Warning Signs in Experimental Design and Interpretation
When an experimental study states "The group with treatment X had
significantly less disease (p = 1%)", many people interpret
this statement as being equivalent to "there is a 99% chance that
if I do treatment X it will prevent disease." This essay explains why these
statements are not equivalent. For such an experiment, all
of the following are possible:
 X is in fact an effective treatment as claimed.
 X is only effective for some people, but not for me, because I am different
in a way that the experiment failed to distinguish.
 X is ineffective, and only looked effective due to random chance.
 X is ineffective because of a systematic flaw in the experiment.
 X is ineffective and the experimenters and/or reader misinterpreted the results
to say that it is.
There is no way to know for sure
which possibility holds, but there are
warning signs that can dilute
the credibility of an experiment. In Part I we look at warning signs
in the design of an experiment that can render it uninformative; in
Part II at warning signs in the interpretation of an experiment that
can lead the reader to give it more credibility than it deserves.
The presence of any one warning sign does not invalidate a study  there
certainly are valid and convincing studies that are not randomized,
for example  but the more warning signs the more skeptical you should be.
Part I: Common Warning Signs in Experimental Design
The most reliable experiment to evaluate a medical treatment is a
randomized
controlled trial, in which a population is randomly divided into a
test group, which receives the
treatment, and a control group, which
does not.
Why are controls important? Because you want a fair comparison. If
you choose subjects who are unusually healthy and give them a
treatment, you may well get unusually positive results, but it won't
tell you much about the treatment. You have to think of all the
variables that must be controlled for: temperature, pressure, age of
subjects, prior history of disease, etc, and make sure that your
subjects and your controls are balanced on these variables. You might
think that in some cases you can use historical values: in the general
population, x% are prone to get disease D, and they recover in y days
on average. Using such historical figures is fraught with danger,
because you don't know how your population of subjects or your
experimental conditions differ from the historical norms. It is far
safer to use a real control group, as well as a test group. As
Geneticist Gerald Fink (quoted by Natalie Angier) says "In my life as a scientist,
the thing I worry about the most is, What are the right
controls? You send a paper off for publication, and you're
stricken with doubt: Did I do it? Did I use the right controls?"
How do you achieve a good balance between the test and control group?
One good way is to randomize the subjects. You can do this by
randomly assigning all the subjects to one group or the other, or by
first stratifying them into similar subsets, and then randomly
assigning members from each subset into the test and control groups.
It wouldn't do for the experimenter to assign subjects to one group or
the other after having met the subjects; the experimenter might
(consciously or unconsciously) assign healthier patients to one
group.
In some cases, you can assign all subjects to both groups: in
psychology experiments that measure things like reaction time, you can
every subject try every experimental condition (in randomized order),
because there is little or no influence between each trial.
Obviously, you can't have subjects try every possibility on things
like cardiac operations: you can only choose one option for each
subject.
Of course there are situations where you
can't use a randomized controlled trial. You can't ethically test the
effects of cigarettes by requiring a control group to smoke. In such
situations, you make do with nonrandomized studies, and there are
various statistical techniques for dealing with the situation. But if
you see a published study that could have used a randomized controlled
trial and didn't, that's a warning sign that something may be wrong.
A
blind study is one where the subjects
don't know what group they are in. A
doubleblind study is one where the
experimenters don't know either. Why is this important? We know there is a
placebo
effect wherein patients do better when they are told they are receiving
a treatment: the patients' expectations play a role in their recovery. To
make sure we are studying the effect of the treatment itself and not the
patients' expectations, it is better to give all patients the same expectation.
So we tell them, for example, "take this pill, it might be experimental drug X
or it might be a sugar pill." The doubleblind part is important because
we don't want the experimenters to subconsciously tip off the subjects as to
what group they are in, nor to treat one group differently than the other, nor
to analyze the results differently.
A wellstructured randomized controlled trial eliminates systematic biases, but
is still open to random variations. It is always possible that by random chance,
all the really healthy subjects get assigned to the test group and all the sick
subjects get assigned to the control group, thereby making a worthless treatment
look good. Since we can't eliminate this possibility, statisticians
develop a way to measure its likelihood. When we say "the treatment is
effective with statistical significance
p=1%" it means that if there were no
difference between the treatment group and the control group, we would expect to
see results like this (favoring the treatment group) 1% of the time, just
because of the randomized assignment of subjects to one group or the
other. The chances go up if there are too few subjects, relative to the
measurements being taken.
Psychologist Seth Roberts, who is wellknown for experiments with N=1
subject (himself) points out that it is also possible to make the
mistake of having too many subjects  wasting time trying to get
confirmation with a large experiment when you should be doing more
exploration with smaller experiments to get better ideas that can then
be confirmed later. He is quite right that this is a potential
problem, and he may well be right that more scientists, in their daily
scientific lives, make the mistake of too many subjects than too few
subjects. Many of the other points in this essay are also like that:
perhaps scientists are too cautious about making the leap from
correlation to causation. However, when it comes time for a reader to
evaluate a published study, we are doing a different task than a
scientist trying to come up with an idea, and it is a warning
sign when there are too few subjects.
Alf Landon
In 1936
Literary Digest magazine polled 10 million people and predicted
that Alf Landon would win the election for president with 57% of the popular
vote. With 10 million responses they certainly did not make the "too few
subjects" mistake, but nobody remembers president Landon because he in fact lost
46 of 48 states to Franklin Delano Roosevelt, the
32nd president. Where did
Literary Digest go wrong? They got
their subjects from three sources: their own readers, automobile registrations,
and telephone subscribers. But in 1936, as the country emerged from the
great depression, many people could not afford literary magazines, nor cars, nor
telephones, and those who could not were more likely to vote for
Roosevelt. Even today, when phone ownership is much closer to universal,
