This PLoS Medicine paper: “Why most Published Research Findings are...
Does the title apply to this paper?
Dr. Ioannidis is a Professor of Medicine at Stanford University and...
Here is a nice table explaining the different types of errors and r...
There have been many recent efforts to evaluate the reproducibility...
This short video explains P-values and significance tests nicely: ...
Researchers typically only report statistically significant results...
This is a very subtle point-> if independent teams are conducting e...
Significance testing and the arbitrary pvalue cutoff of .05 were in...
A great follow up to this point is a modelling exercise in which Gr...
A great follow up to how to improve comes from one of the sequels o...
PLoS Medicine | 0696
Open access, freely available online
August 2005 | Volume 2 | Issue 8 | e124
ublished research fi ndings are
sometimes refuted by subsequent
evidence, with ensuing confusion
and disappointment. Refutation and
controversy is seen across the range of
research designs, from clinical trials
and traditional epidemiological studies
[1–3] to the most modern molecular
research [4,5]. There is increasing
concern that in modern research, false
ndings may be the majority or even
the vast majority of published research
claims [6–8]. However, this should
not be surprising. It can be proven
that most claimed research fi ndings
are false. Here I will examine the key
factors that infl uence this problem and
some corollaries thereof.
Modeling the Framework for False
Positive Findings
Several methodologists have
pointed out [9–11] that the high
rate of nonreplication (lack of
confi rmation) of research discoveries
is a consequence of the convenient,
yet ill-founded strategy of claiming
conclusive research fi ndings solely on
the basis of a single study assessed by
formal statistical signifi cance, typically
for a p-value less than 0.05. Research
is not most appropriately represented
and summarized by p-values, but,
unfortunately, there is a widespread
notion that medical research articles
should be interpreted based only on
p-values. Research fi ndings are defi ned
here as any relationship reaching
formal statistical signifi cance, e.g.,
effective interventions, informative
predictors, risk factors, or associations.
“Negative” research is also very useful.
“Negative” is actually a misnomer, and
the misinterpretation is widespread.
However, here we will target
relationships that investigators claim
exist, rather than null fi ndings.
As has been shown previously, the
probability that a research fi nding
is indeed true depends on the prior
probability of it being true (before
doing the study), the statistical power
of the study, and the level of statistical
signifi cance [10,11]. Consider a 2 × 2
table in which research fi ndings are
compared against the gold standard
of true relationships in a scientifi c
eld. In a research fi eld both true and
false hypotheses can be made about
the presence of relationships. Let R
be the ratio of the number of “true
relationships” to “no relationships”
among those tested in the fi eld. R
is characteristic of the fi eld and can
vary a lot depending on whether the
eld targets highly likely relationships
or searches for only one or a few
true relationships among thousands
and millions of hypotheses that may
be postulated. Let us also consider,
for computational simplicity,
circumscribed fi elds where either there
is only one true relationship (among
many that can be hypothesized) or
the power is similar to fi nd any of the
several existing true relationships. The
pre-study probability of a relationship
being true is R⁄(R + 1). The probability
of a study fi nding a true relationship
refl ects the power 1 − β (one minus
the Type II error rate). The probability
of claiming a relationship when none
truly exists refl ects the Type I error
rate, α. Assuming that c relationships
are being probed in the fi eld, the
expected values of the 2 × 2 table are
given in Table 1. After a research
nding has been claimed based on
achieving formal statistical signifi cance,
the post-study probability that it is true
is the positive predictive value, PPV.
The PPV is also the complementary
probability of what Wacholder et al.
have called the false positive report
probability [10]. According to the 2
× 2 table, one gets PPV = (1 − β)R⁄(R
− βR + α). A research fi nding is thus
The Essay section contains opinion pieces on topics
of broad interest to a general medical audience.
Why Most Published Research Findings
Are False
John P. A. Ioannidis
Citation: Ioannidis JPA (2005) Why most published
research fi ndings are false. PLoS Med 2(8): e124.
Copyright: © 2005 John P. A. Ioannidis. This is an
open-access article distributed under the terms
of the Creative Commons Attribution License,
which permits unrestricted use, distribution, and
reproduction in any medium, provided the original
work is properly cited.
Abbreviation: PPV, positive predictive value
John P. A. Ioannidis is in the Department of Hygiene
and Epidemiology, University of Ioannina School of
Medicine, Ioannina, Greece, and Institute for Clinical
Research and Health Policy Studies, Department of
Medicine, Tufts-New England Medical Center, Tufts
University School of Medicine, Boston, Massachusetts,
United States of America. E-mail:
Competing Interests: The author has declared that
no competing interests exist.
