For anyone interested in issues related to p-values, quality of res...
These are heavyweight names in epidemiology/biostatistics. This pap...
This same sentiment was expressed in the American Statistical Assoc...
Another great resource for misinterpretations of p-values, which wa...
In 2015, the journal "Basic and Applied Social Psychology" (BASP) d...
This is often known as data dredging or p-hacking - an excellent Wi...
Unfortunately, this terminology has led to a misconception and many...
R.A. Fisher created the concept of a "p value" and the "null hypoth...
Multiple hypothesis testing is a huge problem in the sciences. Let'...
[Here's](https://fivethirtyeight.com/features/not-even-scientists-c...
This is an excellent short read in its own right!
Wikipedia has a fantastic and very accessible article on the [Misun...
If you've ever worked with a big data set, you'll know that it is v...
Estimating the science-wide false discovery rate is an active area ...
To appropriately combine evidence from more than one study, we need...
This is a misconception I have witnessed time and time again within...
An additional recommendation that has attracted lots of supporters,...
ESSAY
Statistical tests, P values, confidence intervals, and power: a guide
to misinterpretations
Sander Greenland
1
•
Stephen J. Senn
2
•
Kenneth J. Rothman
3
•
John B. Carlin
4
•
Charles Poole
5
•
Steven N. Goodman
6
•
Douglas G. Altman
7
Received: 9 April 2016 / Accepted: 9 April 2016 / Published online: 21 May 2016
The Author(s) 2016. This article is published with open access at Springerlink.com
Abstract Misinterpretation and abuse of statistical tests,
confidence intervals, and statistical power have been
decried for decades, yet remain rampant. A key problem is
that there are no interpretations of these concepts that are at
once simple, intuitive, correct, and foolproof. Instead ,
correct use and interpretation of these statistics requires an
attention to detail which seems to tax the patience of
working scientists. This high cognitive demand has led to
an epidemic of shortcut definitions and interpretations that
are simply wrong, sometimes disastrously so—and yet
these misinterpretations dominate much of the scientific
literature. In light of this problem, we provide definitions
and a discussion of basic statistics that are more general
and critical than typically found in traditional introductory
expositions. Our goal is to provide a resource for instruc-
tors, researchers, and consumers of statistics whose
knowledge of statistical theo ry and technique may be
limited but who wish to avoid and spot misinterpretations.
We emphasize how violation of often unstated analysis
protocols (such as selecting analyses for presentation based
on the P values they produce) can lead to small P values
even if the declared test hypothesis is correct, and can lead
to large P values even if that hypothesis is incorrect. We
then provide an explanatory list of 25 misinterpretations of
P values, confidence intervals, and power. We conclude
with guidelines for improving statistical interpretation and
reporting.
Editor’s note This article has been published online as
supplementary material with an article of Wasserstein RL, Lazar NA.
The ASA’s statement on p-values: context, process and purpose. The
American Statistician 2016.
Albert Hofman, Editor-in-Chief EJE.
& Sander Greenland
lesdomes@ucla.edu
Stephen J. Senn
stephen.senn@lih.lu
John B. Carlin
john.carlin@mcri.edu.au
Charles Poole
cpoole@unc.edu
Steven N. Goodman
steve.goodman@stanford.edu
Douglas G. Altman
doug.altman@csm.ox.ac.uk
1
Department of Epidemiology and Department of Statistics,
University of California, Los Angeles, CA, USA
2
Competence Center for Methodology and Statistics,
Luxembourg Institute of Health, Strassen, Luxembourg
3
RTI Health Solutions, Research Triangle Institute,
Research Triangle Park, NC, USA
4
Clinical Epidemiology and Biostatistics Unit, Murdoch
Children’s Research Institute, School of Population Health,
University of Melbourne, Melbourne, VIC, Australia
5
Department of Epidemiology, Gillings School of Global
Public Health, University of North Carolina, Chapel Hill, NC,
USA
6
Meta-Research Innovation Center, Departments of Medicine
and of Health Research and Policy, Stanford University
School of Medicine, Stanford, CA, USA
7
Centre for Statistics in Medicine, Nuffield Department of
Orthopaedics, Rheumatology and Musculoskeletal Sciences,
University of Oxford, Oxford, UK
123
Eur J Epidemiol (2016) 31:337–350
DOI 10.1007/s10654-016-0149-3
Keywords Confidence intervals Hypothesis testing Null
testing P value Power Significance tests Statistical
testing
Introduction
Misinterpretation and abuse of statistical tests has been
decried for decades, yet remains so rampant that some
scientific journals discourage use of ‘‘statistical signifi-
cance’’ (classifying results as ‘‘significant’’ or not based on
a P value) [1]. One journal now bans all statistical tests and
mathematically related procedures such as confiden ce
intervals [2], which has led to considerable discussion and
debate about the merits of such bans [3, 4].
Despite such bans, we expect that the sta tistical methods
at issue will be with us for many years to come. We thus
think it imperative that basic teaching as well as general
understanding of these methods be improved. Toward that
end, we attempt to explain the meaning of significance
tests, confidence intervals, and statistical powe r in a more
general and critical way than is traditionally done, and then
review 25 common misconceptions in light of our expla-
nations. We also discuss a few more subtle but nonetheless
pervasive problems, explaining why it is important to
examine and synthesize all results relating to a scientific
question, rather than focus on individual findings. We
further explain why statistical tests should never constitute
the sole input to inferences or decisions about associations
or effects. Among the many reasons are that, in most sci-
entific settings, the arbitrary classification of results into
‘‘significant’’ and ‘‘non-significant’’ is unnecessary for and
often dam aging to valid interpretation of data; and that
estimation of the size of effects and the uncertainty sur-
rounding our estimates will be far more important for
scientific inference and sound judgment than any such
classification.
More detailed discussion of the general issues can be found
in many articles, chapters, and books on statistical methods and
their interpretation [5–20]. Specific issues are covered at length
in these sources and in the many peer-reviewed articles that
critique common misinterpretations of null-hypothesis testing
and ‘‘statistical significance’’ [1, 12, 21–74].
Statistical tests, P values, and confidence intervals:
a caustic primer
Statistical models, hypotheses, and tests
Every method of statistical inference depends on a complex
web of assumptions about how data were collected and
analyzed, and how the analysis results were selected for
presentation. The full set of assumptions is embodied in a
statistical model that underpins the method. This model is a
mathematical representation of data variability, and thus
ideally would capture accurately all sources of such vari-
ability. Many problems arise however because this statis-
tical model often incorporates unrealistic or at best
unjustified assumptions. This is true even for so-called
‘‘non-parametric’’ methods, which (like other methods)
depend on assumptions of random sampling or random-
ization. These assumptions are often deceptively simple to
write down mathematically, yet in practice are difficult to
satisfy and verify, as they may depend on successful
completion of a long sequence of actions (such as identi-
fying, contacting, obtaining consent from, obtaining
cooperation of, and following up subjects, as well as
adherence to study protocol s for treatment allocation,
masking, and data analysis).
There is also a serious problem of defining the scope of a
model, in that it should allow not only for a good repre-
sentation of the observed data but also of hypothetical
alternative data that might have been observed. The ref-
erence frame for data that ‘‘might have been observed’’ is
often unclear, for example if multiple outcome measures or
multiple predictive factors have been measured, and many
decisions surrounding analysis choices have been made
after the data were collected—as is invariably the case
[33].
The difficulty of understanding and assessing underlying
assumptions is exacerbated by the fact that the statistical
model is usually presented in a highly compressed and
abstract form—if presented at all. As a result, many
assumptions go unremarked and are often unrecognized by
users as well as consumers of statistics. Nonetheless, all
statistical methods and interpretations are premised on the
model assumptions; that is, on an assumption that the
model provides a valid representation of the variation we
would expect to see across data sets, faithfully reflecting
the circumstances surrounding the study and phenomena
occurring within it.
In most applications of statistical testing, one assump-
tion in the model is a hypothesis that a particular effect has
a specific size, and has been targeted for statistical analysis.
(For simplicity, we use the word ‘‘effect’’ when ‘‘associa-
tion or effect’’ would arguably be better in allowing for
noncausal studies such as most surveys.) This targeted
assumption is called the study hypothesis or test hypothe-
sis, and the stati stical methods used to evaluate it are called
statistical hypothesis tests. Most often, the targeted effect
size is a ‘‘null’’ value representing zero effect (e.g., that the
study treatment makes no difference in average outcome),
in which case the test hypothesis is called the null
hypothesis. Nonetheless, it is als o possible to test other
338 S. Greenland et al.
123
effect sizes. We may also test hypot heses that the effect
does or does not fall within a specific range; for example,
we may test the hypothesis that the effect is no greater than
a particular amount, in which case the hypothesis is said to
be a one-sided or dividing hypothesis [7, 8].
Much statistical teaching and practice has developed a
strong (and unhealthy) focus on the idea that the main aim
of a study should be to test null hypotheses. In fact most
descriptions of statistical testing focus only on testing null
hypotheses, and the entire topic has been called ‘‘Null
Hypothesis Significance Testing’’ (NHST). This exclusive
focus on null hypotheses contributes to misunderstanding
of tests. Adding to the misunderstanding is that many
authors (including R.A. Fisher) use ‘‘null hypothesis’’ to
refer to any test hypothesis, even though this usage is at
odds with other authors and with ordinary English defini-
tions of ‘‘null’’—as are statistical usages of ‘‘significance’’
and ‘‘confidence.’’
