1. science
2. mathematics
3. statistics

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Bayesian versus Orthodox statistics: Which side are you on?
RUNNING HEAD: Bayesian versus orthodox statistics
Zoltan Dienes
School of Psychology
University of Sussex
Brighton BN1 9QH UK
dienes@sussex.ac.uk
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Abstract
Some common situations are presented where Bayesian and orthodox
approaches to statistics come to different conclusions; you can see where your
intuitions initially lie. The approaches are placed in the context of different notions of
rationality and I accuse myself and others as having been irrational in the way we
have been using statistics, i.e. as orthodox statistics. One notion of rationality is
having sufficient justification for one’s beliefs. Assuming one can assign numerical
continuous degrees of justification to beliefs, some simple minimal desiderata lead to
the “likelihood principle” of inference. Hypothesis testing violates the likelihood
principle, indicating that some of the deepest held intuitions we train ourselves to
have as orthodox users of statistics are irrational on a key intuitive notion of
rationality. I consider practical considerations so people can make a start at being
Bayesian, if they so wish: If we want to, we really can change!
Keywords: Statistical inference, Bayes, significance testing, evidence
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Bayesian versus Orthodox statistics: Which side are you on?
Introduction
Psychology and other disciplines have benefited enormously from having a
rigorous procedure for extracting inferences from data. The question this article raises
is whether we could not be doing it better. Two main approaches are contrasted,
orthodox statistics versus the Bayesian approach. Around the 1940s the heated debate
between the two camps was momentarily won in terms of what users of statistics did:
Users followed the approach systematised by Jerzy Neyman and Egon Pearson (at
least this approach defined norms; in practice researchers followed the somewhat
different advice of Ronald Fisher; see e.g. Gigerenzer, 2004). But it wasn’t that the
intellectual debate was decisively won. It was more a practical matter: A matter of
which approach had the mathematics been most well worked out for detailed
application at the time; and which approach was conceptually easier for the researcher
to apply. But now the practical problems have been largely solved; there is little to
stop researchers being Bayesian in almost all circumstances. Thus the intellectual
debate can be opened up again, and indeed it has (e.g. Hoijtink, Klugkist, & Boelen,
2008; Howard, Maxwell, & Fleming, 2000; Rouder et al , 2007; Taper & Lele,
2004). It is time for researchers to consider foundational issues in inference. And it is
time to consider whether the fact it takes less thought to calculate p values is really an
advantage, or whether it has led us astray in interpreting data (e.g. Harlow, Mulaik, &
Steiger, 1997; Meehl, 1967; Royall, 1997; Ziliak & McCloskey, 2008), despite the
benefits it has also provided. Indeed, I argue we would be most rational, under one
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intuitively compelling notion of rationality, to be Bayesians. To see how which side
your intuitions fall, at least initially, we next consider some common situations where
the approaches come to different conclusions.
Bayesian or Orthodox: Where do your intuitions fall?
Consider the following scenarios and see what your intuitions tell you. You
might reject all the answers or feel attracted to more than one. Real research questions
do not have pat answers. See if, nonetheless, you have clear preferences for one or a
couple of answers over another. Almost all answers are consistent either with some
statistical approach or with what a large section of researchers do in practice, so do
not worry about picking out the one ‘right’ answer (though, given certain
assumptions, I will argue that there is one right answer!).
1) You have run the 20 subjects you planned and obtain a p value of .08.
Despite predicting a difference, you know this won’t be convincing to any editor and
run 20 more subjects. SPSS now gives a p of .01. Would you:
a) Submit the study with all 40 participants and report an overall p of .01?
b) Regard the study as non-significant at the 5% level and stop pursuing the
effect in question, as each individual 20-subject study had a p of .08?
c) Use a method of evaluating evidence that is not sensitive to your intentions
concerning when you planned to stop collecting subjects, and base conclusions on all
the data?
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2) After collecting data in a three-way design you find an unexpected partial
two-way interaction, specifically you obtain a two-way interaction (p = .03) for just
the males and not the females. After talking to some colleagues and reading the
literature you realise there is a neat way of accounting for these results: certain
theories can be used to predict the interaction for the males but they say nothing about
females. Would you:
a) Write up the introduction based on the theories leading to a planned contrast
for the males, which is then significant?
b) Treat the partial two-way as non-significant, as the three-way interaction
was not significant, and the partial interaction won’t survive any corrections for post
hoc testing?
c) Determine how strong the evidence of the partial two-way interaction is for
the theory you put together to explain it, with no regard to whether you happen to
think of the theory before seeing the data or afterwards, as all sorts of arbitrary factors
could influence when you thought of a theory?
3) You explore five possible ways of inducing subliminal perception as
measured with priming. Each method interferes with vision in a different way. The
test for each method has a power of 80% for a 5% significance level to detect the size
of priming produced by conscious perception. Of these methods, the results for four
are non-significant and one, the Continuous Flash Suppression, is significant, p = .03,
with a priming effect numerically similar in size to that found with conscious
perception. Would you:
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a) Report the test as p=.03 and conclude there is subliminal perception for this
method?
b) Note that when a Bonferoni-corrected significance value of .05/5 is used, all
tests are non-significant, and conclude subliminal perception does not exist by any of
these methods?
c) Regard the strength of evidence provided by these data for subliminal
perception produced by Continuous Flash Suppression to be the same regardless of
whether or not four other rather different methods were tested?
4) A theory predicts a difference in reaction time between two conditions. A
previous study finds a significant difference between the conditions of 20 seconds,
with a Cohen’s dz of 0.5. You wish to replicate in your lab. In order to obtain a
conventional power of 80% you run 35 subjects and find a t of 1.0 and a p of .32.
Would you
a) conclude that under the conditions of your replication experiment there is
no effect?
b) conclude that null results are never informative and withhold judgment
about whether there is an effect or not?
c) realise that while 20 seconds is a likely value given the theory being tested,
the difference could in fact be 15 seconds either side of this value and still be
consistent with the theory. You treat the evidence as inconclusive; e.g. your certainty
in the theory might go down modestly from being about 65% to a bit more than 50%,
and so you decide to run more subjects until the evidence more strongly supports the
null over the theory or the theory over the null?