it is difficult to get a truly representative sample of voters. Call a
home number during the day, and you get mostly people who don't work.
Since there are legal restrictions on calling cell phone numbers for polls, you will
underweight the younger voters who tend to prefer cell phones. Pollsters
have ways for balancing out these biases, but the sample will never be
completely unbiased.
As another example, many psychology experiments are run on volunteer college
students. Often an experimenter gets a result from such an experiment and
claims it is valid across all people, but later finds out that the result only
holds for (a) people roughly 20 years old or (b) people with the skills
and dedication necessary to be a college student or (c) the type of people who
like to volunteer for things.
Even a careful study can end up measuring the wrong thing. You do a study
that you believe shows that treatment X is effective in relieving stress, and in
fact it turns out that it is only effective against the artificial stressful
situation you set up in the lab, but not for real stress in the real
world. Or, you treat different plots of crops with different fertilizers
and believe that the fertilizer used in plot #4 is most effective, when actually
wind and water seepage have pushed all the fertilizer south by one plot, and
really the fertilizer used in plot #3 is the effective one.
Sometimes experimenters deceptively ask the question they want answered, not the
most useful question. In 1987, John Cannell
surveyed
the results of school testing and found that 50 out of 50 US states reported
their children were above average. He called this the "Lake Woebegone
Effect." How was it achieved? It turns out that when a school
district or state contracts to have its students take a standardized test, they
also purchase rights to the scores of a "comparison group," and it appears that
test vendors are competing in part on just how low a comparison group they can
offer.
As an experimenter, the first thing you should do after collecting
your data is to
look at it. Plot the data. Calculate means
and standard deviations. Are there any
outliers? If so, are they valid measurements, or indications of some error
in data collection or recording?
Is the data normally distributed? If not, make sure you don't use a
statistical test that relies heavily on an assumption of normality.
Is the data linear? If not, don't run a linear regression.
Are the data points independent? For example, did you take 100
measurements from 100 different subjects, or 10 measurements, one per day,
for 10 different subjects? If they are not independent, make sure you use
a test that recognizes that.
A recent
article
in London's
Sunday Times reported that
clusters of cancer centered around seven different mobile telephone masts,
raising the concern that mobile phone radiation might cause cancer.
However, there are 47,000 mobile phone masts in England. The article was titled
Cancer clusters at phone masts but for all the details it contains it
could just as well have been titled
Cell phone
masts prevent cancer clusters 99.985% of the time. It is certainly
legitimate to be concerned about these seven cancer clusters, but before
concluding that cell phones have anything to do with it, we'd need more
data: how many of the other 47,000 masts have cancer clusters? How does that number compare to what we would expect by chance?
Humans are very good
at detecting patterns, but rather poor at detecting randomness. We expect random
incidents of cancer to be spread homogeneously, when in fact true randomness
results in random clusters, not homogeneity. We need careful statistical
tests to
distinguish between random and nonrandom clusters.
Similarly, if we collect 40 different variables for
each subject, it is a mistake to ignore the measurements that show no
significant results, and report only on the ones that do. Out of 40
different variables you would expect 2 to have a significant effect at
p=5%. A report showing 2 such variables is useless: it is
indistinguishable from random chance.
A proper experiment states its hypothesis before gathering
evidence and then puts the hypothesis to the test. Remember when you
did your seventh grade science fair experiment: you made up a
hypothesis first ("Hamsters will get fatter from eating Lucky Charms
than they will from Wheaties") and then did the experiment to confirm or refute the
hypothesis. You can't just make up a hypothesis after the fact to fit
the data. Compare what happens when a football team scores, but the
score is disallowed because a player was offsides. We don't count the
score halfway; we count it as zero, because it breaks the rules. The
team's fans are free to use the play as evidence of their team's
tremendous offensive potential, and point out that it is inevitable
that they will score again. On the other hand, the fans of the other
team are free to say it was a fluke, and only happened because the
player got an unfair advantage from being offsides. The difference
between these two opinions will be settled by playing the remainder of
the game and seeing who actually does score. In the same way, a
statistically significant result observed in a variable that was not
part of the original hypothesis for an experiment counts for zero 
using it would be breaking the rules of science. Supporters get to
argue that it is inevitable that the variable is in fact significant,
but they have to play the game  in this case, run another experiment
 to prove it.
Is it really fair to rule out serendipity in experiments? The
statistician Stephen Senn once complained "The definition of a medical
statistician is one who will not accept that Columbus discovered
America because he said he was looking for India in the trial plan."
He has a point, and I think you should be free to use your own
judgment: if you have good reason to believe a result that was not
part of the original protocol for an experiment, go ahead and believe
it. But don't consider it proved beyond a reasonable doubt and don't
insist that others believe it until you
have independent studies confirming it.
It is interesting to consider why people are so prone to see patterns in
the data, like the cancer clusters around cell phone masts. It turns out
that people and other mammals are sensitive to patterns, and are quick to spot
them where they exist, and even when they don't exist. On the other hand,
people are poor at identifying randomness. Consider the following three
plots. In one of the plots each of the blue points is sampled with equal
probability from the entire square. Which one is it?
Most people say the rightmost plot is "most random". Those with some
statistical sophistication suspect it may be
too random, and pick the
middle plot. In fact, it is the leftmost plot that is a uniform random
sample of 250 points on the unit square. In the middle plot, the grid
is divided into the 25 squares shown by the light lines, and ten
points are placed (with a random uniform distribution) in each of the
25 squares. The plot on the right is formed in a similar way, except
it is composed of 64 smaller squares (not shown by lines), each of
which has 4 points placed at random. People don't like the leftmost
plot because it has several clumps of points that seem nonrandom. In
fact, true randomness consists of a mixture of clumps and
nonclumps. Randomness is different from homogeneity.
Here's another example: guess which of these four squares was
generated with each tick mark independent of the one before it in lefttoright toptobottom order?
   
