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Chan A, Hróbjartsson A, Haahr MT, Gøtzsche PC, Altman DG. Empirical Evidence for Selective Reporting of Outcomes in Randomized TrialsComparison of Protocols to Published Articles. JAMA. 2004;291(20):2457–2465. doi:10.1001/jama.291.20.2457
Context Selective reporting of outcomes within published studies based on the
nature or direction of their results has been widely suspected, but direct
evidence of such bias is currently limited to case reports.
Objective To study empirically the extent and nature of outcome reporting bias
in a cohort of randomized trials.
Design Cohort study using protocols and published reports of randomized trials
approved by the Scientific-Ethical Committees for Copenhagen and Frederiksberg,
Denmark, in 1994-1995. The number and characteristics of reported and unreported
trial outcomes were recorded from protocols, journal articles, and a survey
of trialists. An outcome was considered incompletely reported if insufficient
data were presented in the published articles for meta-analysis. Odds ratios
relating the completeness of outcome reporting to statistical significance
were calculated for each trial and then pooled to provide an overall estimate
of bias. Protocols and published articles were also compared to identify discrepancies
in primary outcomes.
Main Outcome Measures Completeness of reporting of efficacy and harm outcomes and of statistically
significant vs nonsignificant outcomes; consistency between primary outcomes
defined in the most recent protocols and those defined in published articles.
Results One hundred two trials with 122 published journal articles and 3736
outcomes were identified. Overall, 50% of efficacy and 65% of harm outcomes
per trial were incompletely reported. Statistically significant outcomes had
a higher odds of being fully reported compared with nonsignificant outcomes
for both efficacy (pooled odds ratio, 2.4; 95% confidence interval [CI], 1.4-4.0)
and harm (pooled odds ratio, 4.7; 95% CI, 1.8-12.0) data. In comparing published
articles with protocols, 62% of trials had at least 1 primary outcome that
was changed, introduced, or omitted. Eighty-six percent of survey responders
(42/49) denied the existence of unreported outcomes despite clear evidence
to the contrary.
Conclusions The reporting of trial outcomes is not only frequently incomplete but
also biased and inconsistent with protocols. Published articles, as well as
reviews that incorporate them, may therefore be unreliable and overestimate
the benefits of an intervention. To ensure transparency, planned trials should
be registered and protocols should be made publicly available prior to trial
Selective publication of studies with statistically significant results
has received widespread recognition.1 In contrast,
selective reporting of favorable outcomes within published studies has not
undergone comparable empirical investigation. The existence of outcome reporting
bias has been widely suspected for years,2-12 but
direct evidence is limited to case reports that have low generalizability13-15 and may themselves
be subject to publication bias.
Our study had 3 goals: (1) to determine the prevalence of incomplete
outcome reporting in published reports of randomized trials; (2) to assess
the association between outcome reporting and statistical significance; and
(3) to evaluate the consistency between primary outcomes specified in trial
protocols and those defined in the published articles.
In February 2003, we identified protocols and protocol amendments for
randomized trials by reviewing paper files from clinical studies approved
by the Scientific-Ethical Committees for Copenhagen and Frederiksberg, Denmark,
in 1994-1995. This period was chosen to allow sufficient time for trial completion
and publication. A randomized trial was defined as a prospective study assessing
the therapeutic, preventative, adverse, pharmacokinetic, or physiological
effects of 1 or more health care interventions and allocating human participants
to study groups using a random method. Pharmocokinetic trials measured primarily
the kinetics of drug metabolism and excretion; physiological trials, with
the exception of preventative trials, examined the effect of interventions
on healthy volunteers rather than in the intended disease or at-risk population.
Studies were included if they simply claimed to allocate participants randomly
or if they described a truly random sequence of allocation. Pseudo-random
methods of allocation, such as alternation or the use of date or case numbers,
were deemed inadequate for inclusion.
Trials with at least 1 identified journal article were included in our
study cohort. Publication in journals was identified by contacting trialists
and by searching MEDLINE, EMBASE, and the Cochrane Controlled Trials Register
using investigator names and keywords (final search, May 2003). For each trial,
we included all published articles reporting final results. Abstracts and
reports of preliminary results were excluded.