Uncertainty, probability, and statistical significance
A more refined goal of statistical anal ysis is to provide an
evaluation of certainty or uncertainty regarding the size of
an effect. It is natural to express such certainty in terms of
‘‘probabilities’’ of hypotheses. In conventional statistical
methods, however, ‘‘probability’’ refers not to hypotheses,
but to quantities that are hypothetical frequencies of data
patterns under an assumed statistical model. These methods
are thus calle d frequentist methods, and the hypothetical
frequencies they predict are called ‘‘frequency probabili-
ties.’’ Despite considerable training to the contrary, many
statistically educated scientists revert to the habit of mis-
interpreting these frequency probabilities as hypothesis
probabilities. (Even more confusingly, the term ‘‘likelihood
of a parameter value’’ is reserved by statisticians to refer to
the probability of the observed data given the parameter
value; it does not refer to a probability of the parameter
taking on the given value.)
Nowhere are these problems more rampant than in
applications of a hypothetical frequency called the P value,
also known as the ‘‘observed significance level’’ for the test
hypothesis. Statistical ‘‘significance tests’’ based on this
concept have been a central part of statistical analyses for
centuries [75]. The focus of traditional definitions of
P values and statistical significance has been on null
hypotheses, treating all other assumptions used to com pute
the P value as if they were known to be correct. Recog-
nizing that these other assumptions are often questionable
if not unwarranted, we will adopt a more general view of
the P value as a statistical summary of the compatibility
between the observed data and what we would predict or
expect to see if we knew the entire statistical model (all the
assumptions used to compute the P value) were correct.
Specifically, the distance between the data and the
model prediction is measured using a test statistic (such as
a t-statistic or a Chi squared statistic). The P value is then
the probability that the chosen test statistic would have
been at least as large as its observed value if every model
assumption were correct, including the test hypothesis.
This definition embodies a crucial point lost in traditional
definitions: In logical terms, the P value tests all the
assumptions about how the data were generated (the entire
model), not just the targeted hypothesis it is supposed to
test (such as a null hypothesis). Furthermore, these
assumptions include far more than what are traditionally
presented as modeling or probability assumptions—they
include assumptions about the conduct of the analysis, for
example that intermediate analysis results were not used to
determine which analyses would be presented.
It is true that the smaller the P value, the more unusual
the data would be if every single assumption were correct;
but a very small P
value does not tell us which assumption
is incorrect. For example, the P value may be very small
because the targeted hypothesis is false; but it may instead
(or in addition) be very small because the study protocols
were violated, or because it was selected for pres entation
based on its small size. Convers ely, a large P value indi-
cates only that the data are not unusual under the model,
but does not imply that the model or any aspect of it (such
as the targeted hypothesis) is correct; it may instead (or in
addition) be large becau se (again) the study protocols were
violated, or because it was selected for presentation based
on its large size.
The general definition of a P value may help one to
understand why statistical tests tell us much less than what
many think they do: Not only does a P value not tell us
whether the hypothesis targeted for testing is true or not; it
says nothing specifically related to that hypothesis unless
we can be completely assured that every other assumption
used for its computation is correct—an assurance that is
lacking in far too many studies.
Nonetheless, the P value can be viewed as a continuous
measure of the compatibility between the data and the
entire model used to compute it, ranging from 0 for com-
plete incompatibility to 1 for perf ect compatibility, and in
this sense may be viewed as measuring the fit of the model
to the data. Too often, however, the P value is degraded
into a dichotomy in which results are declared ‘‘statistically
significant’’ if P falls on or below a cut-off (usually 0.05)
and declared ‘‘nonsignificant’’ otherwise. The terms ‘‘sig-
nificance level’’ and ‘‘alpha level’’ (a) are often used to
refer to the cut-off; however, the term ‘‘significance level’’
invites confusion of the cut-off with the P value itself.
Their difference is profound: the cut-off value a is sup-
posed to be fixed in advance and is thus part of the study
design, unchanged in light of the data. In contrast, the
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 339
123
P value is a number computed from the data and thus an
analysis result, unknown until it is computed.
Moving from tests to estimates
We can vary the test hypothesis while leaving other
assumptions unchanged, to see how the P value differs
across competing test hypotheses. Usually, these test
hypotheses specify different sizes for a targeted effect; for
example, we may test the hypothesis that the average dif-
ference between two treatment groups is zero (the null
hypothesis), or that it is 20 or -10 or any size of interest.
The effect size whose test produced P = 1 is the size most
compatible with the data (in the sense of predicting what
was in fact observed) if all the othe r assumptions used in
the test (the statistical model) were correct, and provides a
point estimate of the effect under those assumptions. The
effect sizes whose test produced P [ 0.05 will typically
define a range of sizes (e.g., from 11.0 to 19.5) that would
be considered more compatible with the data (in the sense
of the observations being closer to what the model pre-
dicted) than sizes outside the range—again, if the statistical
model were correct. This range corresponds to a
1 - 0.05 = 0.95 or 95 % confidence interval, and provides
a convenient way of summarizing the results of hypothesis
tests for many effect sizes. Confidence int ervals are
examples of interval estimates.
Neyman [76] proposed the construction of confidence
intervals in this way because they have the following
property: If one calculates, say, 95 % confidence intervals
repeatedly in valid applications, 95 % of them, on average,
will contain (i.e., include or cover) the true effect size.
Hence, the specified confidence level is called the coverage
probability. As Neyman stressed repeatedly, this coverage
probability is a property of a long sequence of confidence
intervals computed from valid models, rather than a
property of any single confiden ce interv al.
Many journals now require confidence intervals, but
most textbooks and studies discuss P values only for the
null hypothesis of no effect. This exclusive focus on null
hypotheses in testing not only contributes to misunder-
standing of tests and underappreciation of estimation, but
also obscures the close relationship between P values and
confidence intervals, as well as the weaknesses they share.
What P values, confidence intervals, and power
calculations don’t tell us
Much distortion arises from basic misunderstanding of
what P values and their relatives (such as confidence
intervals) do not tell us. Therefore, based on the articles in
our reference list, we review prevalent P value
misinterpretations as a way of moving toward defensi ble
interpretations and presentations. We adopt the format of
Goodman [40] in providing a list of misinterpretations that
can be used to critically evaluate conclusions offered by
research reports and reviews. Every one of the bolded
statements in our list has contributed to statistical distortion
of the scientific literature, and we add the emphatic ‘‘No!’’
to underscore statements that are not only fallacious but
also not ‘‘true enough for practical purposes.’’
Common misinterpretations of single P values
1. The P value is the probability that the test
hypothesis is true; for example, if a test of the null
hypothesis gave P = 0.01, the null hypothesis has
only a 1 % chance of being true; if instead it gave
P = 0.40, the null hypothesis has a 40 % chance of
being true. No! The P value assumes the test
hypothesis is true—it is not a hypothesis probability
and may be far from any reasonable probability for the
test hypot hesis. The P value simply indicates the degree
to which the data conform to the pattern predicted by
the test hypothesis and all the other assumptions used in
the test (the underlying statistical model). Thus
P = 0.01 would indicate that the data are not very close
to what the statistical mode l (including the test
hypothesis) predicted they should be, while P = 0.40
would indicate that the data are much closer to the
model prediction, allowing for chance variation .
2. The P value for the null hypothesis is the probability
that chance alone produced the observed assoc ia-
tion; for example, if the P value for the null
hypothesis is 0.08, there is an 8 % probability that
chance alone produced the association. No! This is a
common variation of the first fallacy and it is just as
false. To say that chance alone produced the observed
association is logically equivalent to asserting that
every assumption used to compute the P value is
correct, including the null hypothesis. Thus to claim
that the null P value is the probability that chance alone
produced the observed association is completely back-
wards: The P value is a probability computed assuming
chance was operating alone. The absurdity of the
common backwards interpretation might be appreci-
ated by pondering how the P value, which is a
probability deduced from a set of assumptions (the
statistical model), can possibly refer to the probability
of those assumptions.
Note: One often sees ‘‘alone’’ dropped from this
description (becoming ‘‘the
P value for the null
hypothesis is the probability that chance produced the
observed association’’), so that the statement is more
ambiguous, but just as wrong.
340 S. Greenland et al.
123
3. A significant test result (P £ 0.05) means that the
test hypothesis is false or should be rejected. No! A
small P value simply flags the data as being unusual
if all the assumptions used to compute it (including
the test hypothesis) were correct; it may be small
because there was a large random error or because
some assumption other than the test hypothesis was
violated (for example, the assumption that this
P value was not selected for presentation because
it was below 0.05). P B 0.05 only means that a
discrepancy from the hypothesis prediction (e.g., no
difference between treatment groups) would be as
large or larger than that observed no more than 5 %
of the time if only chance were creating the
discrepancy (as opposed to a violation of the test
hypothesis or a mistaken assumption).
4. A nonsignificant test result (P > 0.05) means that
the test hypothes is is true or should be accepted.