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5) You look up the evidence for a new expensive weight loss pill. Use of the
pill resulted in significant weight loss after 3 months daily ingestion with a beforeafter Cohen’s dz of 1.0 with n=10 subjects giving a p of .01. In addition, you accept
that there are no adverse side effects. Would you:
a) Reject the null hypothesis of no change and buy a 3 month’s supply?
b) Decide 10 subjects does not provide enough evidence to base a decision on
when it comes to taking a drug, withhold judgment for the time being, and help
sponsor a further study?
c) Decide that in a 3-month period you would like to loose between 10-15kg.
In fact, despite the high standardised effect size, the raw mean weight loss in the study
was 2kg. The evidence that the pill uses a mechanism producing 0-10 kg loss (which
you are not interested in) rather than 10-15kg (which you are) is overwhelming. You
have sufficient data to decide not to buy the pill?
We will discuss answers to this quiz below. But first we need to establish what
the rational basis for orthodox and Bayesian statistics consists in and why they can
produce different answers to the above questions.
Rationality
What is it to be rational? One answer is it is having sufficient justification for
one’s beliefs; another is that it is a matter of having subjected one’s beliefs to critical
scrutiny. Popper and others inspired by him took the second option under the name of
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critical rationalism (e.g. Popper, 1963, Miller, 1994). On this view, there is never a
sufficient justification for a given belief because knowledge has no absolute
foundation. Propositions can be provisionally accepted as having survived criticism,
given other propositions those people in the debate are conventionally and
provisionally willing to accept. All we can do is set up (provisional) conventions for
accepting or rejecting propositions. An intuition behind this approach is that irrational
beliefs are just those not subjected to sufficient criticism.
Critical rationalism bears some striking similarities to the orthodox approach
to statistical inference, the Neyman Pearson approach (an approach almost universally
used by users of statistics, but few would know it by that name, or any other). On this
view, statistical inference cannot tell you how confident to be in different hypotheses;
it only gives conventions for behavioural acceptance or rejection of different
hypotheses, which, given a relevant statistical model (which can itself be subjected to
testing), results in pre-set long term error rates being controlled. One cannot say how
justified a particular decision is or how probable a hypothesis is; one cannot give a
number to how much data supports a given hypothesis (i.e. how justified the
hypothesis is, or how much its justification has changed); one can only say that the
decision was made by a decision procedure that in the long run controls error
probabilities (as objective probabilities in the sense of long run frequencies) (see
Dienes, 1008, chapter 3, for a conceptual introduction to this approach; also Oakes,
1986; and Royall, 1997, for why p values do not provide such degrees of support).
Note probability is a long run relative frequency so it does not apply to the truth of
hypotheses, nor even to particular experiments. It is the long run relative frequency of
errors for a given decision procedure. It can be obtained from the tail area of test
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statistics (e.g. tail area of t-distributions), adjusted for factors that affect long run error
rates, like how many other tests are being conducted. These error rates apply to
decision procedures not to individual experiments. An individual experiment is a oneoff event, so it does not determine a unique long-run set of events; but a decision
procedure can in principle be considered to apply over a long run indefinite number of
events (i.e. experiments).
Now consider the other approach to rationality, that it is a matter of having
sufficient justification for one’s beliefs. If we want to assign numerical degrees of
justification (i.e. of belief ) to propositions, what are the rules for logical and
consistent reasoning? Cox (1946; see Sivia & Skilling, 2006) took two minimal
desiderata, namely that
1. If we specify degree of belief in P we have implicitly specified degree of belief in
not-P
2. If we specify degree of belief in P and also specify degree of belief in (Q given P)
then we have implicitly specified degree of belief in (P&Q)
Cox did not assume in advance what form this specification was nor what the
relationships were; just that the relationships existed. Using deductive logic Cox
showed that degrees of belief must follow the axioms of probability if we wish to
accept the above minimal constraints. Thus, if we want to determine by how much we
should revise continuous degrees of belief, we need to make sure our system of
inference obeys the axioms of probability. In my experience, researchers think all the
time in terms of the degree of support data provide for a hypothesis. If they want to
think that way, they should make sure their inferences obey the axioms of probability.
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One version of such continuous degrees of belief are subjective probabilities,
i.e. personal conviction in an opinion (e.g. Howson & Urbach, 2006). One can hone in
on one’s initial personal probabilities by various gambling games (see Dienes, 2008,
chapter four, for an introductory review of these ideas). This can be a useful idea for
how one could have probabilities for different propositions when it is hard to specify
clear and full reasons for why the probabilities must have certain values. It is natural
that people regard the same theory as being more or less plausible, and that
probabilities can be personal. However, when probabilities of different propositions
form part of the inferential procedure we use in deriving conclusions from data then
we need to make sure that the procedure is fair. Thus, there has been an attempt to
specify “objective probabilities” that follow from the informational specification of a
problem (e.g. Jaynes, 2003). This will be a useful way of thinking about probabilities
for evaluating how much data support different hypotheses. In this sense, probabilities
can be normative convictions a person should have given the constraints and
information made explicit in the statement of the problem. In this way, the
probabilities become an objective part of the problem, whose values can be argued
about given the explicit assumptions, and do not depend on any further way on
personal idiosyncrasies. Note these sort of probabilities can be regarded as consistent
with critical rationalism (despite Popper’s aversion to Bayes): The assumptions
defining the problem are without absolute foundation, they are open to criticism, but
can be debated until tentatively accepted. In any case, whatever probabilities one
starts with (entirely subjective personal ones gathered by reaching deep in one’s soul,
or objectively specified ones given stated constraints), Bayesian inference insists that
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one must revise these initial probabilities in the light of data in ways consistent with
the axioms of probability.
In the Bayesian approach, probability applies to the truth of theories (the
relative frequency notion of probability as used in Neyman Pearson statistics does not
apply to theories). Thus we can answer questions about p(H), the probability of a
hypothesis being true (our prior probability), and also p(H|D), the probability of a
hypothesis given data (our posterior probability), neither of which we can do on the
orthodox approach. The probability of obtaining the exact data we got given the
hypothesis is the likelihood. From the axioms of probability, it follows directly that:
Posterior is given by likelihood times prior
From this theorem (Bayes’ theorem) comes the likelihood principle: All
information relevant to inference contained in data is provided by the likelihood (e.g.
Birnbaum, 1962). When we are determining how given data relatively changes the
probability of our different theories, it is only the likelihood that connects the prior to
the posterior.
