may be said to be confirmed or strengthened"
(p. 73). Thus, although nonsignificant results cannot establish null
hypotheses, according to his second thoughts, we can do more than just
"ignore" them: We may say that a nonsignificant result "confirms,"
but does not "establish," the null hypothesis. Now Fisher
suggested that a nonsignificant result might indeed support the null
hypothesis, but he did not explain how.
Power
In null hypothesis testing, only one kind of error is defined: rejecting
the null hypothesis when it is in fact true. In their attempt to supply
a logical basis for Fisher's ideas and make them consistent (see Gigerenzer
et al., 1989, pp. 98106), Neyman and Pearson replaced Fisher's single
null hypothesis by a set of rival hypotheses. In the simplest
case, two hypotheses, H0 and H1
are specified, and it is assumed that one of them is true. This assumption
allows us to determine the probability of both Type I errors and Type
II errors, indicated in NeymanPearson theory by a and b respectively.
If H1 , is rejected although H1 ,
is true, a Type II error has occurred. (a is also called the size
of a test, and 1  b is called its power. The power of a test
is the longrun frequency of accepting H1 if it
is true. The concept of power makes explicit what Fisher referred to
as "sensitivity."
In the Design, Fisher pointed out two ways to make an experiment
more sensitive: by enlarging the number of repetitions, and by qualitative
methods, such as experimental refinements that minimize the error in
the measurements (pp. 2125). Nevertheless, he rejected the concept
of Type II error and calculations of power on the grounds that they
are inappropriate for scientific induction. In his view, calculations
of power, although they look harmless, reflect the "mental confusion"
between technology and scientific inference (Fisher, 1955, p. 73). If
someone designs a test for acceptance procedures in quality control,
where the goal is to minimize costs due to decision errors, calculations
of power based on costbenefit considerations in situations of repetitive
tests are quite appropriate. But scientific inference and discovery,
in Fisher's view, are about gaining knowledge, not saving money.
Fisher always rejected the concept of power. Neyman, for his
part, pointed out that some of Fisher's tests "are in a mathematical
sense 'worse than useless,"' because their power is less than their
size (see Hacking, 1965, p. 99). Even in the Tea Tasting Experiment,
used by Fisher to introduce the logic of null hypothesis testing in
the Design, the power is only a little higher than the level
of significance (.05), or cannot be calculated at all, depending on
the conditions (see Neyman, 1950).
Random Sampling from Known Populations?
Acceptance procedures involve random sampling from a known population
(say, a firm's daily production). They also allow for repeated random
sampling (every day a random sample may be taken). Recall that Neyman
and Pearson based their theory on the concept of repeated random sampling,
which defined the probability of Type I and Type II errors as longrun
frequencies of wrong decisions in repeated experiments.
Fisher, in contrast, held that in scientific applications there is no
known population from which repeated sampling can be done. There are
always many populations to which a sample may belong. "The phrase
'repeated sampling from the same population' does not enable us to determine
which population is to be used to define the probability level, for
no one of them has objective reality, all being products of the statistician's
imagination" (Fisher, 1955, p. 71). Fisher proposed to view any
sample (such as the sample of subjects in a typical psychological experiment,
which is not drawn randomly from a known population) as a random sample
from an unknown hypothetical infinite population. "The postulate
of randomness thus resolves into the question, 'Of what population is
this a random sample'?' which must frequently be asked by every practical
statistician" (Fisher, 1922, p. 313). But how can the practical
statistician find out? The concept of an unknown hypothetical infinite
population has puzzled many: "This is, to me at all events, a most
baffling conception" (Kendall, 1943, p. 17).
Mechanical Scientific Inference
One reading of the Design is that null hypothesis testing is
a fairly mechanical procedure: Set up a null hypothesis, use a conventional
level of significance, calculate a test statistic, and disprove the
null hypothesis, if you can. Fisher later made clear that he did not
mean it to be so. For instance, he pointed out that the choice of the
test statistic, and of deciding which null hypotheses are worth testing,
cannot be reduced to a mechanical process. You need constructive imagination
and much knowledge based on experience (Fisher, 1933). Statistical inference
has two components: informed judgment and mathematical rigor.
Similarly, Neyman and Pearson always emphasized that the statistical
part has to be supplemented by a subjective part. As Pearson
(1962) put it: "We left in our mathematical model a gap for the
exercise of a more intuitive process of personal judgment in such matters
 to use our terminology  as the choice of the most likely
class of admissible hypotheses, the appropriate significance level,
the magnitude of worthwhile effects and the balance of utilities"
(pp. 395396).
In Neyman and Pearson's theory, once all judgments are made, the decision
(reject or accept) falls out mechanically from the mathematics. In his
later writings, Fisher opposed these mechanical accept/reject decisions,
which he believed to be inadequate in science where one looks forward
to further data. Science is concerned with communication of information,
such as exact levels of significance. Again, Fisher saw a broader context,
the freedom of the Western world. Communication of information (but
not mechanical decisions) recognizes "the right of other
free minds to utilize them in making their own decisions"
(Fisher, 1955, p. 77).