No! A large P value only suggests that the data are
not unusual if all the assumptions used to compute the
P value (including the test hypothesis) were correct.
The same data would also not be unusual under many
other hypotheses. Furthermore, even if the test
hypothesis is wrong, the P value may be large
because it was inflated by a large random error or
because of some other erroneous assumption (for
example, the assumption that this P value was not
selected for presentation because it was above 0.05).
P [ 0.05 only mea ns that a discrepancy from the
hypothesis prediction (e.g., no difference between
treatment groups) would be as large or larger than
that observed more than 5 % of the time if only
chance were creating the discrepancy.
5. A large P value is evidence in favor of the test
hypothesis. No! In fact, any P value less than 1
implies that the test hypothesis is not the hypothesis
most compatible with the data, because any other
hypothesis with a larger P value would be even
more compatible with the data. A P value cannot be
said to favor the test hypothesis except in relation to
those hypotheses with smaller P values. Further-
more, a large P value often indicates only that the
data are incapable of discriminating among many
competing hypotheses (as would be seen immedi-
ately by examining the range of the confidence
interval). For example, many authors will misinter-
pret P = 0.70 from a test of the null hypothesis as
evidence for no effect, when in fact it indicates that,
even though the null hypothesis is compatible with
the data under the assumptions used to compute the
P value, it is not the hypothesis most compatible
with the data—that honor would belong to a
hypothesis with P =
1. But even if P = 1, there
will be many other hypotheses that are highly
consistent with the data, so that a definitive conclu-
sion of ‘‘no association’’ cannot be deduced from a
P value, no matter how large.
6. A null-hyp othesis P value greater than 0.05 means
that no effect was observed, or that absence of an
effect was shown or demonstrated. No! Observing
P [ 0.05 for the null hypothesis only means that the
null is one among the many hypotheses that have
P [ 0.05. Thus, unless the point estimate (observed
association) equals the null value exactly, it is a
mistake to conclude from P [ 0.05 that a study
found ‘‘no association’’ or ‘‘no evidence’’ of an
effect. If the null P value is less than 1 some
association must be present in the data, and one
must look at the point estimate to determine the
effect size most compatible with the data under the
assumed model.
7. Statistical significance indicates a scientifically or
substantively important relation has been detected.
No! Especially when a study is large, very minor
effects or small assumption violations can lead to
statistically significant tests of the null hypot hesis.
Again, a small null P value simply flags the data as
being unusual if all the assumptions used to compute
it (including the null hypothesis) were correct; but the
way the data are unusual might be of no clinical
interest. One must look at the confidence interval to
determine which effect sizes of scient ific or other
substantive (e.g., clinical) importanc e are relatively
compatible with the data, given the model.
8. Lack of statistical significance indicates that the
effect size is small. No! Especially when a study is
small, even large effects may be ‘‘drowned in noise’’
and thus fail to be detected as statistically significant
by a statistical test. A large null P value simply flags
the data as not being unusual if all the assumptions
used to compute it (including the test hypothesis)
were correct; but the same data will also not be
unusual under many other models and hypotheses
besides the null. Again, one must look at the
confidence interval to determine whether it includes
effect sizes of importance.
9. The P value is the chance of our data occurring if
the test hypothesis is true; for example, P = 0.05
means that the observed association would occur
only 5 % of the time under the test hypothesis. No!
The P value refers not only to what we observed, but
also observations more extreme than what we
observed (where ‘‘extremity’’ is measured in a
particular way). And again, the P value refers to a
data frequency when all the assumptions used to
compute it are correct. In addition to the test
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 341
123
hypothesis, these assumptions include randomness in
sampling, treatment assignment, loss, and missing-
ness, as well as an assumption that the P value was
not sel ected for presentation based on its size or some
other aspect of the results.
10. If you reject the test hypothesis because P £ 0.05,
the chance you are in error (the chance your
‘‘significant finding’’ is a false positive) is 5 %.No!
To see why this description is false, suppose the test
hypothesis is in fact true. Then, if you reject it, the chance
you are in error is 100 %, not 5 %. The 5 % refers only to
how often you would reject it, and therefore be in error,
over very many uses of the test across different studies
when the test hypothesis and all other assumptions used
for the test are true. It does not refer to your single use of
the test, which may have been thrown off by assumption
violations as well as random errors. This is yet another
version of misinterpretation #1.
11. P = 0.05 and P £ 0.05 mean the same thing. No!
This is like saying reported height = 2 m and
reported height B2 m are the same thing:
‘‘height = 2 m’’ would include few people and those
people would be considered tall, whereas ‘‘height
B2 m’’ would include most people including small
children. Similarly, P = 0.05 would be considered a
borderline result in terms of statistical significance,
whereas P B 0.05 lumps borderline results together
with results very incompatible with the model (e.g.,
P = 0.0001) thus rendering its meaning vague, for no
good purpose.
12. P values are properly reported as inequalities (e.g.,
report ‘‘P < 0.02’’ when P = 0.015 or report
‘‘P > 0.05’’ when P = 0.06 or P = 0.70). No! This is
bad practice because it makes it difficult or impossible for
the reader to accurately interpret the statistical result. Only
when the P value is very small (e.g., under 0.001) does an
inequality become justifiable: There is little practical
difference among very small P values when the assump-
tions used to compute P values are not known with
enough certainty to justify such precision, and most
methods for computing P values are not numerically
accurate below a certain point.
13. Statistical significance is a property of the phe-
nomenon being studied, and thus statistical tests
detect significance. No! This misinterpretation is
promoted when researcher s state that they have or
have not found ‘‘evidence of’’ a statistically sign ifi-
cant effect. The effect being tested either exists or
does not exist. ‘‘Statistical significance’’ is a dichoto-
mous description of a P value (that it is below the
chosen cut-off) and thus is a property of a result of a
statistical test; it is not a property of the effect or
population being studied.
14. One should always use two-sided
P values. No!
Two-sided P values are designed to test hypotheses that
the targeted effect measure equals a specific value (e.g.,
zero), and is neither above nor below this value. When,
however, the test hypothesis of scientific or practical
interest is a one-sided (dividing) hypothesis, a one-
sided P value is appropriate. For example, consider the
practical question of whether a new drug is at least as
good as the standard drug for increasing survival time.
This question is one-sided, so testing this hypothesis
calls for a one-sided P value. Nonetheless, because
two-sided P values are the usual default, it will be
important to note when and why a one-sided P value is
being used instead.
There are other interpretations of P values that are
controversial, in that whether a categorical ‘‘No!’’ is war-
ranted depends on one’s philosophy of statistics and the
precise meaning given to the terms involved. The disputed
claims deserve recognition if one wishes to avoid such
controversy.
For example, it has been argued that P values overstate
evidence against test hypotheses, based on directly com-
paring P values against certain quantities (likelihood ratios
and Bayes factors) that play a central role as evidence
measures in Bayesian analysis [37, 72, 77–83]. Nonethe-
less, many other statisticians do not accept these quant ities
as gold standards, and instead point out that P values
summarize crucial evidence needed to gauge the error rates
of decisions based on statistical tests (even though they are
far from sufficient for making those decisions). Thus, from
this frequentist perspective, P valu es do not overstate
evidence and may even be considered as measuring one
aspect of evidence [7, 8, 84–87], with 1 - P measuring
evidence against the model used to compute the P value.
See also Murtaugh [ 88] and its accompanying discussion.
Common misinterpretations of P value comparisons
and predictions
Some of the most severe distortions of the scientific liter-
ature produced by statistical testing involve erroneous
comparison and synthesis of results from different studies
or study subgroups. Among the worst are:
15. When the same hypothesis is tested in different
studies and none or a minority of the tests are
statistically significant (all P > 0.05), the overall
evidence supports the hypothesis. No! This belief is
often used to claim that a literature supports no effect
when the opposite is case. It reflects a tendency of
researchers to ‘‘overestimate the power of most
research’’ [89]. In reality, every study could fail to
reach statistical significance and yet when combined
342 S. Greenland et al.
123
show a statistically significant association and persua-
sive evidence of an effect. For example, if there were
five studies each with P = 0.10, none would be
significant at 0.05 level; but when these P values are
combined using the Fisher formula [9], the overall
P value would be 0.01. There are many real examples
of persuasive evidence for important effects when few
studies or even no study reported ‘‘statistically signif-
icant’’ associations [90, 91]. Thus, lack of statistical
significance of individual studies should not be taken as
implying that the totality of evidence supports no
effect.
16. When the same hypothesis is tested in two different
populations and the resulting P values are on
opposite sides of 0.05, the results are conflicting.
No! Statistical tests are sensitive to many differences
between study populations that are irrelevant to
whether their results are in agreement, such as the
sizes of compared groups in each population. As a
consequence, two studies may provide very different
P values for the same test hypothesis and yet be in
perfect agreement (e.g., may show identical observed
associations). For example, suppose we had two
randomized trials A and B of a treatment, identical
except that trial A had a known standard error of 2 for
the mean difference between treatment groups
whereas trial B had a known standard error of 1 for
the difference. If both trials observed a difference
between treatment groups of exactly 3, the usual
normal test would produce P = 0.13 in A but
P = 0.003 in B. Despite their difference in P values,
the test of the hypothesis of no difference in effect
across studies would have P = 1, reflecting the
perfect agreement of the observed mean differences
from the studies. Differences between results must be
evaluated by directly, for example by estimating and
testing those differences to produce a confiden ce
interval and a P value comparing the results (often
called analysis of heterogeneity, interaction, or
modification).