The likelihood is the probability of obtaining the exact data obtained given a
hypothesis, P(D|H). This is different from a p-value, which is the probability of
obtaining the same data or data more extreme given both a hypothesis and a decision
rule. Thus, a p-value for a t-test is a tail area of the t-distribution (adjusted according
to the decision rule); the corresponding likelihood is the height of the t-distribution at
the point representing the data - not an area and certainly not an area adjusted for the
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decision rule. In orthodox statistics these adjustments must be made because they
accurately reflect the factors that affect long term error rates of a decision procedure.
The likelihood principle may seem a truism; it seems to just follow from the
axioms of probability. But in orthodox statistics, p-values are changed according to
the decision rule: How one decided to stop collecting data; whether or not the test is
post hoc; how many other tests one conducted. None of these factors influence the
likelihood. Thus, orthodox statistics violates the likelihood principle. I will consider
each of these cases because they have been used to argue Bayesian inference must be
wrong, given that we have been trained as researchers to regard these violations of the
likelihood principle to be a normative part of orthodox statistical inference. But these
violations of the likelihood principle also lead to bizarre paradoxes. I will argue that
when the full context of a problem is taken into account, the arguments against Bayes
based on these points fail. On the other hand, where subjective probabilities play a
role in the construction of the likelihood, care does need to be taken in establishing
inter-subjective consensus for Bayesian inferences to be generally acceptable.
The Bayes factor
One form of Bayesian analysis pits one theory against another, say theory1
against theory2. Theory1 could be your pet theory put under test in an experiment;
theory2 could be the null hypothesis, or some other sort of default position. If your
personal probability of theory1 being true before the experiment is P(theory1) and that
for theory2 is P(theory2), then your prior odds in favour of theory1 over theory2 is
P(theory1)/P(theory2). These prior probabilities and prior odds can be entirely
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personal or subjective; there is no reason why people should agree about these before
data are collected. Once data are collected we can calculate the likelihood for each
theory. These likelihoods are things we want people to agree on; thus, any
probabilities that contribute to them should be plausibly or simply determined by the
specification of the theories. The Bayes factor B is the ratio of the likelihoods. From
the axioms of probability,
Posterior odds = B*prior odds
If B is greater than 1 then the data supported your experimental hypothesis
over the null. If B is less than 1, then the data supported the null hypothesis over the
experimental one. If B is about 1, then the experiment was not sensitive (Jeffreys,
1961, suggests Bayes factors above 3 - or below 1/3 - are “substantial”). Note that B
automatically gives a notion of sensitivity; it directly distinguishes data supporting the
null from data uninformative about whether the null or your theory was supported.
Contrast this state of affairs with just relying on p values in significance testing. The
most common mistake people make is believing they can simply take a nonsignificant p-value, and from this alone decide that the null was supported over the
theory. In fact, the Neyman Pearson approach itself proscribes against this. It says one
should calculate power, and only accept the null when power was high. If people
followed the Neyman Pearson approach as it should be done, they would know when
a null result meant one could accept the null and when it meant withholding decision.
Unfortunately, one CAN simply calculate p-values without calculating power, this is
easier, so that’s what people do. In Bayes one does not have the choice: You get the
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full answer whether you want it or not. This is a practical reason for preferring Bayes
over Neyman Pearson. According to this argument, both approaches would work fine
if done correctly; but Bayes forces one to do it correctly and Neyman Pearson
obviously does not. Decades of statisticians admonishing psychologists has not made
them do it properly (see e.g Cohen, 1977, 1994; Harlow, Mulaik, & Steiger, 1997;
Hunter & Schmidt, 2004). Now I wish to consider reasons for preferring Bayes even
if Neyman Pearson is done correctly. And those reasons are based on the ways in
which Neyman Pearson depart from the likelihood principle.
Problems with Neyman Pearson
1) On the Neyman Pearson approach one must specify the “stopping rule” in
advance, i.e. the conditions under which one would stop collecting data. Once those
conditions are met, there is to be no more data collection. Typically this means you
should plan in advance how many subjects you will run (with a power calculation).
You are forbidden from running until you get a significant result – because if you try
you will always succeed, given sufficient time, even if the null is true. Further, one
cannot plan to run 30 subjects, find a p of .06, and then run 10 more, and report the pvalue of .04 SPSS now delivers for the full set of 40 subjects, and declare it
significant at the 5% level. Five percent is an inaccurate reflection of the error rate of
the decision procedure one used (that procedure being: “Run 30 subjects, test, if nonsignificant, run 10 more subjects and test again”). You cannot test your data once at
the .05 level, then run some more subjects, and test again at .05 level. The Type I
error rate is no longer .05 because you gave yourself two chances at declaring
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significance. Remember on the Neyman Pearson approach probabilities are long run
relative frequencies – i.e. the long run properties of your decision procedure, and thus
do not apply to your individual experiment. You will make a Type I error 5% of the
time at the first test; the second test can only increase the percentage of Type I errors.
The significance can thus be never less than .05, no matter how many subjects one
subsequently runs and how strong the evidence seems against the null and no matter
what SPSS tells you the p-value is. Each test must be conducted at a lower
significance level for the overall error rate to be kept at .05. This puts one in an
impossible moral dilemma having tested once at the 5% level if an experiment after
30 subjects yields a p of .06. One cannot reject the null on that number of subjects; yet
one cannot accept it either (no matter what the official rules are, would you accept the
null for a p of .06?). One cannot publish the data; yet one cannot in good heart bin the
data and waste public resources. Bayes avoids this impossible moral dilemma. When
calculating a Bayes factor, it does not matter when you decide to stop running
subjects. You can always run more subjects if you think it will help.
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Figure 1 The importance of the stopping rule for significance testing
Consider the cartoon in Figure 1. Two researchers come to the end of running
40 subjects. One calculates the p-value based on the full set of data without
correction: he had planned to run that many from the start and only test once at the
end of data collection. He gets a significant result and decides to reject the null. The
other researcher tested after 20 subjects, found it non-significant, so tested again at the
end of 40. But he wasn’t cheating: he made the appropriate corrections (see Armitage,
Berry and Mathews, 2002, pp 615-623 for examples of legitimate corrections). Now
on the final test, because of the correction, the result is non-significant. Notice how
the appropriate inference (to accept or reject the null) depends on more than the
likelihood, that is, on more than how likely these precise data are given the null
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hypothesis or theory under test. It depends not just on what the data are but also on
what might have happened, even if it did not. In particular, appropriate inference
depends on if the researchers would have stopped after 20 subjects if it had been
significant – even though it wasn’t, and they didn’t. Notice in the cartoon that if
whether they would have stopped collecting data after 20 subjects, even though they
didn’t, depends on who has the better kung fu, then the mathematically correct result
depends on whose kung fu is better! And if whether they would have stopped
collecting data after 20 subjects depends on who has the strongest unconscious desire
to please the other then the mathematically correct answer depends on whose
unconscious wish to please the other is strongest! This example might seem
deliberately absurd but the point is very real and practical. How many people have
looked at the results some way through testing – how many would have stopped
collecting if the results had been clear enough then? Would you? (Are you sure?)