But Neyman reproached Fisher with the same sin  mechanical statistical
inference. As a statistical behaviorist, Neyman (1957) looked at what
Fisher actually did in his own research in genetics, biology, and agriculture,
rather than at what he said one should do. He found Fisher using .01
as a conventional level of significance, without giving any thought
to the choice of a particular level dependent on the particular problem
or the probability of an error of the second kind; he accused Fisher
of drawing mechanical conclusions, depending on whether or not the result
was significant. Neyman urged a thoughtful choice of the level of significance,
not using .01 for all problems and contexts.
Both camps in the controversy accused the other party of mechanical,
thoughtless statistical inference, thus I conclude that here at least
they agreed  statistical inference should not be automatic.
These differences between what Fisher proposed as the logic of significance
testing and what Neyman and Pearson proposed as the logic of hypothesis
testing suffice for the purpose of this chapter. Both have developed
further tools for inductive inference, and so did others, resulting
in a large toolbox that contains maximum likelihood, fiducial probability,
confidence interval approaches, point estimation, Bayesian statistics,
sequential analysis, and exploratory data analysis, to mention only
a few. But it is null hypothesis testing and NeymanPearson hypothesistesting
theory that have transformed experimental psychology and part of the
social sciences.
The Offspring: Hybrid Logic
The conflicting views presented earlier are those of the parents of
the hybrid logic. Not everyone can tolerate unresolved conflicts easily
and engage in a free market of competing ideas. Some long for the single
truth or search for a compromise that could at least repress the conflicts.
Kendall (1949) commented on the desire for peace negotiations among
statisticians:
If some people asserted that the earth rotated from east to west
and others that it rotated from west to east, there would always be
a few wellmeaning citizens to suggest that perhaps there was something
to be said for both sides, and maybe it did a little of one and a
little of the other; or that the truth probably lay between the extremes
and perhaps it did not rotate at all. (p. 115)
The denial of the existing conflicts and the pretense that there is
only one statistical solution to inductive inference were carried to
an extreme in psychology and several neighboring sciences. This one
solution was the hybrid logic of scientific inference, the offspring
of the shotgun marriage between Fisher and Neyman and Pearson. The hybrid
logic became institutionalized in experimental psychology (see Gigerenzer,
1987), personality research (see Schwartz & Dangleish, 1982), clinical
psychology and psychiatry (see Meehl, 1978), education (see Carver,
1978), quantitative sociology (see Morrison & Henkel, 1970), and
archaeology (see Cowgill, 1977; Thomas, 1978), among others. Nothing
like this happened in physics, chemistry, or molecular biology (see
Gigerenzer et al., 1989).
The Hybrid Logic Is Born
Before World War 2, psychologists drew their inferences about the
validity of hypotheses by many means  ranging from eyeballing to critical
ratios. The issue of statistical inference was not of primary importance.
Note that this was not because techniques were not yet available. On
the contrary; already in 1710, John Arbuthnot proved the existence of
God by a kind of significance test, astronomers had used them during
the 19th century for rejecting outliers (Swijtink, 1987), and Fechner
(1897) wrote a book on statistics including inference techniques  to
give just a few examples. Techniques of statistical inference were known
and sometimes used, but experimental method was not yet dominated by
and almost equated with statistical inference.
Through the work of the statisticians Snedecor at Iowa State College,
Hotelling at Columbia University, and Johnson at the University of Minnesota,
Fisher's ideas spread in the United States. Psychologists began to cleanse
the Fisherian message of its agricultural smell and its mathematical
complexity, and to write a new genre of textbooks featuring null hypothesis
testing. Guilford's Fundamental Statistics in Psychology and Education,
first published in 1942, was probably the most widely read textbook
in the 1940s and 1950s. In the preface, Guilford credited Fisher for
the new logic of hypothesis testing taught in a chapter that was "quite
new to this type of text" (p. viii). The book does not mention
Neyman, E. S. Pearson, or Bayes. What Guilford teaches as the logic
of hypothesis testing is Fisher's null hypothesis testing, deeply colored
by "Bayesian" terms: Null hypothesis testing is about the
probability that the null hypothesis is true. "If the result comes
out one way, the hypothesis is probably correct, if it comes out another
way, the hypothesis is probably wrong" (p. 156). Null hypothesis
testing is said to give degrees of doubt such as "probable"
or "very likely" a "more exact meaning" (p. 156).
Its logic is explained via headings such as "Probability of hypotheses
estimated from the normal curve" (p. 160).
Guilford's logic is not consistently Fisherian, nor does it consistently
use "Bayesian" language of probabilities of hypotheses. It
wavers back and forth and beyond. Phrases like "we obtained directly
the probabilities that the null hypothesis was plausible" and "the
probability of extreme deviations from chance" are used interchangeably
for the same thing: the level of significance. And when he proposed
his own "somewhat new terms," his intuitive Bayesian thinking
becomes crystal clear. A p value of .015 for a hypothesis of
zero difference in the population "gives us the probability that
the true difference is a negative one, and the remainder of the area
below the point, or .985, gives us the probability that the true difference
is positive. The odds are therefore .985 to .015 that the true difference
is positive" (p. 166). In Guilford's hands, p values that
specify probabilities p(DH) of some data (or test
statistic) D given a hypothesis H turn miraculously into
Bayesian posterior probabilities p(H D) of a hypothesis
given data.
Guilford's logic is not an exception. It marks the beginning of a genre
of statistical texts that vacillate between the researcher's "Bayesian"
desire for probabilities of hypotheses and what Fisher is willing to
give them.