17. When the same hypothesis is tested in two different
populations and the same P values are obtained, the
results are in agreement. No! Again, tests are sensitive
to many differences between populations that are irrel-
evant to whether their results are in agreement. Two
different studies may even exhibit identical P values for
testing the same hypothesis yet also exhibit clearly
different observed associations. For example, suppose
randomized experiment A observed a mean difference
between treatment groups of 3.00 with standard error
1.00, while B observed a mean difference of 12.00 with
standard error 4.00. Then the standard normal test would
produce P = 0.003 in both; yet the test of the hypothesis
of no difference in effect across studies gives P = 0.03,
reflecting the large difference (12.00 - 3.00 = 9.00)
between the mean differences.
18. If one observ es a small P value, there is a good
chance that the next study will produce a P value
at least as small for the same hypothesis. No! This is
false even under the ideal condition that both studies are
independent and all assumptions including the test
hypothesis are correct in both studies. In that case, if
(say) one observes P = 0.03, the chance that the new
study will show P B 0.03 is only 3 %; thus the chance
the new study will show a P value as small or smaller
(the ‘‘replication probability’’) is exactly the observed
P value! If on the other hand the small P value arose
solely because the true effect exactly equaled its
observed estimate, there would be a 50 % chance that
a repeat experiment of identical design would have a
larger P value [37]. In general, the size of the new
P value will be extremely sensitive to the study size and
the extent to which the test hypothesis or other
assumptions are violated in the new study [86]; in
particular, P may be very small or very large depending
on whether the study and the violations are large or
small.
Finally, although it is (we hope obviously) wrong to do
so, one sometimes sees the null hypothesis compared with
another (alternative) hypothesis using a two-sided P value
for the null and a one-sided P value for the alternative. This
comparison is biased in favor of the null in that the two-
sided test will falsely reject the null only half as often as
the one-sided test will falsely reject the alternative (again,
under all the assumptio ns used for testing).
Common misinterpretations of confidence intervals
Most of the above misinterpr etations translate into an
analogous misinterpretation for confidence intervals. For
example, another misinterpretation of P [ 0.05 is that it
means the test hypothesis has only a 5 % chance of being
false, which in terms of a confidence interval becomes the
common fallacy:
19. The specific 95 % confidence interval presented by
a study has a 95 % chance of containing the true
effect size. No! A reported confidence interval is a range
between two numbers. The frequency with which an
observed interval (e.g., 0.72–2.88) contains the true effect
is either 100 % if the true effect is within the interval or
0 % if not; the 95 % refers only to how often 95 %
confidence intervals computed from very many studies
would contain the true size if all the assumptions used to
compute the intervals were correct.Itispossibleto
compute an interval that can be interpreted as having
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 343
123
95 % probability of containing the true value; nonethe-
less, such computations require not only the assumptions
used to compute the confidence interval, but also further
assumptions about the size of effects in the model. These
further assumptions are summarized in what is called a
prior distribution, and the resulting intervals are usually
called Bayesian posterior (or credible) intervals to
distinguish them from confidence intervals [18].
Symmetrically, the misinterpretation of a small P value as
disproving the test hypothesis could be translated into:
20. An effect size outside the 95 % confidence interval
has been refuted (or excluded) by the data. No! As
with the P value, the confidence interval is computed
from many assumptions, the violation of which may
have led to the results. Th us it is the combination of
the data with the assumptions, along with the arbitrary
95 % criterion, that are needed to declare an effect
size outside the interval is in some way incompa tible
with the observations. Even then, judgements as
extreme as saying the effect size has been refuted or
excluded will require even stronger conditions.
As with P values, naı
¨
ve comparison of confidence intervals
can be highly misleading:
21. If two confidence intervals overlap, the difference
between two estimates or studies is not significant.
No! The 95 % confidence intervals from two subgroups
or studies may overlap substantially and yet the test for
difference between them may still produce P \ 0.05.
Suppose for example, two 95 % confidence intervals for
means from normal populations with known variances
are (1.04, 4.96) and (4.16, 19.84); these intervals
overlap, yet the test of the hypothesis of no difference
in effect acrossstudies gives P = 0.03. As with P values,
comparison between groups requires statistics that
directly test and estimate the differences across groups.
It can, however, be noted that if the two 95 % confidence
intervals fail to overlap, then when using the same
assumptions used to compute the confidence intervals
we will find P \ 0.05 for the difference; and if one of the
95 % intervals contains the point estimate from the other
group or study, we will find P [ 0.05 for the difference.
Finally, as with P values, the replication properties of
confidence intervals are usually misunderstood:
22. An observed 95 % confidence interval predicts
that 95 % of the estimates from future studies will
fall inside the observed interval. No! This statement
is wrong in several ways. Most importantly, under the
model, 95 % is the frequency with which other
unobserved intervals will contain the true effect, not
how fre quently the one interval being presented will
contain future estimates. In fact, even under ideal
conditions the chance that a future estimate will fall
within the current interval will usually be much less
than 95 %. For example, if two independent studies of
the same quantity provide unbiased normal point
estimates with the same standard errors, the chance
that the 95 % confidence interval for the first study
contains the point estimate from the second is 83 %
(which is the chance that the difference between the
two estimates is less than 1.96 standard errors). Again,
an observed interval either does or does not contain the
true effect; the 95 % refers only to how often 95 %
confidence intervals computed from very many studies
would contain the true effect if all the assumpt ions used
to compute the intervals were correct.
23. If one 95 % confidence interval includes the null
value and another excludes that value, the interval
excluding the null is the more precise one.No!
When the model is correct, precision of statistical
estimation is measured directly by confidence interval
width (measured on the appropriate scale). It is not a
matter of inclusion or exclusion of the null or any other
value. Consider two 95 % confidence intervals for a
difference in means, one with limits of 5 and 40, the
other with limits of -5 and 10. The first interval
excludes the null value of 0, but is 30 units wide. The
second includes the null value, but is half as wide and
therefore much more precise.
In addition to the above misinterpretations, 95 % confi-
dence intervals force the 0.05-level cutoff on the reader,
lumping together all effect sizes with P [ 0.05, and in this
way are as bad as presenting P values as dichotomies.
Nonetheless, many authors agree that confidence intervals are
superior to tests and P values because they allow one to shift
focus away from the null hypothesis, toward the full range of
effect sizes compatible with the data—a shift recommended
by many authors and a growing number of journals. Another
way to bring attention to non-null hypotheses is to present
their P values; for example, one could provide or demand
P values for those effect sizes that are recognized as scien-
tifically reasonable alternatives to the null.
As with P values, further cautions are needed to avoid
misinterpreting confidence intervals as providing sharp
answers when none are warranted. The hypothesis which
says the point estimate is the correct effect will have the
largest P value (P = 1 in most cases), and hypotheses inside
a confidence interval will have higher P values than
hypotheses outside the interval. The P values will vary
greatly, however, among hypotheses inside the interval, as
well as among hypotheses on the outside. Also, two
hypotheses may have nearly equal P values even though one
of the hypotheses is inside the interval and the other is out-
side. Thus, if we use P valu es to measure compatibility of
344 S. Greenland et al.
123
hypotheses with data and wish to compare hypotheses with
this measure, we need to examine their P values directly, not
simply ask whether the hypotheses are inside or outside the
interval. This need is particularly acute when (as usual) one
of the hypotheses under scrutiny is a null hypothesis.
Common misinterpretations of power
The power of a test to detect a correct alternative
hypothesis is the pre-study probability that the test will
reject the test hypothesis (e.g., the probability that P will
not exceed a pre-specified cut-off such as 0.05). (The
corresponding pre-study probability of failing to reject the
test hypothesis when the alternative is correct is one minus
the power, also known as the Type-II or beta error rate)
[84] As with P values and confidence intervals, this p rob-
ability is defined over repetitions of the same study design
and so is a frequency probability. One source of reasonable
alternative hypotheses are the effect sizes that were used to
compute power in the study proposal. Pre-study power
calculations do not, howe ver, measure the compatibility of
these alternatives with the data actually observed, while
power calculated from the observed data is a direct (if
obscure) transformation of the null P value and so provides
no test of the alternatives. Thus, presentation of power does
not obvia te the need to provide interval estimates and
direct tests of the alternatives.
For these reasons, many authors have condemned use of
power to interpret estimates and statistical tests [42, 92–
97], arguing that (in contrast to confidence intervals) it
distracts attention from direct comparisons of hypotheses
and introduces new misinterpretations, such as:
24. If you accept the null hypothesis because the null
P value exceeds 0.05 and the power of your test is
90 %, the chance you are in error (the chance that
your finding is a false negative) is 10 %. No! If the
null hypot hesis is false and you accept it, the chance
you are in error is 100 %, not 10 %. Conversely, if the
null hypothesis is true and you accept it, the chance
you are in error is 0 %. The 10 % refers only to how
often you would be in error over very many uses of
the test across different studies when the particular
alternative used to compute power is correct and all
other assumptions used for the test are correct in all
the studies. It does not refer to your single use of the
test or your error rate under any alternative effect size
other than the one used to compute power.