How many people “top up” with just a few more subjects? I believe the practice to be
very common. As I said, there are ethical problems with not doing so in many cases.
And maybe many people justify it because in their hearts they believe in the
likelihood principle: Surely what subjective intentions are concealed in the mind are
irrelevant to drawing inferences from data; what matters is just what the obtained data
are. The problem is, one cannot believe the likelihood principle and follow Neyman
Pearson techniques. Long term error rates using significance tests are affected by
counterfactuals, even if likelihoods are not.
The Bayes factor behaves differently from p-values as more data are run
(regardless of stopping rule). For a p-value, if the null is true, any value in the interval
0 to 1 is equally likely no matter how much data you collect. For this reason, sooner
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or later you are guaranteed to get a significant result if you run subjects for long
enough. In contrast, as you run more subjects and the null is true, or closer to the truth
than your alternative, the Bayes factor is driven towards zero. You could run an
infinite number of subjects and never have B achieve a given value, e.g. 4. Hence you
can run as many subjects as you like, stopping when you like. Isn’t this what
researchers really want of their inferential statistics? And if this sounds more
sensible, it is because it is literally more rational.
2) On Neyman Pearson, it matters whether you formulated your hypothesis before or
after looking at the data (post hoc vs planned comparisons): Predictions made in
advance of rather than before looking at the data are treated differently. In Bayesian
inference, it does not matter what day of the week you thought of your theory. The
evidence for your theory is just as strong regardless of its timing relative to the data.
This is because the likelihood is unaffected by the time the data were collected. Note
the likelihood principle contradicts not only Neyman Pearson on this point, but also
the advice of e.g. Popper (1963) and Lakatos (1978), who valued the novelty of
predictions (though Lakatos later gave up the importance of temporal novelty,
Lakatos & Feyerabend, 1999, pp 109-112). Kerr (1998) also criticised the practice of
HARKing: Hypothesising After the Results are Known. Indeed, novel predictions are
often impressive as support for a theory. But this may be because in making novel
predictions the choice of auxiliary hypotheses (i.e. those hypotheses implicitly or
explicitly used in connecting theory to specific predictions) was fair and simple. Post
hoc fitting can involve preference (for no good reason) for one auxiliary over many
others of at least equal plausibility. Thus, a careful consideration of the reason for
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postulating different auxiliaries should render novelty irrelevant as a factor
determining the evidential value of data. That is, the issue is not the timing of the data
per se, but the priori probability of the hypotheses involved. And prior probability is
something Bayes is uniquely well equipped to deal with!
Consider an example that has been used as a counter argument to the
likelihood principle. I have a pack of cards face down. I lift up the top card. It is a six
of hearts. Call the hypothesis that the pack is a standard pack of playing cards “Hs”.
Call the hypothesis that all cards in the pack are six of hearts “H6h”. The likelihood of
drawing a six of hearts given the pack is a standard pack is 1/52. So L(Hs) = 1/52. The
likelihood of drawing a six of hearts given the hypothesis that the pack consists only
of 52 six of hearts is 1. So L(H6h) = 1. So the Bayes factor in favour of the pack
consisting only of sixes of hearts versus being a standard pack is 52. If you saw a pack
of cards face down your initial prediction would be that they are a standard pack of
playing cards. The drawing of a single six of hearts would not change your mind.
Surely the hypothesis that they are all sixes of hearts is purely post hoc, a mindless
fitting of the data! If Bayesian statistics support the post hoc theory over the theory
that it is a standard pack of cards, surely something is wrong with Bayes! If someone
could predict in advance that the pack was all sixes of hearts that would be one thing;
but that is precisely the point, they wouldn’t. By missing out on the importance of
what can be predicted in advance, does not the likelihood principle fail scientists?
Remember the likelihood principle follows from the axioms of probability.
The axioms of probability are by their nature almost self-evident assumptions. They
will not lead to wrong conclusions. Indeed, in this case, if we put the problem in its
full context, we see the Bayesian answers are very sensible (see Royall, 1997, p 13,
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for the following argument). Before we pick up the card there are 52 hypotheses that
the pack is all of one sort of card – the hypothesis that it is all aces of hearts, all twos
of hearts, and so on. Call the probability that one or other of these hypotheses is true
π. So the probability of any one of them being true is π /52, assuming we hold them to
all have equal probability. Once we have observed the six of hearts, all these
hypotheses go to zero, except for H6h. The probability of that hypothesis goes to π.
The probability that the whole pack is all of one suit remains the same – it is still π..
The probability that it is a standard pack of cards remains the same. The axioms of
probability and their consequence, Bayes theorem, give us just the right answer. There
is no need to introduce an extra concern with ability to predict in advance; that
concern is already implicitly covered in the Bayesian approach. It is not the ability to
predict in advance per se that is important; that ability is just an (imperfect) indicator
of the prior probability of relevant hypotheses. The data provide stronger or weaker
evidence for different hypotheses regardless of the day of the week the data were
collected. When performing Bayesian inference there is no need to adjust for the
timing of predictions per se. Indeed, it would be paradoxical to do so: Adjusting
conclusions according to when the hypothesis was thought of would introduce
irrelevancies into inference, leading to one conclusion on Tuesday and another on
Wednesday for the same data and hypotheses.
3) On Neyman Pearson you must correct for how many tests you conduct in total.
