Effect of the Statistical Significance of Results on the Time to Completion and Publication of Randomized Efficacy Trials FREE

SEVERAL INVESTIGATORS have raised concerns that clinical studies with negative results may never be published and their failure to appear in the literature may distort the picture we obtain from clinical experiments about the optimal practice of medicine.^{1 - 5} However, ascertaining the extent of this bias is difficult. Retrieving information about lost studies is a challenge.^{3 - 6} Prior research has been based on retrospective interviews about the fate of research protocols located through questionnaires,⁶ meeting abstracts,⁷ or archives of institutional boards or funding organizations.^{1 - 2 ,5} Prospective evaluation of the phenomenon with detailed trial registries⁸ gathering information on all the implementation milestones of randomized trials (onset, completion of enrollment, completion of follow-up, submission, and publication) has not been accomplished. Also most prior investigations have applied the term publication bias indistinguishably to phase 1, 2, and 3 trials and to both randomized and nonrandomized studies. However, the loss of information from a small, unrevealing pilot or observational study is not comparable to the disappearance of the results of randomized efficacy trials, which form the mainstream of evidence for medical practice. Such loss of information could affect systematic reviews, the decisions of funding agencies, and the outcomes of patients.

From retrospective investigations, it remains unclear whether publication bias affects specifically phase 2 and 3 trials to a substantial extent.^{1 ,4} Moreover, since many efficacy trials perform interim analyses during their conduct and may be prematurely interrupted if significant results are seen, it is unknown whether the results of a study would affect not only the time to publication after completion, but also the time a trial takes to be completed. Until now it has not been possible to address this last question with retrospectively constructed databases. Knowledge of the exact natural history of efficacy trials is needed to provide an accurate perspective on how medical evidence is obtained and whether there is a time lag between studies with "positive" and "negative" results.

The best insight into the fate of clinical trials can be gained from trial databases that collect prospectively information about the conduct of all studies in a given domain. Such an approach can offer a perspective on the natural history of clinical trials from inception through completion to publication. In this article detailed information from a large database of clinical trial protocols was used with data on the implementation milestones and publication dates of registered trials. This allowed assessment of the natural history of randomized efficacy trials in the domain of human immunodeficiency virus (HIV) infection and its complications, a discipline of rapidly expanding therapeutics with intense clinical research activity.

All efficacy clinical trials conducted from 1986 until 1996 by the AIDS [acquired immunodeficiency syndrome] Clinical Trials Group (ACTG) and by the Terry Beirn Community Programs for Clinical Research on AIDS (CPCRA) were considered in the analysis. These trial groups sponsored by the Division of AIDS of the National Institute of Allergy and Infectious Diseases (NIAID) represent globally the largest networks for the conduct of clinical trials on HIV infection and its complications. ACTG uses the resources of 30 university sites across the United States as well as other collaborative clinical units. The CPCRA is a community-based program encompassing more than 160 clinical practices across the United States. All protocols and detailed dated information on their implementation and presentation are archived by the Division of AIDS. Supplemental information about recently analyzed trials and clarifications on unclear or missing data were obtained from investigators and medical officers and staff responsible for the protocols.

The analysis was limited to randomized trials addressing the efficacy of the compared interventions (phase 2 and phase 3 trials). Observational, nonrandomized, pharmacokinetic, and safety phase 1 and phase 1/2 studies were excluded as well as substudies of the main protocols. Qualification for inclusion and recording of study design factors (including target sample size, end points, designation of phase, blinding, and data management) was based on examination of the complete protocols archived in the Division of AIDS, which offered a distinct advantage to avoid bias in recording as compared with interviews, questionnaires, and data extraction from abstracts that have been used in previous investigations of publication bias.^{1 - 7} Trials were selected regardless of whether they compared a regimen with placebo, different regimens, or different doses of the same medication. All protocols that enrolled any patients have been registered. The considered implementation milestones included the dates of starting enrollment, completion of follow-up, submission for peer-reviewed publication, and publication. For studies that continued follow-up beyond their primary analysis and publication, follow-up was censored at the time of the primary analysis. For 9 early studies, exact dates for completion of follow-up were not available but could be approximated with high accuracy from data on closure to enrollment and trial follow-up. All data were censored for analysis on October 10, 1996.