It can be especially misleading to compare results for two
hypotheses by presenting a test or P value for one and power
for the other. For example, testing the null by seeing whether
P B 0.05 with a power less than 1 - 0.05 = 0.95 for the
alternative (as done routinely) will bias the comparison in
favor of the null because it entails a lower probability of
incorrectly rejecting the null (0.05) than of incorrectly
accepting the null when the alternative is correct. Thus, claims
about relative support or evidence need to be based on direct
and comparable measures of support or evidence for both
hypotheses, otherwise mistakes like the following will occur:
25. If the null P value exceeds 0.05 and the power of this
test is 90 % at an alternative, the results support the
null over the alternative. This claim seems intuitive to
many, but counterexamples are easy to construc t in
which the null P valu e is between 0.05 and 0.10, and yet
there are alternatives whose own P value exceeds 0.10
and for which the power is 0.90. Parallel results ensue
for other accepted measures of compatibility, evidence,
and support, indicating that the data show lower
compatibility with and more evidence against the null
than the alternative, despite the fact that the null P value
is ‘‘not significant’’ at the 0.05 alpha level and the
power against the alternative is ‘‘very high’’ [42].
Despite its shortcomings for interpreting current data,
power can be useful for designing studies and for under-
standing why replication of ‘‘statistical significance’’ will
often fail even under ideal conditions. Studies are often
designed or claimed to have 80 % power against a key
alternative when using a 0.05 significance level, although
in execution often have less powe r due to unanticipated
problems such as low subject recruitment. Thus, if the
alternative is correct and the actual power of two studies is
80 %, the chance that the studies will both show P B 0.05
will at best be only 0.80(0.80) = 64 %; furthermore, the
chance that one study shows P B 0.05 and the othe r does
not (and thus will be misinterpreted as showing conflicting
results) is 2(0.80)0.20 = 32 % or about 1 chance in 3.
Similar calculations taking account of typical problems
suggest that one could anticipate a ‘‘replication crisis’’ even
if there were no publication or reporting bias, simply
because current design and testing conventions treat indi-
vidual study results as dich otomous outputs of ‘‘si gnifi-
cant’’/‘‘nonsignificant’’ or ‘‘reject’’/‘‘accept.’’
A statistical model is much more
than an equation with Greek letters
The above list could be expanded by reviewing the
research literature. We will however now turn to direct
discussion of an issue that has been receiving more atten-
tion of late, yet is still widely overlooked or interpreted too
narrowly in statistical teaching and presentations: That the
statistical model used to obtain the results is correct.
Too often, the full statistical model is treated as a simple
regression or structural equation in which effects are
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 345
123
represented by parameters denoted by Greek letters. ‘‘Model
checking’’ is then limited to tests of fit or testing additional
terms for the model. Yet these tests of fit themselves make
further assumptions that should be seen as part of the full
model. For example, all common tests and confidence
intervals depend on assumptions o f random selection for
observation or treatment and random loss or missingness
within levels of controlled covariates. These assumptions
have gradually come under scrutiny via sensitivity and bias
analysis [98], but such methods remain far removed from the
basic statistical training given to most researchers.
Less often stated is the even more crucial assumption
that the analyses themselves were not guided toward
finding nonsignificance or significance (analysis bias), and
that the analysis results were not reported based on their
nonsignificance or significance (reporting bias and publi-
cation bias). Selective reporting renders false even the
limited ideal meanings of statistical significance, P values,
and confidence intervals. Because author decisions to
report and editorial decisions to publish results often
depend on whether the P value is above or below 0.05,
selective reporting has been identified as a major probl em
in large segments of the scientific literature [99–101 ].
Although this selection problem has also been subject to
sensitivity analysis, there has been a bias in studies of
reporting and publication bias: It is usually assumed that
these biases favor significance. This assumption is of course
correct when (as is often the case) researchers select results
for presentation when P B 0.05, a practice that tends to
exaggerate associations [101–105]. Nonetheless, bias in
favor of reporting P B 0.05 is not always plausible let alone
supported by evidence or common sense. For example, one
might expect selection for P [ 0.05 in publications funded
by those with stakes in acceptance of the null hypothesis (a
practice which tends to understate associations); in accord
with that expectation, some empirical studies have observed
smaller estimates and ‘‘nonsignificance’’ more often in such
publications than in other studies [101, 106, 107].
Addressing such problems would require far more political
will and effort than addressing misinterpretation of statistics,
such as enforcing registration of trials, along with open data
and analysis code from all completed studies (as in the
AllTrials initiative, http://www.alltrials.net/). In the mean-
time, readers are advised to consider the entire context in
which research reports are produced and appear when inter-
preting the statistics and conclusions offered by the reports.
Conclusions
Upon realizing that statistical tests are usually misinter-
preted, one may wonder wha t if anything these tests do for
science. They were originally intended to account for
random variability as a source of error, thereby sounding a
note of caution against overinterpretation of observed
associations as true effects or as stronger evidence against
null hypotheses than was warranted. But before long that
use was turned on its head to provide fallacious support for
null hypotheses in the form of ‘‘failure to achieve’’ or
‘‘failure to attain’’ statistical significance.
We have no doubt that the founders of modern statistical
testing would be horrified by common treatments of their
invention. In their first paper describing their binary
approach to statistical testing, Neyman and Pearson [108]
wrote that ‘‘it is doubtful whether the knowledge that [a
P value] was really 0.03 (or 0.06), rather than 0.05…would
in fact ever modify our judgment’’ and that ‘‘The tests
themselves give no final verdict, but as tools help the
worker who is using them to form his final decision.’’
Pearson [109] later added, ‘‘No doubt we could more aptly
have said, ‘his final or provisional decision.’’’ Fisher [110]
went further, saying ‘‘No scientific worker has a fixed level
of significance at which from year to year, and in all cir-
cumstances, he rejects hypotheses; he rather gives his mind
to each particular case in the light of his evidence and his
ideas.’’ Yet fallacious and ritualistic use of tests continued
to spread, including beliefs that whether P was above or
below 0.05 was a universal arbiter of discovery. Thus by
1965, Hill [111] lamented that ‘‘too often we weaken our
capacity to interpret data and to take reasonable decisions
whatever the value of P. And far too often we deduce ‘no
difference’ from ‘no significant difference.’’’
In response, it has been argued that some misinterpre-
tations are harmless in tightly controlled experiments on
well-understood systems, where the test hypothesis may
have special support from established theories (e.g., Men-
delian genetics) and in which every other assumption (such
as random allocation) is forced to hold by careful design
and execution of the study. But it has long been asserted
that the harms of statistical testing in more uncontrollable
and amorphous research settings (such as social-science,
health, and medical fields) have far outweighed its benefits,
leading to calls for banning such tests in research reports—
again with one journal banning P values as well as confi-
dence intervals [2].
Given, however, the deep entrenchment of statistical
testing, as well as the absence of generally accepted
alternative methods, there have been many attempts to
salvage P values by detaching them from their use in sig-
nificance tests. One approach is to focus on P values as
continuous measures of compatibility, as described earlier.
Although this approach has its own limitations (as descri-
bed in points 1, 2, 5, 9, 15, 18, 19), it avoids comparison of
P values with arbitrary cutoffs such as 0.05, (as described
in 3, 4, 6–8, 10–13, 15, 16, 21 and 23–25). Another
approach is to teach and use correct relations of P values to
346 S. Greenland et al.
123
hypothesis probabilities. For exampl e, under common sta-
tistical models, one-sided P values can provide lower
bounds on probabilities for hypotheses about effect direc-
tions [45, 46, 112, 113]. Whether such reinterpretations can
eventually replace common misinterpretations to good
effect remains to be seen.
A shift in emphasis from hypothesis testing to estimation
has been promoted as a simple and relatively safe way to
improve practice [5, 61, 63, 114, 115] resulting in increasing
use of confidence intervals and editorial demands for them;
nonetheless, this shift has brought to the fore misinterpre-
tations of intervals such as 19–23 above [116]. Other
approaches com bine tests of the null with further calcula-
tions involving both null and alternative hypotheses [117,
118]; such calculations may, however, may bring with them
further misinterpretations similar to those described above
for power, as well as greater complexity.
Meanwhile, in the hopes of minimizing harms of current
practice, we can offer several guidelines for users and
readers of statistics, and re-emphasize some key warnings
from our list of misinterpretations:
(a) Correct and careful interpretation of statistical tests
demands examining the sizes of effect est imates and
confidence limits, as well as precise P values (not
just whether P values are above or below 0.05 or
some other threshold).
(b) Careful interpretation also demands critical exami-
nation of the assumptions and conventions used for
the statistical analysis—not just the usual statistical
assumptions, but also the hidden assumptions about
how results were generated and chosen for
presentation.
(c) It is simply false to claim that statistically non-
significant results support a test hypothesis, because
the same results may be even more compatible with
alternative hypotheses—even if the power of the test
is high for those alternatives.