For each published trial, we reviewed the study protocol, any amendments,
and all published articles to extract the trial characteristics, the number
and nature of reported outcomes (including statistical significance, completeness
of reporting, and specification as primary/secondary),as well as the number
and specification of unreported outcomes. Data from amendments took precedence
over data from earlier protocols.
An outcome was defined as a variable that was intended for comparison
between randomized groups in order to assess the efficacy or harm of an intervention.
We prefer the term "harm" rather than "safety" because all interventions can
be potentially harmful. Unreported outcomes were those that were specified
in the most recent protocol but were not reported in any of the published
articles, or that were mentioned in the "Methods" but not the "Results" sections
of any of the published articles. Their statistical significance and the reasons
for omitting them were solicited from contact authors through a prepiloted
questionnaire. We initially asked whether there were any outcomes that were
intended for comparison between randomized groups but were not reported in
any published articles, excluding characteristics used only for assessment
of baseline comparability. We subsequently provided trialists with a list
of unreported outcomes identified from our comparison of protocols with published
articles. Double-checking of outcome data extraction from a random subset
of 20 trials resulted in corrections to 21 of 362 outcomes (6%), 15 of which
were in a single trial.
We classified the level of outcome reporting in 4 groups based on data
provided across all published articles of a trial (Table 1). A fully reported outcome was one with sufficient data
for inclusion in a meta-analysis. The nature and amount of data required to
meet this criterion vary depending on the data type (Box 1). Partially reported outcomes had some of the necessary
data for meta-analysis, while qualitatively reported outcomes had no useful
data except for a P value or a statement regarding
the presence or absence of statistical significance. Unreported outcomes were
those for which no data were provided in any published articles despite having
been specified in the protocol or the "Methods" sections of the published
For Unpaired Continuous Data
Sample size in each group
and Magnitude of treatment effect
(group means/medians or difference in means/medians)
of precision or variability (confidence interval, standard deviation, or standard
error for means; interquartile or other range for medians) or the precise P value*
For Unpaired Binary Data
Sample size in each group
and Either the numbers (or percentages)
of participants with the event for each group, or the odds ratio or relative
risk with a measure of precision or variability (confidence interval, standard
deviation, or standard error) or the precise P value*
For Paired Continuous Data
Sample size in each group
and Either the raw data for
each participant, or the mean difference between groups and a measure of its
precision or variability or the precise P value
For Paired Binary Data
Sample size in each group
and Paired numbers of participants with and without events
For Survival Data
Either a Kaplan-Meier curve or similar, with numbers of patients at
risk over time, or a hazard ratio with a measure of precision and sample size
in each group
*Sample sizes, treatment effect, and precise P value
enable the calculation of a standard error if a measure of precision or variability
is not reported.
We defined 2 additional terms to describe relevant composite levels
of reporting (Table 1). Reported outcomes were defined as those with at least some
data presented (full, partial, and qualitative). Incompletely
reported outcomes were defined as those that were inadequately reported
for meta-analysis (partial, qualitative, and unreported).
Analyses were conducted at the trial level and stratified by study design
using Stata 7 (Stata Corp, College Station, Tex). Efficacy and harm outcomes
were evaluated separately. The reasons given by trialists for not reporting
outcomes were tabulated, and the proportion of unreported and incompletely
reported outcomes per trial was determined.
For each trial, we tabulated all outcomes in a 2 × 2 table relating
the level of outcome reporting (full vs incomplete) to statistical significance
(P<.05 vs P≥.05).
Outcomes were ineligible if their statistical significance was unknown. An
odds ratio was then calculated from the 2 × 2 table for every trial,
except when any entire row or column total was zero. If the table included
a single cell frequency of zero or 2 diagonal cell frequencies of zero, we
added 0.5 to all 4 cell frequencies.16,17 Odds
ratios greater than 1.0 meant that statistically significant outcomes had
a higher odds of being fully reported compared with nonsignificant outcomes.
The odds ratios from each trial were pooled using a random-effects meta-analysis
to provide an overall estimate of bias. Exploratory meta-regression was used
to examine the effect of funding source, sample size, and number of study
centers on the magnitude of bias. Sensitivity analyses were conducted to assess
the robustness of the odds ratios when (1) nonresponders to the survey were
excluded; (2) pharmacokinetic and physiological trials were excluded; and
(3) the level of reporting was dichotomized using a different cutoff (fully
or partially reported vs qualitatively reported or unreported).