DOI: 10.1371/journal.pmed.0020124
There is increasing concern that most
current published research fi ndings are
false. The probability that a research claim
is true may depend on study power and
bias, the number of other studies on the
same question, and, importantly, the ratio
of true to no relationships among the
relationships probed in each scientifi c
eld. In this framework, a research fi nding
is less likely to be true when the studies
conducted in a fi eld are smaller; when
effect sizes are smaller; when there is a
greater number and lesser preselection
of tested relationships; where there is
greater fl exibility in designs, defi nitions,
outcomes, and analytical modes; when
there is greater fi nancial and other
interest and prejudice; and when more
teams are involved in a scientifi c fi eld
in chase of statistical signifi cance.
Simulations show that for most study
designs and settings, it is more likely for
a research claim to be false than true.
Moreover, for many current scientifi c
elds, claimed research fi ndings may
often be simply accurate measures of the
prevailing bias. In this essay, I discuss the
implications of these problems for the
conduct and interpretation of research.
It can be proven that
most claimed research
ndings are false.
PLoS Medicine | 0697
more likely true than false if (1 − β)R
> α. Since usually the vast majority of
investigators depend on α = 0.05, this
means that a research fi nding is more
likely true than false if (1 − β)R > 0.05.
What is less well appreciated is
that bias and the extent of repeated
independent testing by different teams
of investigators around the globe may
further distort this picture and may
lead to even smaller probabilities of the
research fi ndings being indeed true.
We will try to model these two factors in
the context of similar 2 × 2 tables.
First, let us defi ne bias as the
combination of various design, data,
analysis, and presentation factors that
tend to produce research fi ndings
when they should not be produced.
Let u be the proportion of probed
analyses that would not have been
“research fi ndings,” but nevertheless
end up presented and reported as
such, because of bias. Bias should not
be confused with chance variability
that causes some fi ndings to be false by
chance even though the study design,
data, analysis, and presentation are
perfect. Bias can entail manipulation
in the analysis or reporting of fi ndings.
Selective or distorted reporting is a
typical form of such bias. We may
assume that u does not depend on
whether a true relationship exists
or not. This is not an unreasonable
assumption, since typically it is
impossible to know which relationships
are indeed true. In the presence of bias
(Table 2), one gets PPV = ([1 − β]R +
uβR)⁄(R + α − βR + uuα + uβR), and
PPV decreases with increasing u, unless
1 − β ≤ α, i.e., 1 − β ≤ 0.05 for most
situations. Thus, with increasing bias,
the chances that a research fi nding
is true diminish considerably. This is
shown for different levels of power and
for different pre-study odds in Figure 1.
Conversely, true research fi ndings
may occasionally be annulled because
of reverse bias. For example, with large
measurement errors relationships
are lost in noise [12], or investigators
use data ineffi ciently or fail to notice
statistically signifi cant relationships, or
there may be confl icts of interest that
tend to “bury” signifi cant ndings [13].
There is no good large-scale empirical
evidence on how frequently such
reverse bias may occur across diverse
research fi elds. However, it is probably
fair to say that reverse bias is not as
common. Moreover measurement
errors and ineffi cient use of data are
probably becoming less frequent
problems, since measurement error has
decreased with technological advances
in the molecular era and investigators
are becoming increasingly sophisticated
about their data. Regardless, reverse
bias may be modeled in the same way as
bias above. Also reverse bias should not
be confused with chance variability that
may lead to missing a true relationship
because of chance.
Testing by Several Independent
Several independent teams may be
addressing the same sets of research
questions. As research efforts are
globalized, it is practically the rule
that several research teams, often
dozens of them, may probe the same
or similar questions. Unfortunately, in
some areas, the prevailing mentality
until now has been to focus on
isolated discoveries by single teams
and interpret research experiments
in isolation. An increasing number
of questions have at least one study
claiming a research fi nding, and
this receives unilateral attention.
The probability that at least one
study, among several done on the
same question, claims a statistically
signifi cant research fi nding is easy to
estimate. For n independent studies of
equal power, the 2 × 2 table is shown in
Table 3: PPV = R(1 − β
)⁄(R + 1 − [1 −
) (not considering bias). With
increasing number of independent
studies, PPV tends to decrease, unless
1 − β < α, i.e., typically 1 − β < 0.05.
This is shown for different levels of
power and for different pre-study odds
in Figure 2. For n studies of different
power, the term β
is replaced by the
product of the terms β
for i = 1 to n,
but inferences are similar.
A practical example is shown in Box
1. Based on the above considerations,
one may deduce several interesting
corollaries about the probability that a
research fi nding is indeed true.
