 Technical advance
 Open Access
 Published:
True and false positive rates for different criteria of evaluating statistical evidence from clinical trials
BMC Medical Research Methodology volume 19, Article number: 218 (2019)
Abstract
Background
Until recently a typical rule that has often been used for the endorsement of new medications by the Food and Drug Administration has been the existence of at least two statistically significant clinical trials favoring the new medication. This rule has consequences for the true positive (endorsement of an effective treatment) and false positive rates (endorsement of an ineffective treatment).
Methods
In this paper, we compare true positive and false positive rates for different evaluation criteria through simulations that rely on (1) conventional pvalues; (2) confidence intervals based on metaanalyses assuming fixed or random effects; and (3) Bayes factors. We varied threshold levels for statistical evidence, thresholds for what constitutes a clinically meaningful treatment effect, and number of trials conducted.
Results
Our results show that Bayes factors, metaanalytic confidence intervals, and pvalues often have similar performance. Bayes factors may perform better when the number of trials conducted is high and when trials have small sample sizes and clinically meaningful effects are not small, particularly in fields where the number of nonzero effects is relatively large.
Conclusions
Thinking about realistic effect sizes in conjunction with desirable levels of statistical evidence, as well as quantifying statistical evidence with Bayes factors may help improve decisionmaking in some circumstances.
Introduction
For over half a century, the US Food and Drug Administration (or FDA) has been one of the primary regulatory agencies worldwide when it comes to providing quality control of new drugs and biologics, or medications, for clinical use [1]. Included in the many responsibilities of the FDA is the endorsement of new medications. Endorsement of new medications is a rigorous process that follows many stages of multiple clinical trials. Data in each of these trials is evaluated, typically independently, by conducting some form of statistical inference. Typically, some null hypothesis is postulated, stating that the new medication is ineffective (more precisely, works similarly to a placebo medicine without any active component). This hypothesis is then evaluated using a Null Hypothesis Significance Test, which quantifies the probability of obtaining data with an effect at least as strong as that in the data at hand using a pvalue. The effect is typically considered statistically significant when a twosided test yields a pvalue lower than 0.05 and the effect is in the expected direction [2, 3]. In order to mitigate the risk of incorrectly concluding effectiveness, the FDA typically requires “… at least two adequate and wellcontrolled studies, each convincing on its own, to establish effectiveness.” (p. 3) [4].
In previous work [5], we showed with simulations that using a criterion of at least two statistically significant trials, quantified by pvalues lower than 0.05, leads to inconsistent strength of evidence in different circumstances. In particular, we demonstrated that for cases when many clinical trials were conducted out of which exactly two were statistically significant (say, 2 out of 5), the decision to endorse can be much improved by quantifying the evidence of all trials (not just the statistically significant ones) and a natural, convenient way to do this would be by using Bayes factors [6]. In scenarios where blind application of a criterion of two significant trials would always lead to endorsement, Bayes factors would lead to different inferences depending on the presumed underlying population effect.
The scenario of endorsement of medication following a number of registered clinical trials (RCTs) of which only a minority has been statistically significant at a pvalue threshold of < 0.05 is not uncommon for certain groups of medication. For instance, in the field of antidepressants, citalopram was endorsed following 5 RCTs of which only 2 were statistically significant (the nonsignificant trials had pvalues ranging from 0.224 to 0.964). Sertraline similarly was endorsed following 5 RCTs of which only 1 (or 2, if one counts a trial with three ‘subtrials’ of which only one was statistically significant) was statistically significant (the nonsignificant trials had pvalues ranging from 0.21 to 0.87). The antidepressant mirtazapine was endorsed following 10 RCTs of which 5 were statistically significant (the nonsignificant trials had pvalues ranging from 0.19 to 0.49). Finally, bupropion was endorsed after 3 RCTs, only one of which was statistically significant (the nonsignificant trials had pvalues ranging from 0.16 to 0.53). More details of the FDA registered data of these clinical trials for these medications can be found in [7] (see also [8] for a Bayesian metaanalysis).
The endorsement of new medications is certainly not a purely statistical process alone and it is not using simply an automated count of statistically significant results. Aside from numerically evaluating the efficacy of the main outcome, usually careful thought is given to potential side effects, the urgency of the availability of a new treatment, and a qualitative evaluation of the design, conduct and findings in each of these RCTs. A nuanced assessment of the global evidence takes place before reaching licensing decisions. Some guidance exists in this regard, but details may be applied differently in each case and translating results from clinical trials into a licensing decision can be convoluted. Nevertheless, the statistical evaluation is an important centerpiece of the endorsement process, so care should be taken for this component to evaluate the available evidence as optimally as possible, before other considerations are superimposed.