Finally, we evaluated the consistency between primary outcomes specified
in the most recent trial protocols (including amendments) and those defined
in the published articles. Primary outcomes consisted of those that were defined
explicitly as such in the protocol or published article. If none was explicitly
defined, we used the outcome stated in the power calculation. We defined major
discrepancies as those in which (1) a prespecified primary outcome was reported
as secondary or was not labeled as either; (2) a prespecified primary outcome
was omitted from the published articles; (3) a new primary outcome was introduced
in the published articles; and (4) the outcome used in the power calculation
was not the same in the protocol and the published articles. A discrepancy
was said to favor statistically significant results if a new statistically
significant primary outcome was introduced in the published articles or if
a nonsignificant primary outcome was omitted or defined as nonprimary in the
published articles. Discrepancies were verified by 2 independent researchers,
with disagreements resolved by consensus. Double-checking resulted in major
corrections for 3 of 259 primary outcomes (1%).
We identified 1403 applications submitted to the Scientific-Ethical
Committees for Copenhagen and Frederiksberg, Denmark, in 1994-1995 (Figure 1). We excluded 1129 studies, primarily
because they were not randomized trials or were amendments to studies submitted
before 1994. Thirty files (2%) could not be located; it is unclear whether
they would have been eligible for inclusion. We found 274 randomized trial
protocols, but 172 (63%) were never begun or completed, or were unpublished
according to our literature searches and survey of trialists. The final cohort
consisted of 102 trials with 122 published articles. Published articles for
48 of the 102 trials were identified by literature search alone, as the trialists
did not respond to our request for information (Figure 1).
Trial characteristics are shown in Table 2. The majority were of parallel-group design, and most investigated
drug interventions. One half were funded solely by industry, and one half
were multicenter studies. Published articles for 39% of the trials listed
contact authors located at centers outside of Denmark. The median sample size
was 151 (10th-90th percentile range, 28-935) for parallel-group trials, and
16 (10th-90th percentile range, 7-43) for crossover trials.
All but 3 trials were published in specialty journals rather than in
general medical journals—the latter being defined as those publishing
articles from any clinical field. Fifteen trials had more than 1 published
article. The publication year of the first article from each of the 102 trials
ranged from 1995 to 2003. Two appeared in 1995-1996; 13 in 1997; 52 in 1998-1999;
27 in 2000-2001; 7 in 2002; and 1 in 2003.
Across the 102 trials, we identified 3736 outcomes (median, 27 per trial;
10th-90th percentile range, 7-79) from the protocols and the published articles
(Figure 2). Ninety-nine trials measured
efficacy outcomes (median, 20; 10th-90th percentile range, 5-63 per trial),
and 72 trials measured harm outcomes (median, 6; 10th-90th percentile range,
1-31 per trial).
Only 48% (49/102) of trialists responded to the questionnaire regarding
unreported outcomes, 86% (42/49) of whom initially denied the existence of
such outcomes prior to receiving our list of unreported outcomes. However,
all 42 of these trials had clear evidence of unreported outcomes in their
protocols and in the published articles. None of the responders added any
unreported outcomes to the list we subsequently provided.
Among trials that measured efficacy or harm outcomes, 71% (70/99) and
60% (43/72) had at least 1 unreported efficacy or harm outcome, respectively
(ie, outcomes missing in "Results" sections of published articles but listed
in the protocols or in the "Methods" sections of the published articles).
In these trials, a median of 4 (10th-90th percentile range, 1-25; n = 70 trials)
efficacy outcomes and 3 (10th-90th percentile range, 1-18; n = 43 trials)
harm outcomes were unreported.
Among 78 trials with any unreported outcome (efficacy or harm or both),
we received only 24 survey responses (31%) that provided reasons for not reporting
outcomes for efficacy (23 trials) or harm (10 trials) in their published articles.
The most common reasons for not reporting efficacy outcomes were lack of statistical
significance (7/23 trials), journal space restrictions (7/23), and lack of
clinical importance (7/23). Similar reasons were provided for harm data.
Ninety-two percent (91/99) of trials had at least 1 incompletely reported
efficacy outcome, while 81% (58/72) had at least 1 incompletely reported harm
outcome. Primary outcomes were specified for 63 of the published trials, but
for 17 (27%) of these trials at least 1 primary outcome was incompletely reported.