Corollary 1: The smaller the studies
conducted in a scientifi c eld, the less
likely the research fi ndings are to be
true. Small sample size means smaller
power and, for all functions above,
the PPV for a true research fi nding
decreases as power decreases towards
1 − β = 0.05. Thus, other factors being
equal, research fi ndings are more likely
true in scientifi c elds that undertake
large studies, such as randomized
controlled trials in cardiology (several
thousand subjects randomized) [14]
than in scientifi c elds with small
studies, such as most research of
molecular predictors (sample sizes 100-
fold smaller) [15].
Corollary 2: The smaller the effect
sizes in a scientifi c eld, the less likely
the research fi ndings are to be true.
Power is also related to the effect
size. Thus research fi ndings are more
likely true in scientifi c elds with large
effects, such as the impact of smoking
on cancer or cardiovascular disease
(relative risks 3–20), than in scientifi c
elds where postulated effects are
small, such as genetic risk factors for
multigenetic diseases (relative risks
1.1–1.5) [7]. Modern epidemiology is
increasingly obliged to target smaller
Table 1. Research Findings and True Relationships
True Relationship
Yes No Total
Yes c(1 − β)R/(R + 1) cα/(R + 1) c(R + αβR)/(R + 1)
No cβR/(R + 1) c(1 − α)/(R + 1) c(1 − α + βR)/(R + 1)
Total cR/(R + 1) c/(R + 1) c
DOI: 10.1371/journal.pmed.0020124.t001
Table 2. Research Findings and True Relationships in the Presence of Bias
True Relationship
Yes No Total
Yes (c[1 − β]R + ucβR)/(R + 1) cα + uc(1 − α)/(R + 1) c(R + αβR + uuα + uβR)/(R + 1)
No (1 − u)cβR/(R + 1) (1 − u)c(1 − α)/(R + 1) c(1 − u)(1 − α + βR)/(R + 1)
Total cR/(R + 1) c/(R + 1) c
DOI: 10.1371/journal.pmed.0020124.t002
August 2005 | Volume 2 | Issue 8 | e124
PLoS Medicine | 0698
effect sizes [16]. Consequently, the
proportion of true research fi ndings
is expected to decrease. In the same
line of thinking, if the true effect sizes
are very small in a scientifi c eld,
this fi eld is likely to be plagued by
almost ubiquitous false positive claims.
For example, if the majority of true
genetic or nutritional determinants of
complex diseases confer relative risks
less than 1.05, genetic or nutritional
epidemiology would be largely utopian
Corollary 3: The greater the number
and the lesser the selection of tested
relationships in a scientifi c eld, the
less likely the research fi ndings are to
be true. As shown above, the post-study
probability that a fi nding is true (PPV)
depends a lot on the pre-study odds
(R). Thus, research fi ndings are more
likely true in confi rmatory designs,
such as large phase III randomized
controlled trials, or meta-analyses
thereof, than in hypothesis-generating
experiments. Fields considered highly
informative and creative given the
wealth of the assembled and tested
information, such as microarrays and
other high-throughput discovery-
oriented research [4,8,17], should have
extremely low PPV.
Corollary 4: The greater the
exibility in designs, defi nitions,
outcomes, and analytical modes in
a scientifi c eld, the less likely the
research fi ndings are to be true.
Flexibility increases the potential for
transforming what would be “negative”
results into “positive” results, i.e., bias,
u. For several research designs, e.g.,
randomized controlled trials [18–20]
or meta-analyses [21,22], there have
been efforts to standardize their
conduct and reporting. Adherence to
common standards is likely to increase
the proportion of true fi ndings. The
same applies to outcomes. True
ndings may be more common
when outcomes are unequivocal and
universally agreed (e.g., death) rather
than when multifarious outcomes are
devised (e.g., scales for schizophrenia
outcomes) [23]. Similarly, fi elds that
use commonly agreed, stereotyped
analytical methods (e.g., Kaplan-
Meier plots and the log-rank test)
[24] may yield a larger proportion
of true fi ndings than fi elds where
analytical methods are still under
experimentation (e.g., artifi cial
intelligence methods) and only “best”
results are reported. Regardless, even
in the most stringent research designs,
bias seems to be a major problem.
For example, there is strong evidence
that selective outcome reporting,
with manipulation of the outcomes
and analyses reported, is a common
problem even for randomized trails
[25]. Simply abolishing selective
publication would not make this
problem go away.
Corollary 5: The greater the fi nancial
and other interests and prejudices
in a scientifi c eld, the less likely
the research fi ndings are to be true.
Confl icts of interest and prejudice may
increase bias, u. Confl icts of interest
are very common in biomedical
research [26], and typically they are
inadequately and sparsely reported
[26,27]. Prejudice may not necessarily
have fi nancial roots. Scientists in a
given fi eld may be prejudiced purely
because of their belief in a scientifi c
theory or commitment to their own
ndings. Many otherwise seemingly
independent, university-based studies
may be conducted for no other reason
than to give physicians and researchers
qualifi cations for promotion or tenure.