   
   
   
   
   
   
   
   
   
   
   
(A) (B) (C) (D)
I asked 10 people; 2 said A, 6 said B, 2 said C, and none
said D. Everyone agreed that D has too many long runs of horizontal or
vertical marks. Of the others there was disagreement, but the majority
said B was about right: not too many long runs, nor too few. In fact C
is the correct answer; in C each tick mark is the same as the one
before it with probability 1/2. In A
the marks flip from one direction to the other 3/4 of the time; in B
2/3 of the time, and in D 1/4 of the time. Presumably my subjects
didn't like C because of the several long runs of 6 or 7 ticks in a
row. But a run of 7 tick marks should occur with probability 1/64, so
in a sample of 300 tick marks, you should expect about 4 or 5 of
them. Yet when they do occur, people see it as a pattern, not as
randomness.
The UK's National Radiological Protection Board stated that it
considers mobile phones safe in relation to cancer. "Radio waves do
not have sufficient energy to damage genetic material in cells
directly and therefore cannot cause cancer." They have a theory
about how radio waves might cause cancer. (It was this theory (not Relativity) that won the Nobel Prize for Einstein, and so it is said that Einstein proved cell phones do not cause cancer.) As long as this theory is
correct, statistical correlations about cancer clusters and cellphone masts do not matter. (Of course, statistical
results might cause the Board or others to reevaluate the theory.)
Having a theory is part of having a specific hypothesis, and in fact
it is impossible to do a proper experiment without at least a
skeleton of a theory. Why not? Can't an experiment test the
hypothesis that treatment X is effective against disease D, but I
don't know why? Actually it is fine to propose that
"X prevents disease D in a way similar to other
treatments". That counts as a partial theory.
Suppose you did a
trial of treatment X and found no effect. But a critic says "that's
because you did the experiment on a Thursday, and X doesn't work on
Thursdays". Or "X only works for subjects wearing purple shoes who
have an even number of vowels in their middle name." The critic has
a different theory of how the treatment works, and thus of what
variables must be controlled
for. Without some such theory, you can't do any experiment.
OK, we know a randomized controlled trial is best,
but exactly what should we control? That's a difficult
question, answered only by experience. Consider this passage, from
Richard Feynman's 1974 commencement address on Cargo Cult Science:
There have been many experiments running rats through all kinds of mazes, and so onwith little clear result. But in 1937 a man named Young did a very interesting one. He had a long corridor with doors all along one side where the rats came in, and doors along the other side where the food was. He wanted to see if he could train the rats to go in at the third door down from wherever he started them off. No. The rats went immediately to the door where the food had been the time before.
The question was, how did the rats know, because the corridor was so beautifully built and so uniform, that this was the same door as before? Obviously there was something about the door that was different from the other doors. So he painted the doors very carefully, arranging the textures on the faces of the doors exactly the same. Still the rats could tell. Then he thought maybe the rats were smelling the food, so he used chemicals to change the smell after each run. Still the rats could tell. Then he realized the rats might be able to tell by seeing the lights and the arrangement in the laboratory like any commonsense person. So he covered the corridor, and still the rats could tell.
He finally found that they could tell by the way the floor sounded when they ran over it. And he could only fix that by putting his corridor in sand. So he covered one after another of all possible clues and finally was able to fool the rats so that they had to learn to go in the third door. If he relaxed any of his conditions, the rats could tell.
Now, from a scientific standpoint, that is an Anumberone experiment. That is the experiment that makes ratrunning experiments sensible, because it uncovers the clues that the rat is really usingnot what you think it's using. And that is the experiment that tells exactly what conditions you have to use in order to be careful and control everything in an experiment with ratrunning.
I looked up the subsequent history of this research. The next experiment, and the one after that, never referred to Mr. Young. They never used any of his criteria of putting the corridor on sand, or being very careful. They just went right on running the rats in the same old way, and paid no attention to the great discoveries of Mr. Young, and his papers are not referred to, because he didn't discover anything about the rats. In fact, he discovered all the things you have to do to discover something about rats. But not paying attention to experiments like that is a characteristic example of cargo cult science.
Feynman is saying that Young figured out all the things you need to control to have a good ratmaze experiment. Unfortunately, many researchers have failed to adhere to all these controls.