The median proportion of incompletely reported outcomes per trial was 50%
(10th-90th percentile range, 4%-100%) for efficacy outcomes and 65% (10th-90th
percentile range, 0%-100%) for harm outcomes (Table 3). Incomplete reporting was common even when the total number
of measured trial outcomes was low, and was more common for crossover trials
than for parallel-group trials (Table 3).
Forty-nine trials could not contribute to the analysis of reporting
bias for efficacy outcomes because they had entire rows or columns that were
empty in the 2 × 2 table (analogous to a trial assessing mortality but
with no observed deaths); 54 trials were similarly noncontributory for harm
outcomes. Included trials were similar to excluded trials, except the former
had a lower proportion of crossover trials and a higher number of eligible
outcomes per trial. Six hundred ten of 2785 efficacy outcomes (22%) and 346
of 951 harm outcomes (36%) were ineligible for analysis because their statistical
significance was unknown; only 11 trialists provided information about whether
their unreported outcomes were statistically significant.
The odds ratio for outcome reporting bias in each trial is displayed
in Figure 3. The pooled odds ratio
(95% confidence interval) for trials of any design was 2.4 (1.4-4.0) for efficacy
outcomes and 4.7 (1.8-12.0) for harm outcomes (Table 4). Thus, the odds of a particular outcome being fully reported
was more than twice as high if that outcome was statistically significant.
Stratifying by study design, or excluding survey nonresponders or physiologic/pharmacokinetic
trials, had no important impact on the odds ratios (Table 4). Dichotomizing the level of reporting differently by combining
fully reported with partially reported outcomes increased the degree of bias
(Table 4). Exploratory meta-regression
analysis did not reveal any significant associations between the magnitude
of bias and the source of funding, sample size, or number of study centers.
Formal protocol amendments involving study outcomes were submitted to
the ethics committee for approval for 7 trials. Most changes involved secondary
outcomes, with a primary outcome being formally amended in only 2 trials.
Primary outcomes were defined for 82 of the 102 trials (80%), either in the
protocol or in the published articles. Among 63 trials defining primary outcomes
in their published articles, 39 (62%) defined 1 primary outcome, 7 (11%) defined
2, and 17 (27%) defined more than 2.
Overall, 51 of the 82 trials (62%) had major discrepancies between the
primary outcomes specified in protocols and those defined in the published
articles (Table 5). Specific examples
of major discrepancies are shown in Box 2. For 26 trials, protocol-defined primary outcomes were reported
as nonprimary in the published articles, while for 20 trials primary outcomes
were omitted. For 12 trials, outcomes that had been predefined as nonprimary
in the protocol were called primary in the published articles. For 11 trials,
new primary outcomes that were not even mentioned in the protocol appeared
in the published articles. None of the published articles for these trials
mentioned that an amendment had been made to the study protocol. Sixty-one
percent of the 51 trials with major discrepancies were funded solely by industry
sources, compared with 49% of the 51 trials without discrepancies.
Outcome (eg, percentage of patients with severe cerebral bleeding) changed
from primary to secondary Outcome (eg, mean pain intensity) changed
from primary to unspecified Prespecified primary outcome (eg, event-free
survival rate) omitted from published reports Outcome (eg, overall
symptom score) changed from secondary to primary Outcome (eg, percentage
of patients with graft occlusion) listed as a new primary outcome (ie, not
mentioned in the protocol)
*Specific details of primary outcomes omitted to maintain anonymity.
Among the 51 trials with major discrepancies in primary outcomes, 16
had discrepancies that favored statistically significant primary outcomes
in the published articles, while 14 favored nonsignificant primary outcomes
(see the "Methods" section for definition of "favored"). Eleven trials had
several discrepancies that favored a mixture of significant and nonsignificant
results, while for 10 trials the favored direction was unclear due to a lack
of survey data about statistical results for unreported primary outcomes.
When published, 38 trials reported a power calculation, but 4 calculations
were based on an outcome other than the one used in the protocol. In another
6 cases, there was a power calculation presented in a published article but
not in the protocol.