Such nonfi nancial confl icts may also
lead to distorted reported results and
interpretations. Prestigious investigators
may suppress via the peer review process
the appearance and dissemination of
ndings that refute their fi ndings, thus
condemning their fi eld to perpetuate
false dogma. Empirical evidence
on expert opinion shows that it is
extremely unreliable [28].
Corollary 6: The hotter a
scientifi c eld (with more scientifi c
teams involved), the less likely the
research fi ndings are to be true.
This seemingly paradoxical corollary
follows because, as stated above, the
PPV of isolated fi ndings decreases
when many teams of investigators
are involved in the same fi eld. This
may explain why we occasionally see
major excitement followed rapidly
by severe disappointments in fi elds
that draw wide attention. With many
teams working on the same fi eld and
with massive experimental data being
produced, timing is of the essence
in beating competition. Thus, each
team may prioritize on pursuing and
disseminating its most impressive
“positive” results. “Negative” results may
become attractive for dissemination
only if some other team has found
a “positive” association on the same
question. In that case, it may be
attractive to refute a claim made in
some prestigious journal. The term
Proteus phenomenon has been coined
to describe this phenomenon of rapidly
Table 3. Research Findings and True Relationships in the Presence of Multiple Studies
True Relationship
Yes No Total
Yes cR(1 − β
)/(R + 1) c(1 − [1 − α]
)/(R + 1) c(R + 1 − [1 − α]
)/(R + 1)
No cRβ
/(R + 1) c(1 − α)
/(R + 1) c([1 − α]
+ Rβ
)/(R + 1)
Total cR/(R + 1) c/(R + 1) c
DOI: 10.1371/journal.pmed.0020124.t003
DOI: 10.1371/journal.pmed.0020124.g001
Figure 1. PPV (Probability That a Research
Finding Is True) as a Function of the Pre-Study
Odds for Various Levels of Bias, u
Panels correspond to power of 0.20, 0.50,
and 0.80.
August 2005 | Volume 2 | Issue 8 | e124
PLoS Medicine | 0699
alternating extreme research claims
and extremely opposite refutations
[29]. Empirical evidence suggests that
this sequence of extreme opposites is
very common in molecular genetics
These corollaries consider each
factor separately, but these factors often
infl uence each other. For example,
investigators working in fi elds where
true effect sizes are perceived to be
small may be more likely to perform
large studies than investigators working
in fi elds where true effect sizes are
perceived to be large. Or prejudice
may prevail in a hot scientifi c eld,
further undermining the predictive
value of its research fi ndings. Highly
prejudiced stakeholders may even
create a barrier that aborts efforts at
obtaining and disseminating opposing
results. Conversely, the fact that a fi eld
is hot or has strong invested interests
may sometimes promote larger studies
and improved standards of research,
enhancing the predictive value of its
research fi ndings. Or massive discovery-
oriented testing may result in such a
large yield of signifi cant relationships
that investigators have enough to
report and search further and thus
refrain from data dredging and
Most Research Findings Are False
for Most Research Designs and for
Most Fields
In the described framework, a PPV
exceeding 50% is quite diffi cult to
get. Table 4 provides the results
of simulations using the formulas
developed for the infl uence of power,
ratio of true to non-true relationships,
and bias, for various types of situations
that may be characteristic of specifi c
study designs and settings. A fi nding
from a well-conducted, adequately
powered randomized controlled trial
starting with a 50% pre-study chance
that the intervention is effective is
eventually true about 85% of the time.
A fairly similar performance is expected
of a confi rmatory meta-analysis of
good-quality randomized trials:
potential bias probably increases, but
power and pre-test chances are higher
compared to a single randomized trial.
Conversely, a meta-analytic fi nding
from inconclusive studies where
pooling is used to “correct” the low
power of single studies, is probably
false if R ≤ 1:3. Research fi ndings from
underpowered, early-phase clinical
trials would be true about one in four
times, or even less frequently if bias
is present. Epidemiological studies of
an exploratory nature perform even
worse, especially when underpowered,
but even well-powered epidemiological
studies may have only a one in
ve chance being true, if R = 1:10.