In this article, a trial is called "positive" if a statistically significant finding (denoted by P<.05) had been found in the analysis of the data for a main efficacy end point defined in the protocol in favor of an experimental therapy arm. Trials with nonstatistically significant findings or favoring the control arm are called "negative." Whenever there was no distinct control (traditional therapy) arm, a study was called positive if it showed a statistically significant finding in favor of any arm. When multiple major efficacy end points were available, the trial was considered positive if any major efficacy end point reached statistical significance. In 2 trials, significance favored different arms for survival and another end point; these trials were classified according to the direction of the survival results. The availability of the complete archived protocols and trial reports minimized the chances for subjective interpretation of end points and trial results. For further quality assurance, a random selection of 12 protocols and trial reports was evaluated by another colleague who was blinded to the study milestones. There was agreement in determination of pertinent end points and classification of significance between the author and the second independent observer in all cases.

Time-to-event analyses were performed with the Kaplan-Meier method, and comparisons used the log-rank test. The significance levels of the findings and other trial characteristics were used as covariates for the risk of publication in Cox proportional hazards regressions. Trial characteristics included the actual sample size, the ratio of accrual compared with originally anticipated (target) enrollment (typically based on power calculations), the trialist group, the age of the population (adult or pediatric), the trial domain (antiretroviral therapy vs complications of HIV), the presence or not of double blinding, and the place where data were managed (pharmaceutical industry or other). Both univariate and multivariate models and interactions between variables were assessed, but only univariate regressions are reported since the results of the multivariate regressions were similar and no significant interactions were identified. Statistical analyses were run on SPSS software, version 6.0 (SPSS, Inc, Chicago, Ill). All reported P values are 2 tailed.

A total of 109 randomized efficacy trials with total enrollment of 43708 patients qualified for the analysis. Of these, 8 were closed, having failed to accrue more than 20 patients, and are excluded from all subsequent analyses. Typically the conduct of these 8 trials became unfeasible or futile, and no publishable evidence materialized. Of the remaining 101 trials, 25 were still open to accrual, 10 were closed to accrual and continuing follow-up, and 66 trials with 30715 patients had been completed; 36 of the 66 completed trials had been published (18 at the New England Journal of Medicine, 6 in the Annals of Internal Medicine, 5 in the Journal of Infectious Diseases, and 1 each in 7 other journals) at the time data were censored for analysis. Of the 30 completed but unpublished trials, 9 had been submitted at least once for publication, and 8 more had been completed less than 1 year ago. Characteristics of the trials are shown in Table 1.

In a Kaplan-Meier analysis, the median time to publication among the 101 analyzed trials was estimated to be 5.5 years from the time a trial started enrollment (interquartile range, 3.9-7.0 years). On average, the time it took to conduct a study was of similar magnitude as the time it took to publish the results after its completion. The median time from starting until completing follow-up was 2.6 years (interquartile range, 2.0-3.8 years). Among the 66 completed trials, the median time from completion of follow-up to publication was 2.4 years (interquartile range, 1.6-3.8 years).

Overall, positive trials were published significantly earlier than trials with negative findings (Figure 1, A; log-rank P<.001). The median time from starting enrollment to publication was 4.3 years for positive trials vs 6.5 years for negative trials (mean, 4.2 vs 6.4 years). As shown in Figure 1, B, this time lag was largely attributable to differences between positive and negative trials in the time from completion of follow-up to publication (median, 1.7 vs 3.0 years; mean, 1.8 vs 3.6 years; log-rank P <.001).