To our knowledge, this study represents the first empirical investigation
of outcome reporting bias in a representative cohort of published randomized
trials. The cohort was restricted only by the geographic location of the ethics
committee, although many studies involved sites in other countries. A unique
feature of the study was our unrestricted access to trial protocols, which
provided an unbiased a priori description of study outcomes. Protocols and
published reports of systematic reviews have been compared previously,18,19 but similar assessment of primary
research has been limited to case reports,20-22 a
pilot study that required permission from researchers to access their ethics
protocols,2 and a recent study of nonindustry
trials conducted by a large oncology research group.23 Other
studies have compared published articles with final reports submitted to drug
We found that incomplete outcome reporting is common. On average, more
than one third of efficacy outcomes and one half of harm outcomes in parallel-group
trials were inadequately reported; the proportions were much higher in crossover
studies due to unreported paired data. Even primary outcomes were often incompletely
reported. Furthermore, the majority of trials had unreported outcomes, which
would have been difficult to identify without access to protocols. Such poor
reporting not only prevents the identification and inclusion of many essential
outcomes in meta-analyses but also precludes adequate interpretation of the
results in individual trials.
Our findings are likely underestimates due to underreporting of omitted
outcomes by trialists, with 86% of survey responders initially denying the
existence of unreported outcomes despite clear evidence to the contrary. This
surprisingly high percentage suggests that contacting trialists for information
about unreported outcomes is unreliable, even despite our simply worded questionnaire.
We also reviewed all primary and secondary published articles for a trial;
if only the primary article had been reviewed, more trial outcomes would have
been classified as unreported.
The adoption of evidence-based reporting guidelines such as the revised
CONSORT statement26 for parallel-group trials
should help improve poor outcome reporting. The guidelines advise reporting
"for each primary and secondary outcome, a summary of results for each group,
and the estimated effect size and its precision."26
Statistically significant outcomes had more than a 2-fold greater odds
of being fully reported compared with nonsignificant outcomes. As an example,
an odds ratio of 2.4 corresponds to a case in which 71% of significant outcomes
are fully reported, compared with only 50% of nonsignificant outcomes. The
degree of bias observed was robust in sensitivity analyses and was not associated
with funding source, sample size, or number of study centers. The magnitude
of outcome reporting bias is similar to that of publication bias involving
entire studies, which was found to be an odds ratio of 2.54 in a meta-analysis
of 5 cohort studies.27
It should be noted that the estimated magnitude of outcome reporting
bias in each trial varied widely (Figure 3); the pooled odds ratio therefore cannot be applied to reliably
predict the degree of bias for a given study.
Many trials were excluded from the analysis because odds ratios could
not be meaningfully calculated due to empty rows or columns in the 2 ×
2 table. For example, if a trial did not have any fully reported outcomes,
then it was not possible to compare fully reported outcomes with incompletely
reported ones. Trials were therefore more likely to be included in the analysis
if they had variability in the level of reporting and/or statistical significance
across outcomes, such that fewer cells were empty in the 2 × 2 table.
Accordingly, we found that included trials had a higher number of eligible
outcomes and that fewer crossover trials were included, as these often did
not contain any fully reported outcomes.
The purposes of prespecifying primary outcomes are to define the most
clinically relevant outcomes and to protect against "data dredging" and selective
reporting.8,28 Also, the primary
outcome will generally be used for the calculation of sample size. This protective
mechanism is no longer functional if predefined outcomes are subsequently
changed or omitted. Despite incorporating into our analyses the few protocol
amendments relating to outcomes that were submitted to the ethics committee,
we found that 62% of the trials had major discrepancies for primary outcomes.
Although there is little doubt that making major changes to primary
outcomes after trial commencement creates the potential for bias, the rationale
behind such changes is not always clear. A preference for statistically significant
results is one obvious explanation, but since few trialists provided us with
the statistical significance of unreported outcomes, we could rarely ascertain
whether changes to primary outcomes were made in favor of statistically significant
results. Evidence of such bias was observed in one third of the trials with
discrepancies in our sample, but many of the remaining trials contained discrepancies
that favored a combination of significant and nonsignificant results, while
others contained discrepancies that favored unclear directions or nonsignificant
A second explanation for the occurrence of discrepancies favoring nonsignificant
outcomes could be that our analysis did not distinguish which treatment group
was favored by the significant difference, and significant results may have
been omitted if they favored the control treatment. A third explanation is
that the results for other outcomes in the trial may have influenced whether
statistical significance was considered important for a particular outcome.