I'm reminded of when I took an undergrad psychology course, and one of the requitrements was to be a subject in an experiment. I forget the exact task, but the setup was that some stimulus was flashed on a screen, and then I was supposed to press one of four buttons corresponding to the right answer as fast as possible. In these days the apparatus was not fully computercontrolled, so one experimenter announced the trial number beforehand, then the stimuls was presented and I responded, and another experimenter would record the result manually on a clipboard. But after hearing a few of the properlyrandomized trial numbers: 17, 32, 3, 26, ... it occurred to me that the correct button number was always the trial number modulo 4. So from then on I didn't even have to look at the stimulus, I could just listen for the trial number, say 43, quickly compute that that 43 = 3 mod 4 and then press button 3 as soon as the stimulus pops up. The experimenters thought they had correctly randomized the order of presentation of the trials, but they had neglected the fact that announcing the trial number beforehand spoils the whole thing (it would have been okay for the first experimenter to announce the trial number after I had pressed the button).
Part II:
Common Warning Signs in Interpretation of Experiments
If an experiment indicates a phenomenon that is in fact real, then the
experimenter should be able to
repeat the
experiment and get similar results. More importantly, other researchers
should be able to
reproduce the
experiment and get similar results as well. Gullible people get excited by the
very first result, but wiser heads wait for reproducible evidence, and don't get
fooled as often by false alarms.
Here is my amazing claim: under the strictest of controls, I have been able,
using my sheer force of will, to psychically influence an electronic coin flip (implemented
by a random number generator) to come up heads 25 times in a row. The odds
against getting 25 heads in a row are 33 million to 1. You might have any number
of objections: Is the random number generator partial to heads?
No. Is it partial to long runs?
No. Am I lying?
No. Do I really have telekinetic powers?
No. Is there a trick?
Yes. The trick is that I repeated
the experiment 100 million times, and only told you about my best result.
There were about 50 million times when I got zero heads in a row. At times I did
seem lucky/telekinetic: it only took me 2.3 million tries to get 24 heads in a row,
when the odds say it should take 16 million on average. But in the end, I
seemed unlucky: my best result was only 25 in a row, not the expected 26.
Many experiments that claim to beat the odds do it using a version of my
trick. And while my purpose was to intentionally deceive, others do it
without any malicious intent. It happens at many levels: experimenters
don't complete an experiment if it seems to be going badly, or they fail to
write it up for publication (the socalled
"
file
drawer" effect, which has been investigated by many, including my former
colleague Jeff Scargle in a very nice
paper),
or the journal rejects the paper. The whole system has a
publication
bias for positive results over negative results. So when a published
paper proclaims "statistically, this could only happen by chance one in twenty
times", it is quite possible that similar experiments
have been performed twenty times without a positive result, but
have not been published.
In any statistical sample there are two possible sources of error: variance and
bias. The variance is the random fluctuation due to the fact that we can
sample only a small part of the total population. We measure the
probability of a variance error with the
p score (more on that later in
Warning Signs I5 and I6). There are many possible sources of bias errors (for
example, see Warning Sign D4), but they cannot be neatly quantified with a numeric
score, so there is a tendency to ignore them. But bias is still there, and
ignoring it means that more results are accepted that should not be. In
fact, John P. A. Ioannidis went so far as to claim that
Most
Published Research Findings are False. This editorial is a bit misleading in
its title, because it does not actually count how many studies are wrong. In fact, it makes no claims whatsoever about the efficacy or shoddiness of experiments. Rather,
what it does is demonstrate a
mathematical claim that under certain assumptions about the degree of bias and
the percentage of true correlations compared to total possible correlations in a
field of study, then for a given
p value you can estimate how many
published results are in fact true. He gives an example of looking at a set of
100,000 gene polymorphisms to see which are asssociated with
schizophrenia. Under a set of reasonable assumptions, if the bias is 10%,
then the probability of any association that is reported to be significant at
the
p=5% level is actually only 0.044%. This is related to our Warning Sign D7, overzealous data mining: with 10,000 possibilities to choose from, but most of them having no
effect, it is more likely to get a result due to random chance than due to true effect.
In an article titled
An
Intuitive Explanation of Bayesian Reasoning, Eliezer Yudowsky considers this question:
1%
of women at age forty who participate in routine screening have breast
cancer. 80% of women with breast cancer will get positive
mammograms. 9.6% of women without breast cancer will also get positive
mammograms. A woman in this age group had a positive mammography in a
routine screening. What is the probability that she actually has breast
cancer?
Only about 15% of doctors get this right (See
Casscells,
Schoenberger, and Graboys 1978;
Eddy
1982;
Gigerenzer
and Hoffrage 1995; and
others;
researchers keep repeating the study and doctors keep getting it wrong.)
Most doctors estimate the probability to be between 70% and 80%. The correct
answer is 7.8%. Here's why: consider 1000 women of age forty. 1% of
them (10 women) will have breast cancer. Of those, 80% (8 women) will get
a positive mammogram. What about the other 990 women? 9.6% of them,
or 95 women, will also get a positive mammogram. So there are 95 + 8 = 103
anxious women with a positive result, but only 8 actually have cancer. 8/103 =
7.8%. See the table below:

cancer

no cancer

total

P(cancer  positive)

positive mammogram

8

95

103

8/103 = 7.8%

negative mammogram

2

895

897


total

10

990

1000


It says right in the problem description that P(positive  cancer) = 80%.
(Note: Read "P(positive  cancer)" as "the probability of a positive test result
given that the patient has cancer.") But what we're interested in is
P(cancer  positive), the probability of cancer given a positive result.
This is not the same thing at all, as the computation above shows, but doctors
(and lay people) seem to reason that they are more or less the same. In
general, statisticians talk about P(H  E), the probability of a
hypothesis given the
evidence. In this case, the
hypothesis is "having cancer" and the evidence is "positive mammogram."
But usually the probability numbers that are available to us are given in terms
of P(E  H); in this case P(positive  cancer) = 80%.
To make the distinction more clear, let's consider a much rarer disease, central
nervous system vasculitis (CNSV), which affects an estimated 1 in a million
people. Let us assume there is a test that is 99% accurate (for both patients
with and without the disease). What is the chance that a patient with a
positive test result for CNSV actually has it? This time, we'll consider a
hundred million patients:

CNSV

no CNSV

total

P(CNSV  positive)

positive test

99

999,999

1,000,098

99/1,000,098=0.01%

negative test

1

98,999,901

98,999,902


total

100

99,999,900

100,000,000


Even though the test is 99% accurate (that is, P(positive  CNSV) = 99%), a
patient with a positive test result has only an 0.01% chance of having the
disease (that is, P(CNSV  positive) = 0.01%). This is a very small chance,
but it is 100 times higher than patients without a test result, and 10,000 times
higher than patients with a negative result.
Now let's go to the other extreme. Assume the probability of having the
common cold during cold season is 10%. Again, let's assume a test that is
99% accurate.