Conversely, as shown in Figure 1, C, positive and negative trials differed little in the time they took to complete their follow-up (log-rank P=.17). However, when all trials with statistically significant results were considered regardless of whether the experimental or control arm was favored, these trials completed follow-up slightly faster than trials with nonsignificant results (Figure 1, D; log-rank P=.045). The absolute difference was not large (median, 2.3 vs 2.5 years; mean, 2.3 vs 2.8 years). To avoid the possible bias that trials still continuing follow-up at the censoring date may be more likely to be negative, a separate analysis included only the 50 trials that had started before June 30, 1992, and had all been completed by the time of analysis. Trials with significant results were completed slightly earlier (median, 2.3 vs 2.7 years; mean, 2.4 vs 3.0 years; log-rank P =.02).

The time-to-completion difference was probably important mostly for some early interrupted trials and some trials that had protracted enrollment and follow-up. Ten trials completed follow-up within less than 18 months from starting: 4 ran their prespecified course within this period of time; 1 was interrupted prematurely because of the surfacing of the significant results of a similar trial; and 5 trials were stopped early because of significant differences in either survival or clinical outcomes (n=4) or both efficacy and toxicity (n=1). On the other end, 12 trials had taken more than 4 years to complete follow-up: 2 were still trying to accrue patients, and another 9 were protracted because of lower than anticipated event rates in interim analyses despite full accrual; only 1 trial had an anticipated event rate.

Of the 8 trials not published at 6 years after starting enrollment, 5 had a prolonged enrollment and follow-up period (3.8-6.5 years) because of lower than anticipated event rates. Seven of the 8 trials had negative results. In contrast, the 5 trials published within less than 3 years from starting enrollment were all interrupted prematurely on the basis of early differences in efficacy between the arms in interim analyses (2 favoring the defined experimental arm, 2 favoring 1 of the arms, 1 favoring the defined control arm) and were all subsequently published in prestigious journals (New England Journal of Medicine, n=4; Annals of Internal Medicine, n=1).

Table 2 shows that significance of results was the only major determinant of the time from starting enrollment to publication for a clinical trial. The rate of publication was 3.7 (95% confidence interval [CI], 1.8-7.7) times higher for positive trials compared with negative ones, and the difference was explained again mostly by differences in the rapidity of publication after trials had been completed. The magnitude of the effect was unchanged in multivariate analyses adjusting for other trial characteristics (odds ratio, 4.9 [95% CI, 2.1-11.0]). Interestingly, large trials with more than 1000 patients took the same time to be published (if not less) than smaller trials. Large trials took probably a longer time to complete than smaller trials (P=.12), but their time to publication after completion was significantly shorter (P=.02). Using study accrual as a continuous variable, the rate at which a trial was completed decreased 1.8-fold (95% CI, 1.0-3.3) per 1000 patients, but the rate at which a trial was subsequently published after completion increased 2.5-fold (95% CI, 1.3-4.5) per each 1000 patients. Another interesting feature is that trials with data management performed by the pharmaceutical industry were of shorter duration (P<.001), but this did not expedite their overall time to appearance in the peer-reviewed literature (P=.33). There was no significant correlation between the presence of statistical significance, study accrual, and whether the data were managed by the industry or not (all correlation coefficients <0.2 in absolute value), but it should be remembered that trials were still monitored by NIH.

Underpowered trials that accrued less than half of their required prespecified target sample size (which was typically based on a priori power calculations) were published as fast as trials that had reached closer to their target sample size, although a moderate difference may have been missed in this analysis (odds ratio, 1.2 [95% CI, 0.4-3.5]). Among the 43 completed trials that had enrolled at least 90% of their prespecified target sample size, positive trials were still published substantially more rapidly than negative ones (log-rank P <.001).