Finally, in discovery-oriented research
with massive testing, where tested
relationships exceed true ones 1,000-
fold (e.g., 30,000 genes tested, of which
30 may be the true culprits) [30,31],
PPV for each claimed relationship is
extremely low, even with considerable
Box 1. An Example: Science
at Low Pre-Study Odds
Let us assume that a team of
investigators performs a whole genome
association study to test whether
any of 100,000 gene polymorphisms
are associated with susceptibility to
schizophrenia. Based on what we
know about the extent of heritability
of the disease, it is reasonable to
expect that probably around ten
gene polymorphisms among those
tested would be truly associated with
schizophrenia, with relatively similar
odds ratios around 1.3 for the ten or so
polymorphisms and with a fairly similar
power to identify any of them. Then
R = 10/100,000 = 10
, and the pre-study
probability for any polymorphism to be
associated with schizophrenia is also
R/(R + 1) = 10
. Let us also suppose that
the study has 60% power to fi nd an
association with an odds ratio of 1.3 at
α = 0.05. Then it can be estimated that
if a statistically signifi cant association is
found with the p-value barely crossing the
0.05 threshold, the post-study probability
that this is true increases about 12-fold
compared with the pre-study probability,
but it is still only 12 × 10
Now let us suppose that the
investigators manipulate their design,
analyses, and reporting so as to make
more relationships cross the p = 0.05
threshold even though this would not
have been crossed with a perfectly
adhered to design and analysis and with
perfect comprehensive reporting of the
results, strictly according to the original
study plan. Such manipulation could be
done, for example, with serendipitous
inclusion or exclusion of certain patients
or controls, post hoc subgroup analyses,
investigation of genetic contrasts that
were not originally specifi ed, changes
in the disease or control defi nitions,
and various combinations of selective
or distorted reporting of the results.
Commercially available data mining”
packages actually are proud of their
ability to yield statistically signifi cant
results through data dredging. In the
presence of bias with u = 0.10, the post-
study probability that a research fi nding
is true is only 4.4 × 10
. Furthermore,
even in the absence of any bias, when
ten independent research teams perform
similar experiments around the world, if
one of them fi nds a formally statistically
signifi cant association, the probability
that the research fi nding is true is only
1.5 × 10
, hardly any higher than the
probability we had before any of this
extensive research was undertaken!
DOI: 10.1371/journal.pmed.0020124.g002
Figure 2. PPV (Probability That a Research
Finding Is True) as a Function of the Pre-Study
Odds for Various Numbers of Conducted
Studies, n
Panels correspond to power of 0.20, 0.50,
and 0.80.
August 2005 | Volume 2 | Issue 8 | e124
PLoS Medicine | 0700
standardization of laboratory and
statistical methods, outcomes, and
reporting thereof to minimize bias.
Claimed Research Findings
May Often Be Simply Accurate
Measures of the Prevailing Bias
As shown, the majority of modern
biomedical research is operating in
areas with very low pre- and post-
study probability for true fi ndings.
Let us suppose that in a research fi eld
there are no true fi ndings at all to be
discovered. History of science teaches
us that scientifi c endeavor has often
in the past wasted effort in fi elds with
absolutely no yield of true scientifi c
information, at least based on our
current understanding. In such a “null
eld,” one would ideally expect all
observed effect sizes to vary by chance
around the null in the absence of bias.
The extent that observed fi ndings
deviate from what is expected by
chance alone would be simply a pure
measure of the prevailing bias.
For example, let us suppose that
no nutrients or dietary patterns are
actually important determinants for
the risk of developing a specifi c tumor.
Let us also suppose that the scientifi c
literature has examined 60 nutrients
and claims all of them to be related to
the risk of developing this tumor with
relative risks in the range of 1.2 to 1.4
for the comparison of the upper to
lower intake tertiles. Then the claimed
effect sizes are simply measuring
nothing else but the net bias that has
been involved in the generation of
this scientifi c literature. Claimed effect
sizes are in fact the most accurate
estimates of the net bias. It even follows
that between “null fi elds,” the fi elds
that claim stronger effects (often with
accompanying claims of medical or
public health importance) are simply
those that have sustained the worst
For fi elds with very low PPV, the few
true relationships would not distort
this overall picture much. Even if a
few relationships are true, the shape
of the distribution of the observed
effects would still yield a clear measure
of the biases involved in the fi eld. This
concept totally reverses the way we
view scientifi c results. Traditionally,
investigators have viewed large
and highly signifi cant effects with
excitement, as signs of important
discoveries. Too large and too highly
signifi cant effects may actually be more
likely to be signs of large bias in most
elds of modern research. They should
lead investigators to careful critical
thinking about what might have gone
wrong with their data, analyses, and
Of course, investigators working in
any fi eld are likely to resist accepting
that the whole fi eld in which they have
spent their careers is a “null fi eld.”
However, other lines of evidence,
or advances in technology and
experimentation, may lead eventually
to the dismantling of a scientifi c eld.
Obtaining measures of the net bias
in one fi eld may also be useful for
obtaining insight into what might be
the range of bias operating in other
elds where similar analytical methods,
technologies, and confl icts may be
How Can We Improve
the Situation?