cold

no cold

total

P(cold  positive)

positive test

99

9

108

99/108=92%

negative test

1

891

892


total

100

900

1000


This time the probability of having a cold given a positive test is 92%.
Now consider carefully these two statements:
"Sam has a positive test result for CNSV, and the test is correct 99% of the time."
"Pat has a positive test result for a cold, and the test is correct 99% of the time."
Carl Sagan
You
will probably feel an overwhelming urge to say that both Sam and Pat have a 99%
chance of their respective diseases (or something close to 99%).
You must
resist giving in to this urge, because you now know that Sam's chance is
really 0.01% and Pat's 92%. Perhaps the following example will help: suppose I
have a test machine that determines whether the subject is a flying leprechaun
from Mars. I'm told the test is 99% accurate. I put person after person
into the machine and the result is always negative (correctly). Finally one day, I put someone (say,
Tom Hanks) into the machine and the light comes on that says "Flying Leprechaun!"
Would you believe the machine? Of course not: that would be
ridiculous,
so we conclude that we just happened to hit the 1% where the test errs. We
find it easy to completely reject a test result when it predicts something
impossible (even if the test is very accurate); now we have to train ourselves
to
almost completely reject a test result
when it predicts something
almost
completely impossible (even if the test is very accurate).
Carl Sagan (19341996) famously said
"
Extraordinary claims require extraordinary
evidence." (although he was repeating the advice of Marcello Truzzi (19352003) and Pierre Laplace (17491827), who said "The weight of evidence for an extraordinary claim must be proportioned to its strangeness."). Intuitively this seems like good philosophy, but we have just
seen that it is actually a precise statement about
mathematics, not just a vague claim about
philosophy. For an ordinary claim ("Pat has a cold"), evidence in the form
of a test that has a 99% chance of being correct is good enough to give you 92%
confidence in the result. But for an extraordinary claim ("Sam has CNSV"),
a test with 99% probability really doesn't help much; we would need a test with
something like 99.999% accuracy before we will start to believe the claim.
Prof. Michael Wigler has a more pessimistic way of putting it (quoted by
Natalie
Angier): "Most of the time, when you get an amazing, counterintuitive
result, it means you screwed up the experiment."
When an experiment states that the results were significant at the
p=1% level, it means
P(Evidence  (Hypothesis is false)) = 1%. (Or, equivalently, that P(Evidence  (Null Hypothesis is true)) = 1%.
Either the experiments's hypothesis must be true, or the null hypothesis must be true.) Note that this by itself says
nothing directly about P(Hypothesis  Evidence), which is what we really want to
know. Note also that the
p score is
only talking about the chance of an error due to random chance, and says nothing
about any of the other sources of mistakes. And yet, time after time,
doctors and even trained statisticians see
"
p=1%" and think "There's a 99% chance
this result is true." That is a mistake.
In my own work, we do a dozen or more experiments every day, and because we have large data sets our typical
value is
p=0.0000001%  one in a billion
or so. Sometimes we get a
p of one in a
trillion. And even then we agonize over whether we should believe the
results of the experiment. We're not worried about an error due to random
chance, but we are worried about other problems: perhaps this experiment works only because it
is novel, and the effect will wear off as people habituate to it; perhaps it works
in the countries we tested, but won't work in the rest of the world, and so
on. Consider the
p value as one
source of error, but don't ignore the other sources of error.
Don't confuse the statistical significance of an experiment with
the magnitude of the result, even though the
word "significance" is often used for both. In my work we often run
an experiment that produces a statistically significant improvement,
but we don't bother to implement the change because the magnitude of
the improvement is small. For example, the experiment might show that alternative X
is better than
the status quo with statistical significance p=0.0000001%,
but that the magnitude of the difference is small, perhaps 0.01%. In other
words, we are almost certain that X would be better, but it would be better
to such a small degree that nobody would really notice any difference.
In such a
case it might not be worth the expense and complication of switching to
the slightly better method.
Tradition dictates that you should report your p score, but it is almost always more informative
to report a
confidence interval, to show the magnitude of any effect. For example,
rather than just saying that method X is better than method Y with a statistically
significant result at the p=5% level, you should also say that the 95%
confidence interval for X is a score of 327 to 329, while the 95% confidence interval for Y
is 329 to 330.
What
p value is sufficient to accept the
results of an experiment? It should be clear by now the answer is "it
depends." It depends on the prior probability of the Hypothesis. The
p value necessary to convince me that Sam
has CNSV is much stricter than the one necessary to convince me that Pat has a
cold. In High School science classes,
p=5% is considered good enough, because
most of the time we really know the answer anyway, and the experiment is done
just to give the students practice. In most physics journals, the standard
is
p=0.01%. The idea is that there
are real phenomena to be discovered, and it is better to insist on more careful
experiments so that we can be sure. In medical journals,
p=5% is often accepted, although some
insist on
p=1%. Why are medical journals
more lenient? In part because it is harder to get a good result  animal
subjects are more fickle than beakers full of chemicals or wires full of
electrons. In part because it is harder to get a good theory. And in part
because we want to encourage the dissemination of potentially lifesaving
information, and we expect doctors to be critical wellinformed consumers of
this information (an expectation that lamentably appears not to be warranted).
What's the right p value? There can't be a single answer. The answer
actually does not depend on just statistics and probabilities; it depends on
utility. That is, we have to answer what expected value (or cost, depending
on how you want to look at it) would we get in each of the four possibile cases:
the result is true (or false) and we act on it as if we believe it (or don't believe it).
For example, treatment X might or might not cure cancer, and we might or might not believe
the study that says it does. If there are no potential bad side effects of X, and if using
X does not preclude using other potential cures, then we would be inclined to believe that
X is effective even with a relatively poor P value. If X has powerful negative
sideeffects, we would insist on more compelling evidence before using it.
xkcd: Correlation
Statistical studies can easily show that one variable is
correlated with another. Proving
that one
causes the other is more
difficult. Consider
this
story about a study of cell phones and brain tumor risk. First, the
study is a good example of hysteria: it caused a public outcry about the dangers
of cell phone usage. However, if you read the article carefully, you'll
see that the main finding does not actually address causation of cancer by cell
phones, only correlation. The study looked at people who already had brain
tumors. They found that tumors are more likely to occur on the side of the head
on which the phone was most often held. But there are three possibilities
that would lead to this correlation: (1) Holding the phone on one side causes a
tumor, (2) Developing a tumor causes one to hold the phone on that side, and (3)
another variable or set of variables causes both. Because it was a
longterm study, we can largely rule out (2): the study would have covered the
time before tumors developed. But the experiment doesn't distinguish
between (1) and (3). For example, assume that 90% of users hold the phone
in their right hand. Now we'll make an unwarranted assumption for this exercise:
we'll assume that 80% of tumors develop in the right side of the brain and that
tumor location and cell phone usage are completely independent of each other.
With a sample of 1000 people we'd get this:

tumor on R

tumor on L

hold on R

720

180

hold on L

80

20

How many get the tumor on the same side as the phone? (720+20)/1000 = 74%.
Only 26% get it on the opposite side, so if you're not careful you might claim
that "cell phone usage triples the incidence of brain tumors" when actually
(given the assumptions of this exercise) tumor location is completely
independent of cell phone usage.
Now let's change the assumptions. We'll stick with 90% righthand use, but
we'll assume that 10% of tumors are caused by the cell phone and appear on the
same side, and the other 90% are split evenly between the two sides. With
1000 people we get these expected results:

tumor on R

tumor on L

hold on R

495

405

hold on L

45

55

So this time we get (495+55)/1000 = 55% of tumors on the same side, 20% less
than last time, but this time there
is a
causation. So if we can't rely on the numbers to distinguish causation
from correlation, what can we do? We need a
counterfactual intervention: to prove
A causes
B, we need to have cases where
A may or may not occur, and then observe
that when we intervene to make
A occur,
B happens, and when we make
A not occur,
B does not happen. The problem with
this study is that it looked at people who were known to have cancer:
B has already happened and we have no way
to intervene. One good way to intervene is with a randomized controlled
trial. Of course it is difficult to do a randomized trial on topics like
this. First, brain tumors are very rare, so you'd need a lot of
subjects. Second, it would be difficult to get subjects to go along with
the trial: "OK, Ann, you're not allowed to use a cell phone at all for the next
twenty years. Bob, you can use one in your right hand, and Charlie, you have to hold it in your left hand.
...".
How do you move from correlation to causation, if you can't do a randomized
controlled trial? For example, how can you show that smoking causes lung cancer?
I won't go into details here, but you could look at the literature on
propensity scores,
double robustness,
and
selection bias.
Ideally you'd like to have as many of the following as possible:

Observational studies (for example, studies of patients with and without
cancer; some who smoke and some who don't) with balanced values for related
variables: age, sex, history of disease, etc.

A very strong correlation. For example, lung cancer is about 20 times more
likely in smokers than nonsmokers; the case for causation would be less
convincing if it were only 2 times more likely.

Reproducability of results from many studies.

A dosage effect: more smoking correlates with more cancer.
 Nonrandomized Interventions: for example, show that people who quit smoking develop fewer cancers than those who continue.
 Analogs: if we can't do randomized experiments on people, can we do them
on animals? Or on cell tissue in a petri dish?