This first phase of teaching Fisher's logic soon ran into a serious
complication. In the 1950s and 1960s, the theory of Neyman and E. S.
Pearson also became known. How were the textbook writers to cope with
two logics of scientific inference? How should the ideological differences
and personal insults be dealt with? Their solution to this conflict
was striking. The textbook writers did not side with Fisher. That is,
they did not go on to present null hypothesis testing as scientific
inference and add a chapter on hypothesis testing outside science, introducing
the NeymanPearson theory as a logic for quality control and related
technological problems. Nor did they side with Neyman and Pearson, teaching
their logic as a consistent and improved version of Fisher's and dispensing
entirely with Fisherian null hypothesis testing.
Instead, textbook writers started to add NeymanPearsonian concepts
on top of the skeleton of Fisher's logic. But acting as if they feared
Fisher's revenge, they did it without mentioning the names of Neyman
and Pearson. A hybrid logic of statistical inference was created
in the 1950s and 1960s. Neither Fisher nor Neyman and Pearson would
have accepted this hybrid as a theory of statistical inference. The
hybrid logic is inconsistent from both perspectives and burdened with
conceptual confusion. Its two most striking features are (a) it hides
its hybrid origin and (b) it is presented as the monolithic logic of
scientific inference. Silence about its origin means that the respective
parts of the logic are not identified as part of two competing and partly
inconsistent theoretical frameworks. For instance, the idea of testing
null hypotheses without specifying alternative hypotheses is not identified
as part of the Fisherian framework, and the definition of the level
of significance and the power of a test as longrun frequencies of false
and correct decisions, respectively, in repeated experiments is not
identified as part of the NeymanPearson framework. And, as a consequence,
there is no mention of the fact that each of these parts of the hybrid
logic were rejected by the other party, and why, and what the unresolved
controversial issues are.
The Structure of Hybrid Logic
In order to capture the emotional tensions associated with the hybrid
logic, I use a Freudian analogy.[4]
The NeymanPearson logic of hypothesis testing functions as the Superego
of the hybrid logic. It demands the specification of precise alternative
hypotheses, significance levels, and power in advance to calculate the
sample size necessary, and it teaches the doctrine of repeated random
sampling. The frequentist Superego forbids epistemic statements about
particular outcomes or intervals, and it outlaws the interpretation
of levels of significance as the degree of confidence that a particular
hypothesis is true or false.
The Fisherian theory of significance testing functions as the Ego. The
Ego gets things done in the laboratory and gets papers published. The
Ego determines the level of significance after the experiment, and it
does not specify power nor calculate the sample size necessary. The
Ego avoids precise predictions from its research hypothesis; that is,
it does not specify the exact predictions of the alternative hypothesis,
but claims support for it by rejecting a null hypothesis. The Ego makes
abundant epistemic statements about particular results. But it is left
with feelings of guilt and shame for having violated the rules.
Censored by both the frequentist Superego and the pragmatic Ego are
statements about probabilities of hypotheses given data. These form
the Bayesian Id of the hybrid logic. Some direct measure of the validity
of the hypotheses under question  quantitatively or qualitatively 
is, after all, what researchers really want.
The Freudian metaphor suggests that the resulting conceptual confusion
in the minds of researchers, editors, and textbook writers is not due
to limited intelligence. The metaphor brings the anxiety and guilt,
the compulsive and ritualistic behavior, and the dogmatic blindness
associated with the hybrid logic into the foreground. It is as if the
raging personal and intellectual conflicts between Fisher and Neyman
and Pearson, and between these frequentists and the Bayesians were
projected into an "intrapsychic" conflict in the minds of
researchers. And the attempts of textbook writers to solve this conflict
by denying it have produced remarkable emotional, behavioral, and cognitive
distortions.
Anxiety and Guilt
Editors and textbook writers alike have institutionalized the level
of significance as a measure of the quality of research. As mentioned
earlier, Melton, after 12 years editing one of the most prestigious
journals in psychology, said in print that he was reluctant to publish
research with significance levels below .05 but above .01, whereas p
< .01 made him confident that the results would be repeatable and
deserved publication (1962, pp. 553554). In Nunnally's Introduction
to Statistics for Psychology and Education (1975) the student is
taught similar values and informed that the standard has been raised:
"Up until 20 years ago, it was not uncommon to see major research
reports in which most of the differences were significant only at the
0.05 level. Now, such results are not taken very seriously, and it is
more customary today to see results reported only if they reach the
0.01 or even lower probability levels" (p. 195). Not accidentally,
both Melton and Nunnally show the same weak understanding of the logic
of inference and share the same erroneous belief that the level of significance
specifies the probability that a result can be replicated (discussed
later). The believers in the divinatory power of the level of significance
set the standards.
The researcher's Ego knows that these publishorperish standards exist
in the outside world, and knows that the best way to adapt is to round
up the obtained p value after the experiment to the nearest conventional
level, say to round up the value p = .006 and publish p
< .01. But the Superego has higher moral standards: If you set alpha
to 5% before the experiment, then you must report the same finding (p
= .006) as "significant at the 5% level." Mostly, the Ego
gets its way, but is left with feelings of dishonesty and of guilt at
having violated the rules. Conscientious experimenters have experienced
these feelings, and statisticians have taken notice. The following comment
was made in a panel discussion among statisticians; Savage remarked
on the statisticians' reluctance to take responsibility for once having
built up the Superego in the minds of the experimenters:
I don't imagine that anyone in this room will admit ever having taught
that the way to do an experiment is first carefully to record the
significance level then do the experiment, see if the significance
level is attained, and if so, publish, and otherwise, perish. Yet,
at one time we must have taught that; at any rate it has been extremely
well leamed in some quarters. And there is many a course outside of
statistics departments today where the modem statistics of twenty
or thirty years ago is taught in that rigid way. People think that's
what they're supposed to do and are horribly embarrassed if they do
something else, such as do the experiment, see what significance level
would have been attained, and let other people know it. They do the
better thing out of their good instincts, but think they're sinning.