For example, an outcome may have been omitted if it was inconsistent with
other trial outcomes.
It is also possible that we misclassified some changes as favoring nonsignificant
primary outcomes because of our rigid cutoff of P =
.05 used to distinguish between significant and nonsignificant results, as
researchers may regard a P value of .06 as sufficiently
interesting to report. In addition, nonsignificance may sometimes have been
the desired result, particularly for harm outcomes or equivalence trials.
Furthermore, some of the apparent changes may be attributable to deficiencies
in protocols rather than to biased actions of researchers. For example, in
4 of 10 trials in which the specification of outcomes was changed from unspecified
to primary, no primary outcomes were defined in the protocol. In addition,
researchers may not have realized that the protocol specifies how the data
will be analyzed, and that the term "primary" should refer only to prespecified
primary outcomes rather than to outcomes chosen post hoc as having the most
importance or interest.
Finally, it is possible that some of the discrepancies occurred for
valid reasons. After trial commencement, the omission of a predefined primary
outcome can be justified if a logistical obstacle impedes its measurement
or if new evidence invalidates its use as a reliable measure. However, the
potential for bias still exists whenever changes are made to prespecified
outcomes after trial recruitment begins. The reporting of protocol amendments
in published articles must therefore be routine to enable a critical evaluation
of their validity, as endorsed by the revised CONSORT statement and by other
to do so has been described by one journal editor as a "breach of scientific
conduct."32 Unfortunately, none of the trial
reports in our cohort acknowledged that major protocol modifications were
made to primary outcomes, despite the fact that an agreement between the Danish
Medical Association and the Association of the Danish Pharmaceutical Industry
explicitly states that "the data analyses upon which the publication is based
must be in agreement with the trial protocol, which must describe the statistical
methods" (our translation).33
The survey response rate was relatively low. The number of unreported
outcomes identified would therefore be underestimated. Missing data on statistical
significance also necessitated the exclusion of many outcomes from our calculation
of odds ratios. However, the questionnaires constituted a secondary source
of data, as we relied primarily on more objective information from protocols
and published articles. Furthermore, we assume that trialists would have been
more likely to respond if their outcome reporting was more complete and less
biased. Any response bias would thus result in conservative estimates of reporting
deficiencies in our cohort.
Outcome reporting bias acts in addition to the selective publication
of entire studies and has widespread implications. It increases the prevalence
of spurious results, and reviews of the literature will therefore tend to
overestimate the effects of interventions. The worst possible situation for
patients, health care professionals, and policy-makers occurs when ineffective
or harmful interventions are promoted, but it is also a problem when expensive
therapies, which are thought to be better than cheaper alternatives, are not
In light of our findings, major improvements remain to be made in the
reporting of outcomes in randomized trials as published. First, protocols
should be made publicly available—not only to enable the identification
of unreported outcomes and post hoc amendments30,31,34 but
also to deter bias. Ideally, protocols should be published online after initial
trial registration and prior to trial completion. Although journals constitute
one obvious modality for protocol publication, academic and funding institutions
should also take responsibility in providing further venues for disseminating
Second, deviations from trial protocols must be described in the published
articles so that readers can assess the potential for bias. Third, journal
editors should not only consider routinely demanding that original protocols
and any amendments be submitted with the trial manuscript but that this material
should also be provided to peer reviewers and preferably be made available
at the journal's Web site.20,21,36
Finally, trialists and journal editors should bear in mind that most
individual trials may well be incorporated into subsequent reviews. Outcomes
that are mentioned in published articles, but are reported with insufficient
data, may not always matter when interpreting a single trial report, but they
can have an important impact on meta-analyses. Unreported outcomes are even
more problematic for both trials and reviews. It is therefore crucial that
adequate data be reported for prespecified outcomes independent of their results.
The increasing use of the Internet by journals may help to provide the space
needed to accommodate such data.36
In summary, we found that the reporting of trial outcomes in journals
is frequently inadequate to provide sufficient data for interpretation and
meta-analysis, is biased to favor statistical significance, and is inconsistent
with primary outcomes specified in trial protocols. These deficiencies in
outcome reporting pose a threat to the reliability of the randomized trial