Is it unavoidable that most research
ndings are false, or can we improve
the situation? A major problem is that
it is impossible to know with 100%
certainty what the truth is in any
research question. In this regard, the
pure “gold” standard is unattainable.
However, there are several approaches
to improve the post-study probability.
Better powered evidence, e.g., large
studies or low-bias meta-analyses,
may help, as it comes closer to the
unknown “gold” standard. However,
large studies may still have biases
and these should be acknowledged
and avoided. Moreover, large-scale
evidence is impossible to obtain for all
of the millions and trillions of research
questions posed in current research.
Large-scale evidence should be
targeted for research questions where
the pre-study probability is already
considerably high, so that a signifi cant
research fi nding will lead to a post-test
probability that would be considered
quite defi nitive. Large-scale evidence is
also particularly indicated when it can
test major concepts rather than narrow,
specifi c questions. A negative fi nding
can then refute not only a specifi c
proposed claim, but a whole fi eld or
considerable portion thereof. Selecting
the performance of large-scale studies
based on narrow-minded criteria,
such as the marketing promotion of a
specifi c drug, is largely wasted research.
Moreover, one should be cautious
that extremely large studies may be
more likely to fi nd a formally statistical
signifi cant difference for a trivial effect
that is not really meaningfully different
from the null [32–34].
Second, most research questions
are addressed by many teams, and
it is misleading to emphasize the
statistically signifi cant ndings of
any single team. What matters is the
Table 4. PPV of Research Findings for Various Combinations of Power (1 − β), Ratio
of True to Not-True Relationships (R), and Bias (u)
1 − β RuPractical Example PPV
0.80 1:1 0.10 Adequately powered RCT with little
bias and 1:1 pre-study odds
0.95 2:1 0.30 Confi rmatory meta-analysis of good-
quality RCTs
0.80 1:3 0.40 Meta-analysis of small inconclusive
0.20 1:5 0.20 Underpowered, but well-performed
phase I/II RCT
0.20 1:5 0.80 Underpowered, poorly performed
phase I/II RCT
0.80 1:10 0.30 Adequately powered exploratory
epidemiological study
0.20 1:10 0.30 Underpowered exploratory
epidemiological study
0.20 1:1,000 0.80 Discovery-oriented exploratory
research with massive testing
0.20 1:1,000 0.20 As in previous example, but
with more limited bias (more
The estimated PPVs (positive predictive values) are derived assuming α = 0.05 for a single study.
RCT, randomized controlled trial.
DOI: 10.1371/journal.pmed.0020124.t004
August 2005 | Volume 2 | Issue 8 | e124
PLoS Medicine | 0701
totality of the evidence. Diminishing
bias through enhanced research
standards and curtailing of prejudices
may also help. However, this may
require a change in scientifi c mentality
that might be diffi cult to achieve.
In some research designs, efforts
may also be more successful with
upfront registration of studies, e.g.,
randomized trials [35]. Registration
would pose a challenge for hypothesis-
generating research. Some kind of
registration or networking of data
collections or investigators within fi elds
may be more feasible than registration
of each and every hypothesis-
generating experiment. Regardless,
even if we do not see a great deal of
progress with registration of studies
in other fi elds, the principles of
developing and adhering to a protocol
could be more widely borrowed from
randomized controlled trials.
Finally, instead of chasing statistical
signifi cance, we should improve our
understanding of the range of R
values—the pre-study odds—where
research efforts operate [10]. Before
running an experiment, investigators
should consider what they believe the
chances are that they are testing a true
rather than a non-true relationship.
Speculated high R values may
sometimes then be ascertained. As
described above, whenever ethically
acceptable, large studies with minimal
bias should be performed on research
ndings that are considered relatively
established, to see how often they are
indeed confi rmed. I suspect several
established “classics” will fail the test
Nevertheless, most new discoveries
will continue to stem from hypothesis-
generating research with low or very
low pre-study odds. We should then
acknowledge that statistical signifi cance
testing in the report of a single study
gives only a partial picture, without
knowing how much testing has been
done outside the report and in the
relevant fi eld at large. Despite a large
statistical literature for multiple testing
corrections [37], usually it is impossible
to decipher how much data dredging
by the reporting authors or other
research teams has preceded a reported
research fi nding. Even if determining
this were feasible, this would not
inform us about the pre-study odds.
Thus, it is unavoidable that one should
make approximate assumptions on how
many relationships are expected to be
true among those probed across the
relevant research fi elds and research
designs. The wider fi eld may yield some
guidance for estimating this probability
for the isolated research project.
Experiences from biases detected in
other neighboring fi elds would also be
useful to draw upon. Even though these
assumptions would be considerably
subjective, they would still be very
useful in interpreting research claims
and putting them in context. 