For example, if you ran 100 correlations and 4 were just significant at the 5% level,
researchers would not try to interpret those significant results. On Bayes, it does not
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matter how many other statistical hypotheses you investigated. All that matters is the
data relevant to each hypothesis under investigation. Consider an example from
Dienes (2008) to first pump your intuitions along Neyman Pearson lines; and then, as
above, we will see how the axioms of probability do indeed give us the sensible
answer, and hopefully your intuitions come to side with Bayes. The example is about
searching for the reincarnation of a recently departed lama by a search committee set
up by the Tibetan Government-in-exile. The lama’s walking stick is put together with
a collection of 20 others. Piloting at a local school shows each stick is picked equally
often by children in general. We have now set up a test with a known and acceptable
test-wise Type I error probability, i.e. controlled to be less than 5% for each individual
test. If a given candidate picks the stick, p = 1/21 < .05. Various omens narrows the
search down to 21 candidate children. They are all tested and one of these passes the
test. Can the monks conclude that he is the reincarnation?
The Neyman Pearson aficionado says, “No! With 21 tests family-wise error
rate = 1 – (20/21)21 = 0.64. This is unacceptably high. Of course if you test enough
children, sooner or later one of them will pass the test. That proves nothing. As Bayes
does not correct for multiple testing, surely the Bayesian approach must be wrong!”
The Bayesian argues like this. “Assume the reincarnation will definitely
choose the stick. If the 10th child chose the stick, the Bayes factor B for the 10th child
= 21. Whatever your prior odds that the 10th child was the reincarnation they should
be increased by a factor of 21.”
The Neyman Pearson aficionado cannot contain himself. “Ha! You have
manufactured evidence out of thin air! By ignoring the issue of multiple testing you
have found strong evidence in favour of a child being the reincarnation just because
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you tested many children!” (see e.g. Mayo, 1996, 2004, for this argument against
Bayes).
The Bayesian patiently continues with an argument similar to the one in the
previous section, “The likelihood of any child who did not choose the stick is 0. Call
the prior probability that one or other of these children was the reincarnation π. If
prior probabilities for each individual child equal, prior probability that any one is the
reincarnation = π/21. After data, twenty of these go to zero. One goes to 21 * π/21 =
π. They still sum to π. If you were convinced before collecting the data that the null
was false you can pick the reincarnation with confidence; conversely if you were
highly confident in the null beforehand you should be every bit as confident
afterwards. And this is just as it should be!”
The Bayesian answer does not need to correct for multiple testing because
if an answer is already right it does not need to be corrected. Once one takes into
account the full context, the axioms of probability lead to sensible answers, just as one
would expect. As I point out in Dienes (2008), a family of 20 tests in which one is
significant at the .05 level typically leads one by Bayesian reasoning to have MORE
confidence in the family-wise null hypothesis that ‘all nulls are true’ while decreasing
one’s confidence in the one null that was significant. And this fits one’s intuitions that
if evidence went against the null in 4 out of 100 correlations, one would be more
likely to think the complete null is true, but still find oneself more likely to reject the
null for the four specific cases. If all 100 correlations bore on a theory that predicted
non-zero correlations in all cases, then one’s confidence in that theory would typically
decrease by a Bayesian analysis.
23
The moral is that in assessing the evidence for or against a theory, one should
take into account ALL the evidence relevant to the theory, and not cherry pick the
cases that seem to support it. Cherry picking is wrong on all statistical approaches. A
large number of results showing evidence for the null against a theory still count as
against the theory, even if a few of the effects the theory predicted are supported. And
Bayes gives one the apparatus for combining such evidence to come to an overall
conclusion, an apparatus missing in Neyman Pearson. Thus, it is Bayes, rather than
Neyman Pearson, most likely to demand of researchers they draw appropriate
conclusions from a body of relevant data involving multiple testing. Bayes factors
close to zero count as evidence against the theory; in practice, non-significant values
are either left to count or not depending on whim.
4) Finally, because the likelihood tells one by how much to change confidence, and
because significance testing violates the likelihood principle, the Neyman Pearson
approach does not tell one how to change confidence. A significant difference (i.e.
accepting the experimental hypothesis on Neyman Pearson) can mean one should
reduce one’s confidence in a theory that predicted the difference…. and a null result
can mean confidence in theory should increase (see Dienes 2008, chapter four, and
below for examples). Neyman Pearson does not tell you how justification for a theory
has changed. No matter what anyone tells you, Neyman-Pearson analyses do not
directly license assigning any degree of confidence to one conclusion rather than
another. If you are interested in the extent to which you should change your
confidence in a theory, you must do a Bayesian analysis. Consider for example if a
particular theory has often predicted effects which turn out to be about 100 ms in size.
24
In a new prediction in a domain where one would expect the same size effect, a
significant effect of 5 ms is obtained. This may well count strongly against the theory.
To summarise the arguments of this section, key differences between the
approaches that follow from the likelihood principle are shown in Table 1.
Table 1
Contrasts between Bayesian and orthodox statistics following from whether or not the
likelihood principle is obeyed. Because orthodox statistics are sensitive to the factors
listed, contrary to the likelihood principle, in each case different people with the same
data and hypothesis may come to opposite conclusions.
Orthodox: Could
this factor affect
whether or not a
null hypothesis is
rejected?
Bayes: Does this
factor ever affect
the support of data
for a hypothesis?
When you initially
intended to stop
running
participants
Yes
Whether or not you
predicted a result in
advance of
obtaining it
Yes
The number of tests
that can be grouped
in a family
No. You can
always run more
participants to
acquire clearer
evidence if you
wish
No. No one need
ever try to second
guess which really
came first.
No. Please test as
many different
hypotheses as is
worth your time –
but you must take
into account all
evidence relevant
to a theory.
Your answers to the quiz
Yes
25
Now consider the situations we started with. What are your intuitions now? In
all cases, answer c) is the Bayesian answer.
For question 1, I suspect a majority of researchers have at some time taken a)
as their answer in similar cases. They have Bayesian intuitions, but use them with the
wrong tools, the only tools apparently available, and tools inappropriate for actually
cashing out the intuition. Choice a) is also the answer one might pick by thinking with
a meta-analytic mind set, but use of meta-analysis here is complicated by the fact the
stopping rule was conditional upon obtaining a significant finding. Thus, the correct
orthodox answer is to regard the data non-significant, as in b). Power may be low, but
in effect one committed to that level of Type II error in planning the study. Answer c)
spells out the intuition, and Bayes provides the tools for implementing it.
For question 2, again I suspect many people have decided a) in similar
circumstances, because of the Bayesian intuitions in c), and so used the wrong tools
for the right reasons. One suspects in many papers the introduction was written
entirely in the light of the results. We implicitly accept this as good practice, indeed
train our students to do likewise for the sake of the poor reader of our paper. But b) is
the correct answer based on the Neyman Pearson approach, and maybe your
conscience told you so. But should you be worrying about what might be murky –
which really came first, data or hypothesis? – or, rather, about what really matters,
whether the predictions really follow from a substantial theory in a clear simple way?