(d) Interval estimates aid in evaluating whether the data
are capable of discriminating among various
hypotheses about effect sizes, or whether statistical
results have been misrepresented as supporting one
hypothesis when those results are better explained by
other hypotheses (see points 4–6). We caution
however that confidence intervals are often only a
first step in these tasks. To compare hypotheses in
light of the data and the statistical model it may be
necessary to calculate the P value (or relative
likelihood) of each hypothesis. We further caution
that confidence intervals provide only a best-case
measure of the uncertainty or ambiguity left by the
data, insofar as they depend on an uncertain
statistical model.
(e) Correct statistical evaluation of multiple studies
requires a pooled analysis or meta-analysis that deals
correctly with study biases [68, 119–125]. Even when
this is done, however, all the earlier cautions apply.
Furthermore, the outcome of any statistical procedure
is but one of many considerations that must be
evaluated when examining the totality of evidence. In
particular, statistical significance is neither necessary
nor sufficient for determining the scientific or prac-
tical significance of a set of observations. This view
was affirmed unanimously by the U.S. Supreme
Court, (Matrixx Initiatives, Inc., et al. v. Siracusano
et al. No. 09–1156. Argued January 10, 2011,
Decided March 22, 2011), and can be seen in our
earlier quotes from Neyman and Pearson.
(f) Any opinion offered about the probability, likeli-
hood, certainty, or similar property for a hypothesis
cannot be derived from statistical methods alone. In
particular, significance tests and confidence intervals
do not by themselves provide a logically sound basis
for concluding an effect is present or absent with
certainty or a given probability. This point should be
borne in mind whenever one sees a conclusion
framed as a statement of probability, likelihood, or
certainty about a hypothesis. Information about the
hypothesis beyond that contained in the analyzed
data and in conventional statistical models (which
give only data probabilities) must be used to reach
such a conclusion; that information should be
explicitly acknowledged and described by those
offering the conclusion. Bayesian statistics offers
methods that attempt to incorporate the needed
information directly into the statistical model; they
have not, however, achieved the popularity of
P values and confidence intervals, in part because
of philosophical objections and in part because no
conventions have become established for their use.
(g) All statistical methods (whether frequentist or
Bayesian, or for testing or estimation, or for
inference or decision) mak e extensive assumptions
about the sequence of events that led to the results
presented—not only in the data generation, but in the
analysis choices. Thus, to allow critical evaluation,
research reports (including meta-analyses) should
describe in detail the full sequence of events that led
to the statistics presented, including the motivation
for the study, its design, the original analysis plan,
the criteria used to include and exclude subjects (or
studies) and data, and a thorough description of all
the analyses that were conducted.
In closing, we note that no statistical method is immune
to misinterpretation and misuse, but prudent users of
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 347
123
statistics will avoid approaches especially prone to serious
abuse. In this regard, we join others in singling out the
degradation of P values into ‘‘significant’’ and ‘‘nonsignif-
icant’’ as an especially pernicious statistical practice [126].
Acknowledgments SJS receives funding from the IDEAL project
supported by the European Union’s Seventh Framework Programme
for research, technological development and demonstration under
Grant Agreement No. 602552. We thank Stuart Hurlbert, Deborah
Mayo, Keith O’Rourke, and Andreas Stang for helpful comments, and
Ron Wasserstein for his invaluable encouragement on this project.
Open Access This article is distributed under the terms of the Creative
Commons Attribution 4.0 International License (http://creative
commons.org/licenses/by/4.0/), which permits unrestricted use, distri-
bution, and reproduction in any medium, provided you give appropriate
credit to the original author(s) and the source, provide a link to the
Creative Commons license, and indicate if changes were made.
References
1. Lang JM, Rothman KJ, Cann CI. That confounded P-value.
Epidemiology. 1998;9:7–8.
2. Trafimow D, Marks M. Editorial. Basic Appl Soc Psychol.
2015;37:1–2.
3. Ashworth A. Veto on the use of null hypothesis testing and p
intervals: right or wrong? Taylor & Francis Editor. 2015.
Resources online, http://editorresources.taylorandfrancisgroup.
com/veto-on-the-use-of-null-hypothesis-testing-and-p-intervals-
right-or-wrong/. Accessed 27 Feb 2016.
4. Flanagan O. Journal’s ban on null hypothesis significance test-
ing: reactions from the statistical arena. 2015. Stats Life online,
https://www.statslife.org.uk/opinion/2114-journal-s-ban-on-null-
hypothesis-significance-testing-reactions-from-the-statistical-arena.
Accessed 27 Feb 2016.
5. Altman DG, Machin D, Bryant TN, Gardner MJ, eds. Statistics
with confidence. 2nd ed. London: BMJ Books; 2000.
6. Atkins L, Jarrett D. The significance of ‘‘significance tests’’. In:
Irvine J, Miles I, Evans J, editors. Demystifying social statistics.
London: Pluto Press; 1979.
7. Cox DR. The role of significance tests (with discussion). Scand J
Stat. 1977;4:49–70.
8. Cox DR. Statistical significance tests. Br J Clin Pharmacol.
1982;14:325–31.
9. Cox DR, Hinkley DV. Theoretical statistics. New York: Chap-
man and Hall; 1974.
10. Freedman DA, Pisani R, Purves R. Statistics. 4th ed. New York:
Norton; 2007.
11. Gigerenzer G, Swijtink Z, Porter T, Daston L, Beatty J, Kruger
L. The empire of chance: how probability changed science and
everyday life. New York: Cambridge University Press; 1990.
12. Harlow LL, Mulaik SA, Steiger JH. What if there were no
significance tests?. New York: Psychology Press; 1997.
13. Hogben L. Statistical theory. London: Allen and Unwin; 1957.
14. Kaye DH, Freedman DA. Reference guide on statistics. In:
Reference manual on scientific evidence, 3rd ed. Washington,
DC: Federal Judicial Center; 2011. p. 211–302.
15. Morrison DE, Henkel RE, editors. The significance test con-
troversy. Chicago: Aldine; 1970.
16. Oakes M. Statistical inference: a commentary for the social and
behavioural sciences. Chichester: Wiley; 1986.
17. Pratt JW. Bayesian interpretation of standard inference state-
ments. J Roy Stat Soc B. 1965;27:169–203.
18. Rothman KJ, Greenland S, Lash TL. Modern epidemiology. 3rd
ed. Philadelphia: Lippincott-Wolters-Kluwer; 2008.
19. Ware JH, Mosteller F, Ingelfinger JA. p-Values. In: Bailar JC,
Hoaglin DC, editors. Ch. 8. Medical uses of statistics. 3rd ed.
Hoboken, NJ: Wiley; 2009. p. 175–94.
20. Ziliak ST, McCloskey DN. The cult of statistical significance:
how the standard error costs us jobs, justice and lives. Ann
Arbor: U Michigan Press; 2008.
21. Altman DG, Bland JM. Absence of evidence is not evidence of
absence. Br Med J. 1995;311:485.
22. Anscombe FJ. The summarizing of clinical experiments by
significance levels. Stat Med. 1990;9:703–8.
23. Bakan D. The test of significance in psychological research.
Psychol Bull. 1966;66:423–37.
24. Bandt CL, Boen JR. A prevalent misconception about sample
size, statistical significance, and clinical importance. J Peri-
odontol. 1972;43:181–3.
25. Berkson J. Tests of significance considered as evidence. J Am
Stat Assoc. 1942;37:325–35.
26. Bland JM, Altman DG. Best (but oft forgotten) practices: testing
for treatment effects in randomized trials by separate analyses of
changes from baseline in each group is a misleading approach.
Am J Clin Nutr. 2015;102:991–4.
27. Chia KS. ‘‘Significant-itis’’—an obsession with the P-value.
Scand J Work Environ Health. 1997;23:152–4.
28. Cohen J. The earth is round (p \ 0.05). Am Psychol.
1994;47:997–1003.
29. Evans SJW, Mills P, Dawson J. The end of the P-value? Br
Heart J. 1988;60:177–80.
30. Fidler F, Loftus GR. Why figures with error bars should replace
p values: some conceptual arguments and empirical demon-
strations. J Psychol. 2009;217:27–37.
31. Gardner MA, Altman DG. Confidence intervals rather than P
values: estimation rather than hypothesis testing. Br Med J.
1986;292:746–50.
32. Gelman A. P-values and statistical practice. Epidemiology.
2013;24:69–72.
33. Gelman A, Loken E. The statistical crisis in science: Data-de-
pendent analysis—a ‘‘garden of forking paths’’—explains why
many statistically significant comparisons don’t hold up. Am
Sci. 2014;102:460–465. Erratum at http://andrewgelman.com/
2014/10/14/didnt-say-part-2/. Accessed 27 Feb 2016.
34. Gelman A, Stern HS. The difference between ‘‘significant’’ and
‘‘not significant’’ is not itself statistically significant. Am Stat.
2006;60:328–31.
35. Gigerenzer G. Mindless statistics. J Socioecon.
2004;33:567–606.
36. Gigerenzer G, Marewski JN. Surrogate science: the idol of a
universal method for scientific inference. J Manag. 2015;41:
421–40.
37. Goodman SN. A comment on replication, p-values and evi-
dence. Stat Med. 1992;11:875–9.
38. Goodman SN. P-values, hypothesis tests and likelihood: impli-
cations for epidemiology of a neglected historical debate. Am J
Epidemiol. 1993;137:485–96.