(Bamard, Kiefer, LeCam & Savage, 1968, p. 147)
Statistics has become more tolerant than its offspring, the hybrid
logic.
Denial of the Parents
The hybrid logic attempts to solve the conflict between its parents
by denying its parents. It is remarkable that textbooks typically teach
hybrid logic without mentioning Neyman, E. S. Pearson, and Fisher 
except in the context of technical details, such as specific tables,
that are incidental to the logic. In 25 out of 30 textbooks I have examined,
Neyman and E. S. Pearson do not appear to exist. For instance, in his
Statistical Principles in Experimental Design (1 962; 2nd ed.,
1971), Winer credited Fisher for the "logic of scientific method"
(p. 3), and a few pages later, introduced the NeymanPearson terminology
of Type I error, Type II error, power, two precise statistical hypotheses,
costbenefit considerations, and rejecting and accepting
hypotheses. Nowhere in the book do the names of Neyman and E. S. Pearson
appear (except in a "thank you" note to Pearson for permission
to reproduce tables), although quite a few other names can be found
in the index. No hint is given to the reader that there are different
ways to think about the logic of inference. Even in the exceptional
case of Hays's textbook (1963), where all parents are mentioned by their
names, the relationship of their ideas is presented (in a single sentence)
as one of cumulative progress, from Fisher to Neyman and Pearson (p.
287).[5] Both Winer's and Hays's
are among the best texts, without the confusions that abound in Guilford's,
Nunnally's, and a mass of other textbooks. Nevertheless, even in these
texts the parents' different ways of thinking about statistical inference
and the controversial issues are not pointed out.
Denial of Conflicts Between Parents
Thus the conflicting views are almost unknown to psychologists. Textbooks
are uniformly silent. (Some statistics teachers protest that airing
these disputes would only confuse students. I believe that pointing
out the conflicting views would make statistics much more interesting
to students who enjoy thinking rather than being told what to do next.)
As a result of this silence, many a text muddles through the conflicting
issues leaving confusion and inconsistency in its wake  at least, among
the more intelligent and alert students. For instance, Type I and Type
II errors are often defined in terms of longrun frequencies of erroneous
decisions in repeated experiments, but the texts typically stop short
of Neyman's behavioral interpretation, and fall back to epistemic interpretations
of the two errors as levels of confidence about the validity of the
hypotheses. In fact, the poorer texts overflow with amazing linguistic
contortions concerning what a level of significance means. For instance,
within three pages of text, Nunnally explained that "level of significance"
means all of the following: (a) "If the probability is low, the
null hypothesis is improbable" (p. 194); (b) "the improbability
of observed results being due to error" (p. 195); (c) "the
probability that an observed difference is real" (p. 195); (d)
"the statistical confidence ... with odds of 95 out of 100
that the observed difference will hold up in investigations" (p.
195); (e) the degree to which experimental results are taken "seriously"
(p. 195); (f) "the danger of accepting a statistical result as
real when it is actually due only to error" (p. 195); (g) the degree
of "faith [that] can be placed in the reality of the finding"
(p. 196); (h) "the null hypothesis is rejected at the 0.05 level";
and (i) "the investigator can have 95 percent confidence that the
sample mean actually differs from the population mean" (p. 196).
And, after the last two versions, the author assured his readers: "All
of these are different ways to say the same thing" (p. 196).
Nunnally did not spell out the differences between the logics of Fisher,
Neyman and Pearson, and the Bayesians. He avoided the conflicting interpretations
by declaring that everything is the same. The price for this is conceptual
confusion, false assertions, and an illusory belief in the omnipotence
of the level of significance. Nunnally was a pronounced but not an atypical
case.
ObsessiveCompulsive and Mechanical Behavior
As previously mentioned, statisticians have emphasized the indispensable
role of personal judgment, although with respect to different parts
of their logics. For Fisher, informed judgment was needed for the choice
of the statistical model, the test statistics, and a null hypothesis
worth investigating. For Neyman and Pearson, personal judgment was needed
for the choice of the class of hypotheses (two hypotheses, in the simplest
case), and the costbenefit considerations that lead to the choice of
Type I error, power, and sample size. For Bayesians such as de Finetti,
finally, "subjectivism" and "relativism" are the
very cornerstones of 20thcentury probability theory (de Finetti, 1931/1989;
Jeffrey, 1989).
The need for these kinds of informed judgments was rarely a topic in
the textbooks. Rather, a mass of researchers must have read the textbooks
as demanding the mindless, mechanical setting up of null hypotheses
and recording of p values. Journals filled with p values,
stars, double stars, and triple stars that allegedly established replicable
"facts" bear witness to this cookbook mentality.