For question 3, practice may vary depending on whether the author is a
believer or sceptic in subliminal perception. After all, there is no strict standard about
what counts as a “family” for the sake of multiple testing. There is a pull between
accepting the intuition in c) that surely there is evidence for this method, and the
26
realisation that more tests means more opportunities for inferential mistakes. But one
should not confuse strength of evidence with the probability of obtaining it (Royall,
1997). Evidence is evidence even if, as one increases the circle of what tests are in the
“family”, the probability that some of the evidence will be misleading increases.
For question 4, many researchers may conclude a), and indeed feel that by
taking power into account they are morally ahead of the pack of typical researchers
who ignore power. Those schooled in Fisherian intuitions may choose b). A Bayesian
analysis forces one to consider the range of effect sizes consistent with a theory. As
soon as one considers this question, whether as a Bayesian or not, it will become
apparent that the effect obtained in a previous study does not define the lowest effect
size one is interested in. Thus, even in studies that do take power into account, likely
they do not consider a minimally interesting effect, and likely they use rather low
power (80%) – rather low that is, for obtaining evidence that could substantially
favour a null hypothesis over the theory of interest. Because orthodox methods are not
based on how persuasive you should find evidence, they often allow conclusions that
in fact should not be persuasive. And without doing a Bayesian analysis, you have no
idea how persuasive they should be.
Question 5 again illustrates a case where orthodox statistics could produce the
same answer as Bayes: One could calculate a confidence interval on raw weight loss
and see that it excludes the values one is interested in. In this case, the advantage of
the Bayesian approach is that it forces you to consider what range of effects you are
really interested in. It forces you to take into account that which is inferentially
relevant. Orthodox statistics do not (cf e.g. Kirsch, 2009).
27
Now dear reader and fellow journey person: Are you a closet – or indeed, out Bayesian? What inferential methods seem rational to you? If you want some pointers
in bringing our your inner Bayesian, read on!
Bayes factors in practice
The last example illustrates the importance of considering the size of an effect
in using it to evaluate a theory. Effect size is very important in the Neyman Pearson
approach: One must specify the sort of effect one predicts in order to calculate power.
On the other hand, Fisherian significance testing leads people to ignore effect sizes.
People have followed Fisher’s way, while paying lip service to effect sizes. By
contrast, to calculate a Bayes factor one must specify what sort of effect sizes the
theory predicts. Bayes forces people to think about effect size.
Nowadays many journals require one mention standardised effect sizes for
each inferential test. But has this led people to either calculate power or use
confidence intervals? When confidence intervals are given, do authors argue what size
effect would be predicted by the theory and indicate whether the confidence interval
includes or excludes effects interesting on the theory? That is what people should be
doing (particularly when interpreting null results), but they do not. People may
mention effect sizes but they don’t seem to do anything with this information other
than state what they are. And when power is calculated, it is often calculated for “a
Cohen’s d of 0.5” because, the authors say, they are interested in “medium sized”
effects. This is a step above not calculating power at all. But it is still an unthinking
mechanical response when we could be doing so much more. What size effect does
28
the literature suggest is interesting for this particular domain? Rather than plucking
“0.5” out of thin air we should get to know the data of our field. Often the already
existing published data in our field allow us to say in raw units just what sort of effect
size a theory deals with. Sometimes one really does not know; then using wild
speculations – like a Cohen’s d of 0.5 because that is the sort of effect psychologists
in general often deal with – may be the best one can do. But often it will be not far off
the least one can do. (For arguments for the frequent relevance of raw rather than
standardised effect sizes, see Baguley, 2009; Ziliak & McCloskey, 2008.)
It is easy to see why psychologists, and other users of statistics, became
Fisherian, i.e. just reported p values and did not consider effect sizes in an inferential
way. Reporting p-values requires minimal thought. While that response might sound
cynical, it is indeed an advantage of p-values: The result requires minimal
assumptions. For this reason, I suspect p-values may be interesting as a side line when
reporting many tests. It is the result one gets with minimal assumptions. Nonetheless,
this approach has done enough mischief we really have to change. Unless one
incorporates effect sizes into one’s inferences, dealing with null results is impossible.
How predictably are null results handled without thought, leaving the reader
genuinely uninformed about the status of some theory or treatment or danger,
whatever the confident assertions of the author. The data has been collected to inform
the reader, but the reader is not getting informed. Untold damage has been done to
many fields because of this lapse.
Despite some attempts to encourage researchers to use confidence intervals
their use has not taken off (Fidler et al, 2004). Confidence intervals of some sort
would deal with many problems (either confidence, credibility or likelihood intervals;
29
see Dienes 2008 for definitions and comparison). But an approach that has something
of a flavour of a t or other inferential test might be taken up more easily. Further,
confidence intervals themselves have all the problems enumerated above for Neyman
Pearson inference in general (unlike credibility or likelihood intervals). So here I urge
the use of the Bayes factor.
To calculate a Bayes factor in support of a theory (relative to say the null
hypothesis), one has to specify what the probability of different effect sizes are, given
the theory. In a sense this is not new: We should have been specifying predicted effect
sizes anyway. And if we are going to do it, Bayes gives us the apparatus to flexibly
deal with different degrees of uncertainty regarding the predicted effect size.
For example consider a theory that predicts a difference will be in one
direction. A minimally informative distribution, containing only the information that
the difference is positive, is to say all positive differences are equally likely between
zero and the maximum difference allowed by the scale used. Such a vague prediction
works against finding evidence in favour of the theory. Generally we can do better
than that. For example, it seems rather unlikely that the difference will be as large as
the maximum allowed by the scale: That requires all subjects in one condition were at
one extreme of the scale, and all subjects in the other condition were at the other
extreme. In general, smaller effects are more likely than the larger ones. This can be
modelled by one half of a normal distribution, with its mode at zero, and its tail
dropping away in the positive direction. But how to scale the rate of drop? If similar
sorts of effects as those predicted in the past have been on the order of a 5%
difference between conditions in classification accuracy, then we can set the standard
deviation of the normal to be 5%. This distribution would imply that smaller effects
30
are more likely than bigger ones; and that effects bigger than about 10% are unlikely.