Among the 66 completed trials, 45 had been submitted for publication by the time data were censored. The median time to first submission was 1.4 years after completion (interquartile range, 0.7-2.3 years), and the median time to publication was 0.8 year after submission (interquartile range, 0.6-1.4 years). Positive trials were submitted significantly more rapidly compared with trials with negative results (mean, 1.0 vs 2.4 years; median, 1.0 vs 1.6 years; log-rank P =.001; Figure 2, A). A similar time lag was observed when trials with significant results favoring any arm were compared with trials with nonsignificant results (mean, 1.3 vs 2.4 years; median, 1.0 vs 1.6 years; log-rank P =.008). Data were managed by the industry in 2 of the 3 negative studies that had not yet been submitted despite a lapse of more than 3.5 years after their completion. After submission, positive trials were also published more rapidly than negative trials, but the time lag was relatively smaller (for both mean and median, 0.8 vs 1.1 years; log-rank P=.04; Figure 2, B).

Of the 45 submitted trials, 17 were rejected by at least 1 journal. At least 4 negative trials with over 300 patients each were rejected 2 or 3 times, while no positive trial was rejected multiple times. There was a trend that positive results might increase the odds of acceptance on the first submission (odds ratio, 1.6 [95% CI, 0.5-5.6]), but this was far from being formally significant (P=.54 by the Fisher exact test).

Among the 36 published trials, there was a moderately strong correlation between the time from completion to submission and the time from submission to publication (r=0.50; P =.002). These 2 time intervals were not significantly different across the published trials (mean difference, 0.2 year; P=.09 by t test).

This analysis shows that, even within multicenter trial groups of high efficiency, randomized efficacy trials are published more rapidly when results reach traditional levels of statistical significance. Negative studies suffer a substantial time lag. With some exceptions, most of this lag is generated after a trial has been completed. On the average, the time it takes to publish the results of efficacy trials, positive or negative, is of the same magnitude as the time it takes to actually conduct them.

This analysis extends the observations of earlier retrospective investigations of publication bias that claimed that investigators were not interested in the publication of small, negative trials.^{1 ,3 - 4 ,6} Earlier investigations have not agreed on the extent of publication bias for randomized trials,^{1 - 2} and the distinction between efficacy trials and early phase 1 and 1/2 trials could not be made clearly with retrospective approaches. For efficacy trials, publication lag may be a more exact term than publication bias, and this is most accurately described with a survival analysis approach. The effect of this publication lag can still be important, however. Trial results may be outdated when published belatedly. Rapid advances in technology and changes in the patient populations⁹ and clinical practice decrease the importance of the conveyed information. This is particularly true in rapidly evolving fields such as HIV therapeutics, where even significant findings become rapidly outdated. Publication lag drastically reduces the value of the provided evidence and introduces bias over time since the publication of positive results tends to antedate the surfacing of negative findings.

Besides proper peer-reviewed publication, information is disseminated by meetings, preliminary non–peer-reviewed presentations, and pharmaceutical advertisement. The extent of bias in non–peer-reviewed mechanisms of disseminating information is unknown, but unavoidably advertisement is fed preferentially by positive results,¹⁰ and prior investigators have suggested that meetings favor positive results.¹¹ Beyond doubt, medical advances should draw prompt, strong attention. However, there is a concern that, in the rapidly changing face of medicine, positive trials may one-sidedly dominate our information system, as their negative counterparts take longer to appear, typically with less or no advertising glare around them. There are several examples where, on the same topic, positive trials caused early excitement, followed later by disappointing or less promising counterparts. Typical examples in HIV disease (Table 3) include the use of early zidovudine monotherapy in asymptomatic patients,^{12 - 14} acyclovir,¹⁵ ditiocarb (Imuthiol),^{16 - 17} and oral ganciclovir prophylaxis,¹⁸ where positive and negative trials started at about the same time, but negative studies appeared later^{14 ,17} or are still unpublished. Thus, a wave of enthusiasm is sometimes followed by a wave of disappointment or skepticism. Early systematic reviews of the accumulating evidence may give misleading results. An investigation in HIV-related trials, in particular, has shown that meta-analyses including only the published evidence would have found sizable treatment benefits for several controversial or even abandoned treatments,¹⁹ while in the case of zidovudine, a meta-analysis of the early published, short-term trials would suggest markedly more favorable results compared with the pooled treatment effect of the trials with longer follow-up that appeared later.²⁰