Guilford's misunderstanding that to set up a null hypothesis means to
postulate a zero difference or a zero correlation was perpetuated. "Null"
denotes the hypothesis to be "nullified," not that it is necessary
to postulate a zero effect. Rarely were null hypotheses formulated that
postulated something other than a zero effect (such as "the difference
between the means is 3 scale points"). Rarely were precise alternative
hypotheses stated, and even if there were two competing precise hypotheses,
as in Anderson's information integration theory, only one of them was
tested as the null hypothesis, sometimes resulting in tests with a power
as low as .06 (Gigerenzer & Richter, 1990). Reasons for using a
particular level of significance were almost never given, and rarely
was a judgment about the desired power made and the sample size calculated.
As a result, the power of the tests is typically quite low (below .50
for a medium effect), and pointing this out (Cohen, 1962) has not changed
practice. Twoandahalf decades after Cohen's work, the power of the
null hypothesis tests was even slightly worse (Sedlmeier & Gigerenzer,
1989). Rather, null hypotheses are set up and tested in an extremely
mechanical way reminiscent of compulsive handwashing. One can feel widespread
anxiety surrounding the exercise of informed personal judgment in matters
of hypothesis testing. The availability of statistical computer packages
seems to have reinforced this mechanical behavior. A student of mine
once tested in his thesis the difference between two means, which were
numerically exactly the same, by an F test. Just to say that the means
are the same seemed to him not objective enough.
The institutionalization of the hybrid logic as the sine qua non of
scientific method is the environment that encourages mechanical hypothesis
testing. The Publication Manual of the American Psychological Association,
for instance, called "rejecting the null hypothesis" a "basic"
assumption (1974, p. 19) and presupposes the hybrid logic. The researcher
was explicitly told to make mechanical decisions: "Caution: Do
not infer trends from data that fail by a small margin to meet the usual
levels of significance. Such results are best interpreted as caused
by chance and are best reported as such. Treat the result section like
an income tax return. Take what's coming to you, but no more" (p.
19; this passage was deleted in the 3rd ed., 1983). This prescription
sounds like a NeymanPearson acceptreject logic, where it matters for
a decision only on which side of the criterion the data fall, not how
far. Fisher would have rejected such mechanical behavior (e.g., Fisher,
1955, 1956). Nevertheless, the examples in the manual that tell the
experimenter how to report results use p values that were obviously
determined after the experiment and rounded up to the next conventional
level, such as p < .05, p < .01, and p <
.001 (pp. 39, 43, 48, 49, 70, 96). Neyman and Pearson would have rejected
this practice: These p values are not the probability of Type I errors
 and determining levels of significance after the experiment
prevents determining power and sample size in advance. Fisher (e.g.,
1955, 1956) would have preferred that the exact level of significance,
say p = .03, be reported, not upper limits, such as p
< .05, which look like probabilities of Type I errors but aren't.
Distorted Statistical Intuitions
Mechanical null hypothesis testing seems to go handinhand with distorted
statistical intuitions. I distinguish distorted statistical intuitions
from the confusion and inconsistency of the hybrid logic itself. The
latter results from mishmashing Fisher and Neyman and Pearson without
making the conflation explicit, as I argued earlier. The conceptual
confusion of the hybrid logic provided fertile ground for the growth
of what I call distorted statistical intuitions. The distortions
all seem to go in one direction: They exaggerate what can be inferred
from a p value.
The framework of distorted intuitions makes the obsessive performance
of null hypothesis testing seem quite reasonable. Therefore, distorted
intuitions serve an indispensable function. These illusions guide the
writings of several textbook authors and editors, but they seem to be
most pronounced in the users of null hypothesis testing, researchers
in psychology and neighboring fields. Some distorted intuitions concern
the frequentist part of the hybrid logic, others the Bayesian Id. I
give one example of each (there is a larger literature on distorted
statistical intuitions taught in statistical textbooks and held by experimenters;
see Acree, 1978; Bakan, 1966; Brewer, 1985; Carver, 1978; Guttman, 1977,
1985; Lykken, 1968; Pollard & Richardson, 1987; Rozeboom, 1960;
Tversky & Kahneman, 1971).
Replication Fallacy. Suppose a is set as .05 and the null hypothesis
is rejected in favor of a given alternative hypothesis. What if we replicate
the experiment? In what percentage of exact replications will the result
again turn out significant? Although this question arises from the frequentist
conception of repeated experiments, the answer is unknown. The a we
chose does not tell us, nor does the exact level of significance.
The replication fallacy is the belief that the level of significance
provides an answer to the question. Here are some examples: In an editorial
of the Journal of Experimental Psychology, the editor stated
that he used the level of significance reported in submitted papers
as the measure of the "confidence that the results of the experiment
would be repeatable under the conditions described" (Melton, 1962,
p. 553). Many textbooks fail to mention that the level of significance
does not specify the probability of a replication, and some explicitly
teach the replication fallacy. For instance, "The question of statistical
significance refers primarily to the extent to which similar results
would be expected if an investigation were to be repeated" (Anastasi,
1958, p. 9). Or, "If the statistical significance is at the 0.05
level ... the investigator can be confident with odds of 95 out of 100
that the observed difference will hold up in future investigations"
(Nunnally, 1975, p. 195). Oakes (1986, p. 80) asked 70 university lecturers,
research fellows, and postgraduate students with at least 2 years' research
experience what a significant result (t = 2.7, df = 18,
p = .01) means. Sixty percent of these academic psychologists
erroneously believed that these figures mean that if the experiment
is repeated many times, a significant result would be obtained 99% of
the time.