1. Ioannidis JP, Haidich AB, Lau J (2001) Any
casualties in the clash of randomised and
observational evidence? BMJ 322: 879–880.
2. Lawlor DA, Davey Smith G, Kundu D,
Bruckdorfer KR, Ebrahim S (2004) Those
confounded vitamins: What can we learn from
the differences between observational versus
randomised trial evidence? Lancet 363: 1724–
3. Vandenbroucke JP (2004) When are
observational studies as credible as randomised
trials? Lancet 363: 1728–1731.
4. Michiels S, Koscielny S, Hill C (2005)
Prediction of cancer outcome with microarrays:
A multiple random validation strategy. Lancet
365: 488–492.
5. Ioannidis JPA, Ntzani EE, Trikalinos TA,
Contopoulos-Ioannidis DG (2001) Replication
validity of genetic association studies. Nat
Genet 29: 306–309.
6. Colhoun HM, McKeigue PM, Davey Smith
G (2003) Problems of reporting genetic
associations with complex outcomes. Lancet
361: 865–872.
7. Ioannidis JP (2003) Genetic associations: False
or true? Trends Mol Med 9: 135–138.
8. Ioannidis JPA (2005) Microarrays and
molecular research: Noise discovery? Lancet
365: 454–455.
9. Sterne JA, Davey Smith G (2001) Sifting the
evidence—What’s wrong with signifi cance tests.
BMJ 322: 226–231.
10. Wacholder S, Chanock S, Garcia-Closas M, El
ghormli L, Rothman N (2004) Assessing the
probability that a positive report is false: An
approach for molecular epidemiology studies. J
Natl Cancer Inst 96: 434–442.
11. Risch NJ (2000) Searching for genetic
determinants in the new millennium. Nature
405: 847–856.
12. Kelsey JL, Whittemore AS, Evans AS,
Thompson WD (1996) Methods in
observational epidemiology, 2nd ed. New York:
Oxford U Press. 432 p.
13. Topol EJ (2004) Failing the public health—
Rofecoxib, Merck, and the FDA. N Engl J Med
351: 1707–1709.
14. Yusuf S, Collins R, Peto R (1984) Why do we
need some large, simple randomized trials? Stat
Med 3: 409–422.
15. Altman DG, Royston P (2000) What do we
mean by validating a prognostic model? Stat
Med 19: 453–473.
16. Taubes G (1995) Epidemiology faces its limits.
Science 269: 164–169.
17. Golub TR, Slonim DK, Tamayo P, Huard
C, Gaasenbeek M, et al. (1999) Molecular
classifi cation of cancer: Class discovery
and class prediction by gene expression
monitoring. Science 286: 531–537.
18. Moher D, Schulz KF, Altman DG (2001)
The CONSORT statement: Revised
recommendations for improving the quality
of reports of parallel-group randomised trials.
Lancet 357: 1191–1194.
19. Ioannidis JP, Evans SJ, Gotzsche PC, O’Neill
RT, Altman DG, et al. (2004) Better reporting
of harms in randomized trials: An extension
of the CONSORT statement. Ann Intern Med
141: 781–788.
20. International Conference on Harmonisation
E9 Expert Working Group (1999) ICH
Harmonised Tripartite Guideline. Statistical
principles for clinical trials. Stat Med 18: 1905–
21. Moher D, Cook DJ, Eastwood S, Olkin I,
Rennie D, et al. (1999) Improving the quality
of reports of meta-analyses of randomised
controlled trials: The QUOROM statement.
Quality of Reporting of Meta-analyses. Lancet
354: 1896–1900.
22. Stroup DF, Berlin JA, Morton SC, Olkin I,
Williamson GD, et al. (2000) Meta-analysis
of observational studies in epidemiology:
A proposal for reporting. Meta-analysis
of Observational Studies in Epidemiology
(MOOSE) group. JAMA 283: 2008–2012.
23. Marshall M, Lockwood A, Bradley C,
Adams C, Joy C, et al. (2000) Unpublished
rating scales: A major source of bias in
randomised controlled trials of treatments for
schizophrenia. Br J Psychiatry 176: 249–252.
24. Altman DG, Goodman SN (1994) Transfer
of technology from statistical journals to the
biomedical literature. Past trends and future
predictions. JAMA 272: 129–132.
25. Chan AW, Hrobjartsson A, Haahr MT,
Gotzsche PC, Altman DG (2004) Empirical
evidence for selective reporting of outcomes in
randomized trials: Comparison of protocols to
published articles. JAMA 291: 2457–2465.
26. Krimsky S, Rothenberg LS, Stott P, Kyle G
(1998) Scientifi c journals and their authors’
nancial interests: A pilot study. Psychother
Psychosom 67: 194–201.