Many phase 3 trials use sequential preplanned interim analyses to ensure that early differences between arms are not missed,^{21 - 22} and thus, positive trials may be interrupted prematurely while negative trials may be further protracted. This analysis shows that, with some exceptions, this approach does not have a major direct impact on the timing of most clinical trials. Exceptions do exist, mostly for trials at the 2 extremes: all the efficacy trials published within less than 3 years from opening to enrollment had been prematurely interrupted on the basis of interim analyses, while prolonged enrollment and follow-up, often because of slowly accrued events, was common in trials languishing for more than 6 years.

Publication delays for negative trials occur largely after the trial completion. Delays can be substantial even in multicenter trial groups with strict publication policies and high efficiency. As part of the ACTG and CPCRA standards of practice, strong incentives to publication are offered, including credit in the competitive renewal of funding for the site of the principal investigator. Similarly, disincentives to negligent investigators include potential dismissal from authorship and exclusion from chairmanship of future protocols. It is possible that publication lag may be more pronounced for trials conducted by groups not dependent on federal funding and for trials where the sponsor has a financial interest in the outcome.^{23 - 24} Future analyses should try to address prospectively whether the natural history of efficacy trials is different under these less ideal circumstances.

The observed average delay for negative findings after submission to peer review seemed small in this analysis, but it should be acknowledged that it could be an underestimate. Among published trials, the time to submit correlated fairly strongly with the time to be published. It is unknown whether negative trials whose submission had been deferred by the censoring date in this analysis might have similarly been deferred publication after an eventual submission. Also, multiple rejections seemed to cluster among negative trials.

Three more points warrant discussion. First, this analysis shows that, under the current circumstances, evidence from large trials becomes available in the peer-reviewed literature as fast as evidence from smaller trials. Large trials take longer to complete, but then they surface much more rapidly. The relative merits of small vs large trials have often been debated.²⁵ With limited resources and rapid changes in medicine, large trials with prolonged follow-up are a challenge to design and conduct in many medical disciplines, including HIV disease. However, if small trials are to offer an advantage over larger trials, their results should be submitted to peer review and published promptly. Otherwise, a few large trials may be preferable to small trials presented in non–peer-reviewed sources and potentially affected by publication lag and bias.

Second, publication lag and bias may increase under circumstances where positive results accumulate rapidly, leaving even less interest for studies with inconclusive or less spectacular findings. Currently, with a geometric increase in the available therapeutic options in many medical disciplines, including HIV infection, it is possible that the light of publicity may fall even earlier and more heavily on the most positive results, probably even for trials considering the same or comparable regimens. The extent of publication lag should be addressed with similar methods in other domains besides HIV infection to examine its extent in less rapidly evolving specialties.

Third, publication lag may affect evidence-based medicine and systematic reviews and may lead to spuriously larger treatment effects in early meta-analyses of the available evidence. Meta-analyses should be aware of ongoing studies that may influence their conclusions. Late-appearing trials are more likely to show nonsignificant results. Lack of significance could be attributable either to smaller treatment effect estimates or to lower event rates resulting in wider CIs. In this registry, delay in completion and publication because of low event rates and slow accrual of events was a common occurrence. Differences between early- and late-appearing trials could reflect heterogeneity in the trial protocols and the disease risk of the studied patient populations.²⁶ Cumulative meta-analysis may be used to evaluate systematically the extent of the impact of late negative trials,²⁷ and reasons for discrepancies between early meta-analyses and late-appearing trials should be studied systematically.²⁸

Enthusiasm about the results of clinical research should not be based on its P value.²⁹ Clinical trials and meta-analyses provide a continuum of evidence and nondefinitive trials may provide as important information as trials with high levels of statistical significance when seen in the context of other pieces of evidence. It is still very questionable what really optimizes clinical care, but the results of properly conducted trials are definitely a cornerstone in the process. Equipoise in the presentation of all results is important for an objective evaluation of the accumulated evidence.