In Neyman and Pearson's theory the level of significance (alpha) is
defined as the relative frequency of rejections of H0
if H0 is true. In the minds of many, 1  alpha erroneously
turned into the relative frequency of rejections of H0 ,
that is, into the probability that significant results could be replicated.
The Bayesian Id's Wishful Thinking. I mentioned earlier that
Fisher both rejected the Bayesian cake and wanted to eat it, too: He
spoke of the level of significance as a measure of the degree of confidence
in a hypothesis. In the minds of many researchers and textbook writers,
however, the level of significance virtually turned into a Bayesian
posterior probability.
What I call the Bayesian Id's wishful thinking is the belief
that the level of significance, say .01, is the probability that the
null hypothesis is correct, or that 1  .01 is the probability that
the alternative hypothesis is correct. In various linguistic versions,
this wishful thinking was taught in textbooks from the very beginning.
Early examples are Anastasi (1958, p. I 1), Ferguson (1959, p. 133),
Guilford (1942, pp. 156166), and Lindquist (1940, p. 14). But the belief
has persisted over decades of teaching hybrid logic, for instance in
Miller and Buckhout (1973, statistical appendix by Brown, p. 523), Nunnally
(1975, pp. 194196), and the examples collected by Bakan (1966) and
Pollard and Richardson (1987). Oakes (1986, p. 82) reported that 96%
of academic psychologists erroneously believed that the level of significance
specifies the probability that the hypothesis under question is true
or false.
The Bayesian Id has got its share. Textbook writers have sometimes explicitly
taught this misinterpretation, but more often invited it by not specifying
the difference between a Bayesian posterior probability, a NeymanPearsonian
probability of a Type I error, and a Fisherian exact level of significance.
Dogmatism
The institutionalization of one way to do hypothesis testing
had its benefits. It made the administration of the social science research
that exploded since World War 2 easier, and it facilitated editors'
decisions. And there were more benefits. It reduced the high art of
hypothesis construction, of experimental ingenuity and informed judgment,
into a fairly mechanical schema that could be taught, learned, and copied
by almost anyone. The informed judgments that remain are of a lowlevel
kind: whether to use a one or a twotailed significance test. (But
even here some believed that there should be no room for judgment, because
even this simple choice seemed to threaten the ideal of mechanical rules
and invite cheating.) The final, and perhaps most important, benefit
of the hybrid logic is that it provides the satisfying illusion of objectivity:
The statistical logic of analyzing data seemed to eliminate the subjectivity
of eyeballing and wishful distortion. To obtain and maintain this illusion
of objectivity and impartiality, the hybrid logic had to deny
its parents  and their conflicts.
The danger of subjective distortion and selective reading of data exists,
to be sure. But it cannot be cured by replacing the distortions of particular
experimenters by a collective distortion. Note that the institutionalized
practice produces only selective and limited objectivity, and hands
other parts of scientific practice over to rules of thumbeven parts
for which the statistical methods would be applicable. For example,
during the 19th century, astronomers used significance tests to reject
data (socalled outliers), assuming, at least provisionally,
that their hypothesis was correct (Swijtink, 1987). Social scientists
today, in contrast, use significance tests to reject hypotheses,
assuming that their data are correct. The mathematics does not dictate
which one the scientists should trust and which one they should try
to refute. Social scientists seem to have read the statistical textbooks
as saying that statistical inference is indispensable in selecting good
from bad hypotheses, but not for selecting good from bad data. The problem
of outliers is dealt with by rules of thumb.[6]
The dogmatism with which the hybrid logic has been imposed on psychology
researchers by many textbook writers and editors and by researchers
themselves has lasted for almost half a century. This is far too long.
We need a knowledgeable use of statistics, not a collective compulsive
obsession. The last two decades suggest that things are, although very
slowly, changing in the right direction.
Beyond Dogmatism: Toward a Thoughtful Use of Statistics
Here are a few first principles: Do not replace the dogmatism of the
hybrid logic of scientific inference by a new, although different one
(e.g., Bayesian dogmatism). Remember the obvious: The problem of inductive
inference has no universal mathematical solution. Use informed judgment
and statistical knowledge. Here are several more specific suggestions:
1. Stop teaching hybrid logic as the sine qua non of scientific inference.
Teach researchers and students alternative theories of statistical
inference, give examples of typical applications and teach the students
how to use these theories in a constructive (not mechanical) way. Point
out the confused logic of the hybrid, the emotional, behavioral, and
cognitive distortions associated with it, and insist on consistency
(Cohen, 1990). This will lead to recognizing the second point.
2. Statistical inference (Fisherian, NeymanPearsonian, or Bayesian)
is rarely the most important part of data analysis. Teach researchers
and students to look at the data, not just on p values. Computeraided
graphical methods of data display and exploratory data analysis are
means toward this end (Diaconis, 1985; Tukey, 1977). The calculation
of descriptive statistics such as effect sizes is a part of data analysis
that cannot be substituted by statistical inference (Rosnow & Rosenthal,
1989). A good theory predicts particular curves or effect sizes, but
not levels of significance.