A theory: a known mechanism (such as the carcinogens in tobacco tar) for
smoking causing cancer, and the lack of a theory for cancer causing smoking.
Cottingley Fairies In
the 1970s, Russell Targ and Harold E. Puthoff, two scientists at the Stanford
Research Institute did experiments to evaluate the abilities of Uri Geller,
and concluded that he had actual psychic powers. Later, magician James Randi
showed how Geller performed his feats using standard conjuring tricks.
Randi called Targ and Puthoff the "Laurel and Hardy" of psychic
researchers. This may be harsh; their mistake seems to me not to be due
to incompetence, but rather to trust: they couldn't believe that Geller would
brazenly deceive people. Sixty years earlier a similar story played out
when Arthur Conan Doyle, author of the Sherlock Holmes stories, became
convinced of the legitimacy of several psychic mediums. It took another
great magician of the day, Harry Houdini, to expose the tricks used by the
mediums, but Houdini was unable to convince Doyle. Doyle also believed that
the
Cottingley Fairy photos
(one shown at right) were legitimate evidence of
fairies. Eventually, the girls who created the photos admitted that they were
done with paper cutouts (Adobe Photoshop was not available in 1917). To a
modern eye they look exactly like paper cutouts, but perhaps in 1917
people had less experience with photography, and with photographic fakes.
R.A. Fisher
Sir
R. A. Fisher (18901962) was one of the greatest statisticians of all time,
perhaps most noted for the idea of analysis of variance. But he sullied his
reputation by arguing strongly that smoking does not cause cancer. He had some
sensible arguments. First, he rightfully pointed out our Warning Sign I7,
correlation is not causation. He was clever at coming up with alternative
scenarios: perhaps lung cancer causes an irritation that the patient can feel
long before it can be diagnosed, such that the irritation is alleviated by
smoking. Or perhaps there is some unknown common cause that leads to both
cancer and a tendency to smoke. Fisher was also correct in pointing out
Warning Sign D1, lack of randomized trials: we can't randomly separate children at
birth and force one group to smoke and the other not to. (Although we can do
that with animal studies.) But he was wrong to be so dismissive of reproducible
studies, in humans and animals, that showed a strong correlation, with clear
medical theories explaining why smoking could cause cancer, and no good theories
explaining the correlation any other way. He was wrong not to see that he
may have been influenced by his own fondness for smoking a pipe, or by his
libertarian objections to any interference with personal liberties, or by his
employ as a consultant for the tobacco industry. Fisher died in 1962 of
colon cancer (a disease that is 30% more prevalent in smokers than
nonsmokers). It is sad that the disease took Fisher's life, but it is a
tragedy that Fisher's stuborness provided encouragement for the 5 million people
a year who kill themselves through smoking. Note: since Fisher's death there
have been some ingenious studies that largely get around the correlation
problem, such as
a
study of 49 pairs of identical twins where one smokes and the other doesn't;
the smokers were found to have more plaques on their carotid artery
(
p<0.1%). Also, the work of
Judea Pearl, especially his book
Causality, have advanced our understanding of the difference between correlation and causality.
Conclusion
By now you should see that much can go wrong between the simple statement of
"this result is significant at
p=1%." and the conclusion about what
that really means. As
Darell
Huff said, "it is easy to lie with statistics," but as
Frederick Mosteller
said, "it is easier to lie without them." By scrutinizing experiments
against the checklist provided here, you have a better chance of separating
truth from fiction.
Bibliography
 The Canon, book by Natalie Angier, includes a chapter on
statistics.
 Statistics for Experimenters,
book by Box, Hunter and Hunter.
 Peter Donnelly:
How juries are fooled by statistics, video of his TED talk.
 Electronic Statistics Textbook
 How to Lie with Statistics, classic 1954 book by Darrell Huff.
 Cartoon Guide
to Statistics, book by Larry Gonick.
 Judgment under Uncertainty: Heuristics and Biases,
book by Kahneman, Slovic, and Tversky.
 Innumeracy: Mathematical Illiteracy and Its Consequences, book by John Allen Paulos.
 Probability and Statistics EBook, by UCLA Statistics Depratment.
 What is a pvalue anyway? 34 Stories to Help You Actually Understand Statistics by Andrew Vickers.
 Practical Statistics Simply Explained by Russell Langley, a cheap ($10) buut good Dover book.
 Common Statistical Mistakes, web presentation by Laura J. Simon.
Acknowledgments
Thanks to
Tim Josling,
Thomas Lumley,
Ravi Mohan,
Seth Roberts,
and
Steve Simon
for suggestions and corrections.
Peter Norvig