If an argument based on the existing literature makes these assumptions plausible,
then the Bayes factor based on those assumptions is one that can be accepted
generally. To play with how assumptions affect the Bayes factor, see the web site for
Dienes (2008) for flash programs and Matlab code for the Bayes factor, and Baguley
and Kaye (in press) for corresponding R code; and Rouder et al (2009) for another
Bayes factor calculator. Bayes factors vary according to assumptions, but they cannot
be made to vary ad lib: Often a wide range of assumptions leads to essentially the
same conclusion.
The results will depend on the assumptions about likely effect sizes given the
theory. But notice these assumptions are open to public scrutiny. They can be debated
and other assumptions used according to the debate. In this sense Bayes is objective.
In Neyman Pearson inference, the inference depends on how the experimenter
decided to stop and when he thought of the hypothesis. These concerns are not open
to public scrutiny and may not even be known by the author. All assumptions relevant
to Bayesian inference are available to critical debate because they are part of the
public problem situation itself and not locked in the head of researchers. Strangely,
starting from subjective probabilities leads to more objective conclusions than starting
with objective probabilities (as relative frequencies)!
A statistical philosophy would not have persisted so long if it did not produce
tenable conclusions in many cases. And indeed, in many cases Bayesian and orthodox
answers agree, which is reassuring. For example, Dienes et al (2009) investigated
possible correlates of hypnotic suggestibility. Previous research had found that a task
measuring cognitive inhibition correlated about .40 with hypnotic suggestibility. With
31
180 participants, Dienes et al found a correlation of -.05, with a 95% confidence
interval of [-.20. .09]. The null hypothesis was accepted. We can use the software
from Dienes (2008) to calculate a Bayes factor by Fisher-z transforming the
correlation so that its sampling distribution becomes normal. Based on the previous
study alone, a positive correlation would be expected of around .40. However, in light
of the larger literature, one can in addition say that smaller correlations are more
likely than larger ones: Replicable correlates of hypnotic suggestibility, such as they
are, tend to have values closer to .20 or .10 rather than .40 or .50 over many studies
(e.g. Kirsch & Council, 1992). Thus, a reasonable distribution of the population
(Fisher-z transformed) correlation value is a half normal with its mode at 0 and an SD
of .25, effectively ruling out correlations greater than about .50, and allowing any
value between 0 and .50, with smaller values more likely. This is a judgment based on
knowledge of the literature, and it is of course open to debate. The assumptions are
laid bare for anyone to consider. The obtained (Fisher-z transformed) correlation of .05 has a standard error of 1/squareroot(N-3) = .075. Feeding these numbers into the
online software, the Bayes factor is .18, i.e. substantial evidence for the null
hypothesis over the alternative considered.
Note that this does not amount to accepting the null in any absolute sense;
there is just more evidence for the null than the alternative considered. If the
alternative was a normal centred on zero with a standard deviation of .10 (i.e. if one
expected possible correlations between 0 and about .20 in either direction) the Bayes
factor is .69, which barely changes one’s prior odds at all: The data do not
discriminate the null hypothesis from the hypothesis of a range of small correlations.
And of course, this is just as it should be. Finally, one can compare the evidence for a
32
correlation of zero to the specific value of .40 obtained in the prior study (the
likelihoods for 0 and .40 can be obtained from the corresponding heights in normal
tables). The Bayes factor is .00 to two decimal places, indicating exceptionally strong
evidence for a correlation of zero rather than the previously obtained value of .40. The
data are sufficiently clear that the precise statistical philosophy does not change the
ultimate conclusions, even for a null result. But using Bayes does draw one’s attention
to the amount of evidence for one hypothesis relative to a specified other. Orthodox
hypothesis testing does not: One accepts or rejects the null outright.
The specification of what the theory predicts of course depends on the theory.
Bayesians tend at heart to be against mechanical unthinking procedures, and this is
both a strength and a weakness. It is ultimately a strength, though it makes it harder
for the procedures to be adopted generally. Consider a psychologist who decides to
use a conventional expected medium effect size (Cohen’s d) of 0.5 to scale his
distribution of the predicted effect, because medium effect sizes are typical for
psychologists. He uses a distribution symmetric around zero, dropping off in either
direction, scaled by a Cohen’s d of 0.5 (see Rouder et al 2009 for a Bayes factor
calculator that works given these assumptions). These may be excellent assumptions
to make, but they should not be made as an unthinking default. Another person may
convincingly argue that one can be more specific: Based on past literature, this theory
typically deals with raw effects of 100 ms. Cohen’s d may change according to what
other factors and covariates are in the experiment, but one expects a raw effect of
about 100ms in a certain direction. Further, the person might argue that an effect size
of say 10ms would actually argue against the theory being the relevant explanation,
because the effect would be too small. (It is not so far fetched to think psychologists
33
could say something this exact about effect sizes based on their theories: Consider the
difference between pop out and serial search in the attention literature.) Now we could
model the predictions of the theory by a normal centred on 100, and we would need to
debate its standard deviation. The less information we have, the more we spread the
distribution out until limited by known constraints that mean it cannot be spread
further (e.g. maybe we want the probability of effects less than 20ms to be very
small). The process of making these arguments means getting to know one’s theories
and the existing data.
In one sense Orthodox and Bayesian answers will never contradict each other
because they answer entirely different questions (Royall, 1997). But a Bayes factor
can indicate more support for the null hypothesis than a theory that predicts a nonzero
effect when significance testing indicates one should reject the null. And vice versa, a
Bayes factor can indicate more support for a theory that predicts a nonzero effect than
the null hypothesis when a result is non-significant. Because the distribution of effects
predicted by a theory depends on the theory, no firm rules can be given for when
orthodox and Bayesian answers will differ in this respect. It all depends on the theory
considered (cf Berger, 2003). Here we consider some hypothetical examples.
Consider the theory that making prejudice between ethnic groups can be
reduced by making both racial groups part of the same in-group. A manipulation for
reducing prejudice following this idea could consist of imagining being members of
the same sports team. A control group could consists of imagining playing a sport
with no mention of the ethnic group. A post-manipulation mean difference in
prejudice (in the right direction) is obtained with 30 participants of x raw units, equal
to the standard error of difference; i.e. a non-significant t value of 1.00 is obtained.