27. Papanikolaou GN, Baltogianni MS,
Contopoulos-Ioannidis DG, Haidich AB,
Giannakakis IA, et al. (2001) Reporting of
confl icts of interest in guidelines of preventive
and therapeutic interventions. BMC Med Res
Methodol 1: 3.
28. Antman EM, Lau J, Kupelnick B, Mosteller F,
Chalmers TC (1992) A comparison of results
of meta-analyses of randomized control trials
and recommendations of clinical experts.
Treatments for myocardial infarction. JAMA
268: 240–248.
29. Ioannidis JP, Trikalinos TA (2005) Early
extreme contradictory estimates may
appear in published research: The Proteus
phenomenon in molecular genetics research
and randomized trials. J Clin Epidemiol 58:
30. Ntzani EE, Ioannidis JP (2003) Predictive
ability of DNA microarrays for cancer outcomes
and correlates: An empirical assessment.
Lancet 362: 1439–1444.
31. Ransohoff DF (2004) Rules of evidence
for cancer molecular-marker discovery and
validation. Nat Rev Cancer 4: 309–314.
32. Lindley DV (1957) A statistical paradox.
Biometrika 44: 187–192.
33. Bartlett MS (1957) A comment on D.V.
Lindley’s statistical paradox. Biometrika 44:
34. Senn SJ (2001) Two cheers for P-values. J
Epidemiol Biostat 6: 193–204.
35. De Angelis C, Drazen JM, Frizelle FA, Haug C,
Hoey J, et al. (2004) Clinical trial registration:
A statement from the International Committee
of Medical Journal Editors. N Engl J Med 351:
36. Ioannidis JPA (2005) Contradicted and
initially stronger effects in highly cited clinical
research. JAMA 294: 218–228.
37. Hsueh HM, Chen JJ, Kodell RL (2003)
Comparison of methods for estimating the
number of true null hypotheses in multiplicity
testing. J Biopharm Stat 13: 675–689.
August 2005 | Volume 2 | Issue 8 | e124


This is a very subtle point-> if independent teams are conducting experiments (and not communicating with one another) on the same hypothesis, our interpretation of reported results of significance should be adjusted. This PLoS Medicine paper: “Why most Published Research Findings are False,” has been the most-accessed article in the history of the Public Library of Science with over 2.5 million reads. Most scientists care about unbiased/reproducible/good science and this paper has made many aware of how biased/non-reproducible/bad science and science publishing really are. Significance testing and the arbitrary pvalue cutoff of .05 were introduced by R.A. Fisher in the 1920s. Here is a quote from him about .05: "If one in twenty does not seem high enough odds, we may, if we prefer it, draw the line at one in fifty or one in a hundred. Personally, the writer prefers to set a low standard of significance at the 5 per cent point, and ignore entirely all results which fails to reach this level. A scientific fact should be regarded as experimentally established only if a properly designed experiment rarely fails to give this level of
significance." For more: Researchers typically only report statistically significant results, so you never hear about the “negative” results, or the ones that are not “significant” using this arbitrary p-value threshold. This system leads to misaligned incentives, non-reproducible research and a major distortion of scientific output/dissemination and understanding. This short video explains P-values and significance tests nicely: I also love the following link on Wikipedia titled "Misunderstandings of p-values": A great follow up to this point is a modelling exercise in which Grimes and Ioannidis show how research becomes progressively untrustworthy under publish or perish pressure: There have been many recent efforts to evaluate the reproducibility of research across different fields, and in fact, prove that most research claims are false. One major effort called the Reproducibility Project: Psychology, is run by the Center for Open Science and aims to reproduce landmark social psychology results. This project was a collaboration of 270 contributing authors that repeated 100 published experimental and correlational psychological studies, and only were able to reproduce 36% of the publications. Another recent effort aimed to reproduce cancer biology research and could only reproduce 6/53 studies, this study was performed by Amgen researchers. For more studies and commentary: Does the title apply to this paper? Dr. Ioannidis is a Professor of Medicine at Stanford University and Director of the Stanford Prevention Research Center at Stanford University School of Medicine. His work tackles clinical research methodology, as well as evidence-based medicine and he is internationally recognized as a leader in empirical studies assessing biases, replication, and reliability of research findings in biomedicine and beyond.  He also helps run the Meta-Research Innovation Center at Stanford (METRICS) which is reimagining science for the 21st century with the goal of strengthening the research enterprise to improve the quality of scientific studies in biomedicine and beyond. "How Not to Be Wrong" by Jordan Ellenberg, starting pg145, has an excellent discussion of this paper and others like it Here is a nice table explaining the different types of errors and rates: ![Imgur]( A great follow up to how to improve comes from one of the sequels of this article by Ioannidis titled "How to make more published research true":