39. Goodman SN. Towards evidence-based medical statistics, I: the
P-value fallacy. Ann Intern Med. 1999;130:995–1004.
40. Goodman SN. A dirty dozen: twelve P-value misconceptions.
Semin Hematol. 2008;45:135–40.
41. Greenland S. Null misinterpretation in statistical testing and
its impact on health risk assessment. Prev Med. 2011;53:
225–8.
42. Greenland S. Nonsignificance plus high power does not imply
support for the null over the alternative. Ann Epidemiol.
2012;22:364–8.
348 S. Greenland et al.
123
43. Greenland S. Transparency and disclosure, neutrality and bal-
ance: shared values or just shared words? J Epidemiol Com-
munity Health. 2012;66:967–70.
44. Greenland S, Poole C. Problems in common interpretations of
statistics in scientific articles, expert reports, and testimony.
Jurimetrics. 2011;51:113–29.
45. Greenland S, Poole C. Living with P-values: resurrecting a
Bayesian perspective on frequentist statistics. Epidemiology.
2013;24:62–8.
46. Greenland S, Poole C. Living with statistics in observational
research. Epidemiology. 2013;24:73–8.
47. Grieve AP. How to test hypotheses if you must. Pharm Stat.
2015;14:139–50.
48. Hoekstra R, Finch S, Kiers HAL, Johnson A. Probability as
certainty: dichotomous thinking and the misuse of p-values.
Psychon Bull Rev. 2006;13:1033–7.
49. Hurlbert Lombardi CM. Final collapse of the Neyman–Pearson
decision theoretic framework and rise of the neoFisherian. Ann
Zool Fenn. 2009;46:311–49.
50. Kaye DH. Is proof of statistical significance relevant? Wash
Law Rev. 1986;61:1333–66.
51. Lambdin C. Significance tests as sorcery: science is empirical—
significance tests are not. Theory Psychol. 2012;22(1):67–90.
52. Langman MJS. Towards estimation and confidence intervals.
BMJ. 1986;292:716.
53. LeCoutre M-P, Poitevineau J, Lecoutre B. Even statisticians are
not immune to misinterpretations of null hypothesis tests. Int J
Psychol. 2003;38:37–45.
54. Lew MJ. Bad statistical practice in pharmacology (and other
basic biomedical disciplines): you probably don’t know P. Br J
Pharmacol. 2012;166:1559–67.
55. Loftus GR. Psychology will be a much better science when we
change the way we analyze data. Curr Dir Psychol. 1996;5:
161–71.
56. Matthews JNS, Altman DG. Interaction 2: Compare effect sizes
not P values. Br Med J. 1996;313:808.
57. Pocock SJ, Ware JH. Translating statistical findings into plain
English. Lancet. 2009;373:1926–8.
58. Pocock SJ, Hughes MD, Lee RJ. Statistical problems in the
reporting of clinical trials. N Eng J Med. 1987;317:426–32.
59. Poole C. Beyond the confidence interval. Am J Public Health.
1987;77:195–9.
60. Poole C. Confidence intervals exclude nothing. Am J Public
Health. 1987;77:492–3.
61. Poole C. Low P-values or narrow confidence intervals: which
are more durable? Epidemiology. 2001;12:291–4.
62. Rosnow RL, Rosenthal R. Statistical procedures and the justi-
fication of knowledge in psychological science. Am Psychol.
1989;44:1276–84.
63. Rothman KJ. A show of confidence. NEJM. 1978;299:1362–3.
64. Rothman KJ. Significance questing. Ann Intern Med.
1986;105:445–7.
65. Rozeboom WM. The fallacy of null-hypothesis significance test.
Psychol Bull. 1960;57:416–28.
66. Salsburg DS. The religion of statistics as practiced in medical
journals. Am Stat. 1985;39:220–3.
67. Schmidt FL. Statistical significance testing and cumulative
knowledge in psychology: Implications for training of
researchers. Psychol Methods. 1996;1:115–29.
68. Schmidt FL, Hunter JE. Methods of meta-analysis: correcting
error and bias in research findings. 3rd ed. Thousand Oaks:
Sage; 2014.
69. Sterne JAC, Davey Smith G. Sifting the evidence—what’s
wrong with significance tests? Br Med J. 2001;322:226–31.
70. Thompson WD. Statistical criteria in the interpretation of epi-
demiologic data. Am J Public Health. 1987;77:191–4.
71. Thompson B. The ‘‘significance’’ crisis in psychology and
education. J Soc Econ. 2004;33:607–13.
72. Wagenmakers E-J. A practical solution to the pervasive problem
of p values. Psychon Bull Rev. 2007;14:779–804.
73. Walker AM. Reporting the results of epidemiologic studies. Am
J Public Health. 1986;76:556–8.
74. Wood J, Freemantle N, King M, Nazareth I. Trap of trends to
statistical significance: likelihood of near significant P value
becoming more significant with extra data. BMJ.
2014;348:g2215. doi:10.1136/bmj.g2215.
75. Stigler SM. The history of statistics. Cambridge, MA: Belknap
Press; 1986.
76. Neyman J. Outline of a theory of statistical estimation based on
the classical theory of probability. Philos Trans R Soc Lond A.
1937;236:333–80.
77. Edwards W, Lindman H, Savage LJ. Bayesian statistical infer-
ence for psychological research. Psychol Rev. 1963;70:193–242.
78. Berger JO, Sellke TM. Testing a point null hypothesis: the
irreconcilability of P-values and evidence. J Am Stat Assoc.
1987;82:112–39.
79. Edwards AWF. Likelihood. 2nd ed. Baltimore: Johns Hopkins
University Press; 1992.
80. Goodman SN, Royall R. Evidence and scientific research. Am J
Public Health. 1988;78:1568–74.
81. Royall R. Statistical evidence. New York: Chapman and Hall;
1997.
82. Sellke TM, Bayarri MJ, Berger JO. Calibration of p values for
testing precise null hypotheses. Am Stat. 2001;55:62–71.
83. Goodman SN. Introduction to Bayesian methods I: measuring
the strength of evidence. Clin Trials. 2005;2:282–90.
84. Lehmann EL. Testing statistical hypotheses. 2nd ed. Wiley:
New York; 1986.
85. Senn SJ. Two cheers for P-values. J Epidemiol Biostat.
2001;6(2):193–204.
86. Senn SJ. Letter to the Editor re: Goodman 1992. Stat Med.
2002;21:2437–44.
87. Mayo DG, Cox DR. Frequentist statistics as a theory of induc-
tive inference. In: J Rojo, editor. Optimality: the second Erich L.
Lehmann symposium, Lecture notes-monograph series, Institute
of Mathematical Statistics (IMS). 2006;49: 77–97.
88. Murtaugh PA. In defense of P-values (with discussion). Ecol-
ogy. 2014;95(3):611–53.
89. Hedges LV, Olkin I. Vote-counting methods in research syn-
thesis. Psychol Bull. 1980;88:359–69.
90. Chalmers TC, Lau J. Changes in clinical trials mandated by the
advent of meta-analysis. Stat Med. 1996;15:1263–8.
91. Maheshwari S, Sarraj A, Kramer J, El-Serag HB. Oral contra-
ception and the risk of hepatocellular carcinoma. J Hepatol.
2007;47:506–13.
92. Cox DR. The planning of experiments. New York: Wiley; 1958. p. 161.
93. Smith AH, Bates M. Confidence limit analyses should replace
power calculations in the interpretation of epidemiologic stud-
ies. Epidemiology. 1992;3:449–52.
94. Goodman SN. Letter to the editor re Smith and Bates. Epi-
demiology. 1994;5:266–8.
95. Goodman SN, Berlin J. The use of predicted confidence inter-
vals when planning experiments and the misuse of power when
interpreting results. Ann Intern Med. 1994;121:200–6.
96. Hoenig JM, Heisey DM. The abuse of power: the pervasive
fallacy of power calculations for data analysis. Am Stat.
2001;55:19–24.
97. Senn SJ. Power is indeed irrelevant in interpreting completed
studies. BMJ. 2002;325:1304.
98. Lash TL, Fox MP, Maclehose RF, Maldonado G, McCandless
LC, Greenland S. Good practices for quantitative bias analysis.
Int J Epidemiol. 2014;43:1969–85.
Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations 349
123
99. Dwan K, Gamble C, Williamson PR, Kirkham JJ, Reporting
Bias Group. Systematic review of the empirical evidence of
study publication bias and outcome reporting bias—an updated
review. PLoS One. 2013;8:e66844.
100. Page MJ, McKenzie JE, Kirkham J, Dwan K, Kramer S, Green
S, Forbes A. Bias due to selective inclusion and reporting of
outcomes and analyses in systematic reviews of randomised
trials of healthcare interventions. Cochrane Database Syst Rev.
2014;10:MR000035.
101. You B, Gan HK, Pond G, Chen EX. Consistency in the analysis
and reporting of primary end points in oncology randomized
controlled trials from registration to publication: a systematic
review. J Clin Oncol. 2012;30:210–6.
102. Button K, Ioannidis JPA, Mokrysz C, Nosek BA, Flint J,
Robinson ESJ, Munafo
`
MR. Power failure: why small sample
size undermines the reliability of neuroscience. Nat Rev Neu-
rosci. 2013;14:365–76.