34
What follows from this null result? Should one reduce one’s confidence in the theory
(assuming the experiment is regarded as well designed)? It depends. Let us say in
previous research, instead of imagining the scenario, participants actually engaged in
a common activity. A reduction in prejudice on the same scale was obtained of 2x. It
seems unlikely that imagination would reduce prejudice by more than the real thing. If
smaller effects are regarded as more likely than larger effects in general, then we may
model predictions by half a normal, with its mode on zero, and a standard deviation of
x units. In this case, the Bayes factor is 1.38. That is the data are essentially
uninformative but if anything we should more confident in the theory after getting
these null results. It would be a tragic mistake to reject the usefulness of imagination
treatments for prejudice based on this experiment. Indeed, even if the mean difference
had been exactly zero, the Bayes factor is 0.71, that is, one’s confidence in the theory
relative the null should be barely altered. More strongly, even if the mean difference
had been x in the wrong direction, the Bayes factor is still 0.43. This does not count as
substantial evidence against the theory by Jeffreys’ (1961) suggested convention of 3
(or a 1/3) for indicating substantial evidence; and indeed if one felt strongly confident
of the theory before collecting the data, one could normatively still be very confident
afterwards.
Determining predicted effect sizes is hard if a motivation for a study is simply
“I wonder what would happen if…”. One can only predict effect sizes if a motivation
is given for the study that relates to previous work. And the more previous work it
relates to, the more informed the prediction of effect sizes can be. Thus, a Bayesian
analysis puts pressure on formulating general theories. The more one can specify a
mechanism for an effect, the more one can, by reference to past work involving the
35
same putative general mechanism, pin down the expected effect size. And the more
one can pin down an expected effect size by reference to other research, the more
strongly the data can in principle support one’s theory, or else falsify it. This must be
good for theory development. For example, consider obtaining a t-value of 2, a raw
mean difference of x, leading to rejection of the null by orthodox statistics. If the
experiment was not based on any theory at all, and not related to any past data or
expectations, the vaguest prediction is that the difference should be between the
extremes possible on the scale, e.g. plus and minus 10x. The Bayes factor is 0.46,
marginally counting against the vague expectation of some difference. But if theory
led one to predict a difference of around x, and lying between 0 and 2x, we could
model the prediction of the theory as a normal with mean x and standard deviation
x/2. Now the Bayes factor is 5, strongly supporting the theory. That is, the more
researchers can make reasonably precise predictions, the more Bayes can reward
them. (And if they do so with implausible assumptions, surely other researchers will
correct them, and argue for more reasonable ways of applying the theory, leading to
useful debate on plausible auxiliary hypotheses to link theory to data.)
In the development of new paradigms, where there may not be past data to
refer to, pilot studies can be done on the basic effect to scale the expected size of
manipulations of the effect in order to calculate a Bayes factor (as is done in Dienes,
Baddeley, & Jansari, submitted).
Weaknesses of the Bayesian approach
The strengths of Bayesian analyses are also its weaknesses:
36
1. Calculating a Bayes factor depends on answering the following question about
which there may be disagreement: What way of assigning probability distributions of
effect sizes as predicted by theories would be accepted by protagonists on all sides of
a debate?
Answering this question might take some arguing. But isn’t this just the sort of
argument that psychology has been missing out on and could really do with (cf Meehl,
1967)? People would really have to get to know their data and their theories better to
argue what range of effect sizes their theory predicts. This will take effort compared
to simply calculating p-values. The very effort of calculating Bayes factors will have a
desirable consequence: People will think carefully about what specific (probably onedegree-of-freedom) contrasts actually address the key theoretical questions of the
research, and people will not churn out e.g. all the effects of an ANOVA just because
they can. Results sections will become focused, concise and more persuasive. But to
begin with, psychologists may start using Bayes factors only to support key
conclusions, especially based on null results, in papers otherwise based on extensive
orthodox statistics. Of course, it would have to be done that way initially because
editors and reviewers expect orthodox statistics. And it would in any case be good to
explore the use of Bayes factors gradually. Once Bayes factors become part of the
familiar tool box of researchers, their proper use can be considered in the light of that
experience.
An alternative response to the problem of assigning a probability distribution
to effect sizes is to not take on the full Bayesian apparatus: One CAN just report
likelihoods for the simple hypotheses that the population value is 1, 1.1, ….etc (e.g.
37
consider comparing the likelihood of a correlation of zero with a correlation of .40 in
the example above). This is “theory free” in the sense that no prior probabilities are
needed for these different hypotheses (see Blume, in press; Dienes, 2008, chapter five;
Royall, 1997). This procedure results in a likelihood interval, similar to confidence
interval (though one that follows the likelihood principle). The “likelihood approach”
has the advantage of not committing to an objective or subjective notion of
probability, and not worrying about precisely how to specify prior distributions, while
committing to the likelihood principle. On the other hand, if a probability distribution
over effect sizes can be agreed on, the full use of Bayes can be obtained (Jaynes,
2003). In particular, one can average out nuisance parameters, and assign relative
degrees of support to different theories each consistent with a range of effect sizes (for
example, the null hypothesis need not be just the hypothesis of zero, but the range of
values too small to be support for a theory).
2. Bayesian procedures, because they are not concerned with long term frequencies,
are not guaranteed to control Type I and type II error probabilities (Mayo, 1996).
Royall (1997) showed how the probability of making certain errors with a
likelihood ratio – or Bayes factor - can be calculated in advance. In particular, for a
planned number of subjects, one can determine the probability that the evidence will
be weak (Bayes factor close to 1) or misleading (Bayes factor in wrong direction).
These error probabilities have interesting properties compared to Type I and II error
rates: No matter how many subjects one runs, Type I error is always the same,
typically 5%. But for Bayes factors, the more subjects one runs, the smaller the
probability of weak or misleading evidence. Further, these probabilities decrease as
38
one runs more subjects no matter what one’s stopping rule. One can always decide to
run some more subjects to firm up the evidence.
Ultimately, however, the issue is about what is more important to us: To use a
procedure with known long term error rates or to know the degree of support for our
theory (the amount by which we should change our conviction in a theory)? If we
want to know the degree of evidence or support for our theory, we are being irrational
in relying on orthodox statistics.
Conclusion
I suggest that the arguments for Bayes are sufficiently compelling, even if not
completely persuasive, that psychologists should be aware of the debates at the logical
foundations of their statistics and make an informed choice between approaches for
particular research questions. The choice is not just academic; it would profoundly
affect what we actually do as researchers.
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