3. Good data analysis is pointless without good data. The measurement
error should be controlled and minimized before and during the experiment;
instead one tends to control it after the experiment by inserting the
error term in the F ratio. Teach researchers and students that the important
thing is to have a small real error in the data. Without that, a significant
result at any level is, by itself, worthless  as Gosset, who
developed the t test in 1908, emphatically emphasized (see Pearson,
1939). Minimizing the real error in measurements may be achieved by
an iterative method: First, obtain measurements and look at the error
variance, then try methods to minimize the error (e.g., stronger experimental
control, investigating each subject carefully in a singlecase study
rather than in a classroom), then go back and obtain new measurements
and look at the new error variance, and so on, until improvements are
no longer possible. Axiomatic measurement theory that focuses on ordinal
rather than numerical judgments may help (Krantz, Luce, Suppes, &
Tversky, 1971). It is all too rarely used.
4. Good data need good hypotheses and theories to survive. We
need rich theoretical frameworks that allow for specific predictions
in the form of precise research hypotheses. The null hypothesis of zero
difference (or zero correlation) is only one version of such a hypothesis
 perhaps only rarely appropriate. In particular, it has become
a bad habit not to specify the predictions of a research hypothesis,
but to specify a different hypothesis (the null) and to try to reject
it and claim credit for the unspecified research hypothesis. Teach students
to derive competing hypotheses from competing theoretical frameworks,
and to test their ordinal or quantitative predictions directly,
without using the null as a straw man.
Epilogue: More Superegos
Around 1840, the classical theory of probability dissolved and the
frequentist interpretation of probability emerged (Daston, 1988; Porter,
1986). Today, teaching in statistics departments is still predominantly
in the frequentist tradition, and Fisher's and Neyman and Pearson's
theories are two variants thereof. But this century has witnessed the
revival of subjective probability, often referred to as Bayesian
statistics, largely through the writings of the Italian actuary
de Finetti and the English philosopher Ramsey in the 1920s and 1930s,
and in the 1950s by the American statistician Savage. For a Bayesian,
probability is about subjective degrees of belief, not about objective
frequencies. A degree of belief of 1/10 that the next president of the
United States will be a woman can be interpreted as the willingness
to take either side of a nine to one bet on this issue. Bayesians are
still a minority in statistics departments, but the Bayesian model of
rationality has found a role in theoretical economics (mainly microeconomics),
cognitive psychology, artificial intelligence, business, and medicine.
In 1963, Edwards, Lindman, and Savage argued that psychologists should
stop frequentist null hypothesis testing and do Bayesian statistics
instead (their counterparts in Europe were, among others, Kleiter, 1981;
Tholey, 1982). Edwards and his colleagues also started a research program
on whether intuitive statistical judgments follow Bayes' theorem. Their
suggestion that psychologists should turn Bayesian fell on deaf ears,
both in the United States and in Europe. Researchers already had their
hybrid logic, which seemed to them the objective way to do scientific
inference, whereas Bayesian statistics looked subjective. And given
the distorted statistical intuitions of many, there was actually no
need; the level of significance already seemed to specify the desired
Bayesian posterior probabilities.[7]
The second of Edwards's proposals, in contrast, caught on: To study
whether and when statistical intuitions conform to Bayes' theorem (e.g.,
Edwards, 1968). More than in Edwards's research, the heuristics and
biases program of the 1970s and 1980s (e.g., Tversky & Kahneman,
1974) focussed on what were called fallacies and errors in probabilistic
reasoning: discrepancies between human judgment and Bayes' formula.
The New Bayesian Superego
The Bayesian Id of the hybrid logic had turned into the new Superego
of research on intuitive statistics. Frequentist theories were suppressed.
Bayesian statistics (precisely, one narrow version thereof) was seen
as the correct method of statistical reasoning, whether it was
about the subjective probability that a particular person was an engineer
(Kahneman & Tversky, 1973) or that a cab involved in a hitandrun
accident at night was blue (Tversky & Kahneman, 1980). However,
if one applies NeymanPearson theory to the cab problem, or alternative
Bayesian views, one obtains solutions that are strikingly different
from Tversky and Kahneman's Bayesian calculations (Bimbaum, 1983; Gigerenzer
& Murray, 1987, pp. 167174; Levi, 1983). The objections of Fisher
and Neyman to the universal use of Bayesian statistics seemed to be
buried below the level of consciousness, and so was the most basic objection
of a frequentist: Probability is about frequencies, not about single
events (such as whether a particular cab was blue or Linda is a bank
teller).
A striking result demonstrates the importance of that objection: Socalled
fallacies frequently disappear when subjects are asked for frequency
judgments rather than for singleevent probabilities (Gigerenzer, 1991
a, 1991 b; Gigerenzer, Hoffrage, & Kleinbölting, 1991). Within
the heuristics and biases program, the frequentist Superego of the hybrid
logic, who had banned probability statements about particular events
or values, was no longer heard. Nor was the frequentist Bamard (1979),
who commented thus on subjective probabilities for single events: "If
we accept it as important that a person's subjective probability assessments
should be made coherent, our reading should concentrate on the works
of Freud and perhaps Jung rather than Fisher and Neyman" (p. 17
1).