103. Eyding D, Lelgemann M, Grouven U, Ha
¨
rter M, Kromp M,
Kaiser T, Kerekes MF, Gerken M, Wieseler B. Reboxetine for
acute treatment of major depression: systematic review and
meta-analysis of published and unpublished placebo and selec-
tive serotonin reuptake inhibitor controlled trials. BMJ.
2010;341:c4737.
104. Land CE. Estimating cancer risks from low doses of ionizing
radiation. Science. 1980;209:1197–203.
105. Land CE. Statistical limitations in relation to sample size.
Environ Health Perspect. 1981;42:15–21.
106. Greenland S. Dealing with uncertainty about investigator bias:
disclosure is informative. J Epidemiol Community Health.
2009;63:593–8.
107. Xu L, Freeman G, Cowling BJ, Schooling CM. Testosterone
therapy and cardiovascular events among men: a systematic
review and meta-analysis of placebo-controlled randomized
trials. BMC Med. 2013;11:108.
108. Neyman J, Pearson ES. On the use and interpretation of certain
test criteria for purposes of statistical inference: part I. Biome-
trika. 1928;20A:175–240.
109. Pearson ES. Statistical concepts in the relation to reality. J R Stat
Soc B. 1955;17:204–7.
110. Fisher RA. Statistical methods and scientific inference. Edin-
burgh: Oliver and Boyd; 1956.
111. Hill AB. The environment and disease: association or causation?
Proc R Soc Med. 1965;58:295–300.
112. Casella G, Berger RL. Reconciling Bayesian and frequentist
evidence in the one-sided testing problem. J Am Stat Assoc.
1987;82:106–11.
113. Casella G, Berger RL. Comment. Stat Sci. 1987;2:344–417.
114. Yates F. The influence of statistical methods for research
workers on the development of the science of statistics. J Am
Stat Assoc. 1951;46:19–34.
115. Cumming G. Understanding the new statistics: effect sizes,
confidence intervals, and meta-analysis. London: Routledge;
2011.
116. Morey RD, Hoekstra R, Rouder JN, Lee MD, Wagenmakers E-J.
The fallacy of placing confidence in confidence intervals. Psy-
chon Bull Rev (in press).
117. Rosenthal R, Rubin DB. The counternull value of an effect size:
a new statistic. Psychol Sci. 1994;5:329–34.
118. Mayo DG, Spanos A. Severe testing as a basic concept in a
Neyman–Pearson philosophy of induction. Br J Philos Sci.
2006;57:323–57.
119. Whitehead A. Meta-analysis of controlled clinical trials. New
York: Wiley; 2002.
120. Borenstein M, Hedges LV, Higgins JPT, Rothstein HR. Intro-
duction to meta-analysis. New York: Wiley; 2009.
121. Chen D-G, Peace KE. Applied meta-analysis with R. New York:
Chapman & Hall/CRC; 2013.
122. Cooper H, Hedges LV, Valentine JC. The handbook of research
synthesis and meta-analysis. Thousand Oaks: Sage; 2009.
123. Greenland S, O’Rourke K. Meta-analysis Ch. 33. In: Rothman
KJ, Greenland S, Lash TL, editors. Modern epidemiology. 3rd
ed. Philadelphia: Lippincott-Wolters-Kluwer; 2008. p. 682–5.
124. Petitti DB. Meta-analysis, decision analysis, and cost-effec-
tiveness analysis: methods for quantitative synthesis in medi-
cine. 2nd ed. New York: Oxford U Press; 2000.
125. Sterne JAC. Meta-analysis: an updated collection from the Stata
journal. College Station, TX: Stata Press; 2009.
126. Weinberg CR. It’s time to rehabilitate the P-value. Epidemiol-
ogy. 2001;12:288–90.
350 S. Greenland et al.
123
These are heavyweight names in epidemiology/biostatistics. This paper represents the first time that I know of, where they united forces into writing an article, reflecting the importance of addressing these misinterpretations.
This same sentiment was expressed in the American Statistical Association's (ASA) [paper on p-values](https://amstat.tandfonline.com/doi/abs/10.1080/00031305.2016.1154108#.XE8wl89KjRY), to which this article served as a supplement. This was the first time ASA had ever produced such a statement of concern.
Unfortunately, this terminology has led to a misconception and many primarily look at the p-value, rather than the magnitude and direction of the effect being measured, to understand its significance. Well known scientists, such as Harvard's Miguel Hernan, have vouched to stop using the terminology "statistically significant".
R.A. Fisher created the concept of a "p value" and the "null hypothesis" (no relationship between two measured phenomena) when he published about statistical significance tests in 1925, later starting in 1928 Neyman and Pearson began introducing the terminology for null and alternative hypothesis testing that are regularly used today.
For more: https://en.wikipedia.org/wiki/Null_hypothesis
Multiple hypothesis testing is a huge problem in the sciences. Let's say you have 20 hypotheses that you want to test and are using a significance threshold of .05. The probability of one of these hypotheses being significant by random chance is 1 − (1 − 0.05) ^20 = 64% probability.
For more: https://www.stat.berkeley.edu/~mgoldman/Section0402.pdf
[Here's](https://fivethirtyeight.com/features/not-even-scientists-can-easily-explain-p-values/) a funny clip from FiveThirtyEight, where scientists actually working on research quality and p-values at Stanford (including one of the authors of this paper) are asked on the spot to explain p-values!
To appropriately combine evidence from more than one study, we need to use a statistical method, NOT compare p-values. The most commonly used such method in medicine is a meta-analysis. One of the famous success stories of meta-ananlyses is the discovery that administering corticosteroids to preterm babies substantially reduces complications; this was in contrast to all individual studies up to that point, which had not provided convincing evidence of such benefit. The main figure of that meta-analysis is now the logo of probably the most well-known consortium for evidence synthesis, Cochrane - more on this [here](https://www.ncbi.nlm.nih.gov/pubmed/16856047).
Wikipedia has a fantastic and very accessible article on the [Misunderstandings of of p-values](https://en.wikipedia.org/wiki/Misunderstandings_of_p-values), as also indicated above.
This is a misconception I have witnessed time and time again within the biosciences. Even the general guidelines given here, do not apply when comparing groups of very different sample size, which is often the case. The best written article on how to interpret comparisons between standard deviation error bars, standard error error bars and confidence intervals I have found so far, can be found [here](https://www.graphpad.com/support/faq/spanwhat-you-can-conclude-when-two-error-bars-overlap-or-dontspan/).
An additional recommendation that has attracted lots of supporters, and enemies, is that we lower the commonly accepted level of significance from 0.05 to 0.005. The paper proposing this change has been signed by some very big names and can be found [here](https://www.nature.com/articles/s41562-017-0189-z). The authors understand this proposal as an interim measure to curtail the "symptoms" of misunderstandings in statistical inference while working on the "cause."
This is often known as data dredging or p-hacking - an excellent Wikipedia article on it can be found [here](https://en.wikipedia.org/wiki/Data_dredging). A MUST READ case that came to light last year is that of Brian Wansink, a Cornell professor, who inadvertently admitted p-hacking on his personal blog. Many of his papers are now retracted from the academic literature. You can read the original report about this case [here](https://www.buzzfeednews.com/article/stephaniemlee/brian-wansink-cornell-p-hacking).
Another great resource for misinterpretations of p-values, which was also validated by one of the authors, can be found in Wikipedia's article [Misunderstandings of p-values](https://en.wikipedia.org/wiki/Misunderstandings_of_p-values).
This is an excellent short read in its own right!
Estimating the science-wide false discovery rate is an active area of research (and fight!). The journal Biostatistics published a fantastic issue of heavy-weight names weighing on this topic [here](https://academic.oup.com/biostatistics/issue/15/1). Unfortunately, reproducibility projects in psychology, cancer biology and economics, do not paint a particularly favorable picture for even the most prestigious of studies. This has led to what is known as the "reproducibility crisis."
For anyone interested in issues related to p-values, quality of research, open science and evidence-based practice, you may find the [Reddit community on meta-research](https://www.reddit.com/r/metaresearch/) of interest (disclaimer: I am one of the moderators of that community!)
Fisher was in fact vehemently against the null hypothesis significance testing procedure introduced by Neyman and Pearson (which is the procedure most scientists use today). He was very concerned that we would turn the often complicated process of inferring from data into an automated decision algorithm; unfortunately, it turns out he was spot on. One of the classic papers in this space offers further historic details and was written by one of the authors of this paper in 1993 - it can be found [here](https://academic.oup.com/aje/article/137/5/485/50007), but it is behind a paywall...
In 2015, the journal "Basic and Applied Social Psychology" (BASP) declared the null hypothesis significance testing procedure invalid, and banned it for any studies appearing in its journal. For more: http://www.medicine.mcgill.ca/epidemiology/Joseph/courses/EPIB-621/BASP2015.pdf
If you've ever worked with a big data set, you'll know that it is very easy to selectively fish for significant p-values. If you're working with "big data", even the smallest differences might appear as "statistically significant"-> always put your results in context and inspect effect sizes. The more data you have, you probably want to try smaller significance levels, especially if you're testing multiple hypotheses (see Bonferonni correction).