Suddenly, the whole psychic structure of statistical reasoning in psychology
seemed to be reversed. Now Bayesian statistics (precisely, a narrow
version thereof) was presented as the sine qua non of statistical reasoning,
as the nonnative standard. Against this standard, all deviating reasoning
seemed to be a fallacy. Neyman had wamed of "the dogmatism
which is occasionally apparent in the application of Bayes' formula"
(1957, p. 19). He meant the conviction "that it is possible to
devise a formula of universal validity which can serve as a normative
regulator of our beliefs" (p. 15). Similarly, for Fisher, only
some uncertain inferences, but not all kinds, can be adequately dealt
with by probability theory. Bayesian theory "is founded upon an
error, and must be wholly rejected" (Fisher, 1925, p. 9).
Good statistical reasoning has been once more equated with the mechanical
application of some statistical formula.
It seems to have gone almost unnoticed that this dogmatism has created
a strange double standard. Many researchers believe that their subjects
must use Bayes' theorem to test hypotheses, but the researchers themselves
use the hybrid logic to test their hypotheses  and thus themselves
ignore base rates. There is the illusion that one kind of statistics
normatively defines objectivity in scientific inference, and another
one rationality in everyday inference. The price is a kind of "split
brain," where NeymanPearson logic is the Superego for experimenters'
hypothesis testing and Bayesian statistics is the Superego for subjects'
hypothesis testing.
Conclusions
Statistical reasoning is an art and so demands both mathematical knowledge
and informed judgment. When it is mechanized, as with the institutionalized
hybrid logic, it becomes ritual, not reasoning. Many colleagues of mine
have argued that it is not going to be easy to get researchers in psychology
and other sociobiomedical sciences to drop this comforting crutch unless
one offers an easytouse substitute. But this is exactly what I want
to avoid  the substitution of one mechanistic dogma for another.
It is our duty to inform our students about the many good roads to statistical
inference that exist, and to teach them how to use informed judgment
to decide which one to follow for a particular problem. At the very
least, this chapter can serve as a tool in arguments with people who
think they have to defend a ritualistic dogma instead of good statistical
reasoning. Making and winning such arguments is indispensable to good
science.
Acknowledgements
This chapter was written while I was a Fellow at the Center for Advanced
Study in the Behavioral Sciences, Stanford, CA. I am grateful for financial
support provided by the Spencer Foundation and the Deutsche Forschungsgemeinschaft
(DFG 170/21). Leda Cosmides, Lorraine Daston, Raphael Diepgen, Ward
Edwards, Ruma Falk, Gideon Keren, Duncan Luce, Kathleen Much, Zeno Swijtink,
and John Tooby helped to improve the present chapter.






Footnotes
[1] 
The ground for the inference revolution
was prepared by a dramatic shift in experimental practice. During
the 1920s, 1930s, and 1940s, the established tradition of experimenting
with single subjects  from Wundt to Pavlov  was replaced
in the United States by the treatment group experiment, in
which group means are compared. For instance, between 1915 and 1950,
the percentage of empirical studies reporting only group data in
the American Journal of Psychology rose from 25% to 80%,
and the reporting of only individual data decreased from 70% to
17% (Danziger, 1990). Danziger argued that this shift was in part
due to the pressure felt by United States academic psychologists
to legitimize their work through showing its practical utility.
The Wundtian type of experiment was useless to educational administrators,
the largest market for psychological products. The treatment group
experiment, however, appeared to fit their needs exactly, for example,
by allowing them to compare mean performance in two classrooms that
were using different instruction methods. After this change in experimental
practice, null hypothesis testing of group means appeared to be
tailormade to the new unit of research, the group aggregate. Consistent
with Danziger's argument, the institutionalization of both the treatment
group and null bypothesis testing spread from the applied fields
to the laboratories (Lovie, 1979). The contrast with Germany is
telling. German academic psychologists of the early 20th century
had to legitimize their work before a different tribunal, the values
of a wellentrenched intellectual elite (Danziger, 1990). In contrast
to the United States, the German educational system, run by tradition
rather than by experimentation, provided only a limited market for
psychologists. No comparable shift in experimental practice happened
in German psychology. It was only after World War II that a new
generation of German psychologists began to assimilate the methodological
imperatives imported from their colleagues in the United States. 
[2] 
R. Duncan Luce, personal communication,
April 4, 1990. See also Luce's (1989) autobiography, on p. 270 and
pp. 281282. 
[3] 
0n the distinction between statistical
and substantive hypotheses, see Hager and Westermann (1983) and
Meehl (1978). 
[4] 
Here I am elaborating on a metaphor
suggested by Acree (1978). In a different context, Devereux (1967)
talked about the relation between anxiety and elimination of subjectivity
by method. 
[5] 
In the 3rd edition (1981), however,
Hays's otherwise excellent text falls back to common standards:
J. Neyman and E. S. Pearson no longer appear in the book. 
[6] 
SO is the problem of how many replications
(subjects) an experiment should use. Sedlmeier and Gigerenzer (1989)
found no use of NeymanPearsonian calculations of sample size in
published work. Some statistical texts have explicitly encouraged
this: "Experienced researchers use a rule of thumb sample size
of approximately twenty. Smaller samples often result in low power
values while larger samples often result in a waste of time and
money" (Bruning & Kintz, 1977, p. 7). 
[7] 
I know of only a handful of studies published in psychological
journals where researchers used Bayesian statistics instead of
the hybrid logic. Even Hays, who included a chapter on Bayesian
statistics in the second edition of his statistics text, dropped
it in the third edition.

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