There are many ways one may define optimal evaluation of the available evidence. One could seek to minimize the endorsement of ineffective medications, or false positives (the equivalent of maximizing true negatives: not endorsing ineffective medications, see e.g., [9]). An advantage of such a criterion is that most of the medications that become available to the market will work. However, setting too stringent a criterion of this type might lead to many effective medications not passing the bar for endorsement, leading to patients being deprived of potentially effective treatment. A different criterion would be to maximize true positives (the equivalent of minimizing false negatives). Such a policy would prioritize making all working medications available in the market, at the cost of having some ineffective medications pass through as well. Within any kind of statistical evaluation tool, these two criteria typically trade off against one another, but across different statistical inferential methods, dominant approaches are theoretically possible, where one method offers higher true positive rates without necessarily offering a higher false positive rate.
In this paper, we examine the consequences of using a statistical evaluation criterion of two significant trials for the true and false positive rates in the specific case where exactly five trials were conducted (e.g., a situation seen in the citalopram scenario). We compare these to two alternatives: quantifying all available evidence with confidence intervals based on a summary effect size measure obtained from metaanalysis, and with Bayes factors. For both the null hypothesis significance test and the Bayesian test, choices need to be made for the threshold of evidence that would trigger endorsement. The null hypothesis test traditionally uses an α of 0.05, but recently a lower α of 0.005 was proposed [10]. No consensus exists for the Bayesian threshold of endorsement, although criteria of Bayes factors of 20 [11] and 10 [12] have been proposed as a threshold for strong evidence. We conducted simulations, varying the number of clinical trials that were conducted, the distribution of true effect sizes in the population, the number of participants per randomized control, the statistical evaluation method, the threshold for quantifying statistical evidence, and the threshold for an effect being considered clinically meaningful. We evaluated the outcomes by looking at the true positive and false positive rates simultaneously.
Method
We conducted simulations for the scenarios of 2 clinical trials, 3 clinical trials, and 5 clinical trials. For each of these scenarios, we conducted four sets of simulations. For every set, we generated 8000 data sets of 2, 3, or 5 clinical trials each (a total of 16,000, 24,000, or 40,000 trials, depending on the scenario). All of the data sets were intended to mimic two–condition between–subjects experiments with an experimental group and a control (e.g., placebo) group. The four sets of simulations differed in the distribution of true population effect sizes between the two groups. For all sets of simulations, there was a distribution of nonzero effect sizes, normally distributed with a mean of 0.4 (a small to moderate effect) and a standard deviation of 0.13. For the first three sets of simulations, there additionally was a number of zeroeffects. The sets differed in the relative frequency of nonzero and zero effects: the first set of simulations had a 25% occurrence rate of null effects, the second set of simulations had a 50% occurrence rate of null effects, the third set of simulations had a 75% occurrence rate of null effects, and the fourth set of simulations did not include any null effects. These different numbers reflect different rates of ‘apriori optimism’ of the occurrence of true effects (25, 50, 75, and 0%) among medications subjected to stage III trials that try to secure licensing. Throughout the paper, we work with effect sizes in standardized form to facilitate computations and allow for comparison across results. For specific cases, effect sizes can be reexpressed in absolute form by multiplying by the standard deviation. Of note, standardized effects of the same magnitude may be clinically actionable in some cases, but not in others, depending on what the standard deviation is, what outcome they pertain to, and what the riskbenefit involved is.
Therefore, our simulations are:
p_{123} ~ N (0, 1)
Set 1: 25% of e_{1} ~ N (0, 1); 75% of e_{1} ~ N(δ, 1)
Set 2: 50% of e_{2} ~ N (0, 1); 50% of e_{2} ~ N(δ, 1)
Set 3: 75% of e_{3} ~ N (0, 1); 25% of e_{3} ~ N(δ, 1)
Set 4: e_{4} ~ N(δ, 1)
δ ~ N (0.4, 0.13)
where p_{123} indicates simulated data for the placebo groups in all sets of simulations; e_{1}, e_{2}, e_{3}, and e_{4} indicate simulated data for the experimental groups in the first, second, third, and fourth set of simulations respectively; and where δ indicates the population effect size for a given iteration. The notation ~N(μ,σ) indicates that values were drawn from a normal distribution with mean and standard deviation parameters given by μ and σ, respectively.
The choice of parameters is consistent with empirical data. For example, one empirical assessment of 743 randomized trials on cancer, neurological and other diseases estimated an average treatment effect of the new treatment versus the old or placebo corresponding to a hazard ratio of 0.9 (i.e., a small effect) [13] and it is assumed that about half of the treatments that reach that stage of testing for these diseases may have some efficacy [14]. Among the 18 oncology drugs licensed by FDA between 2000 and 2011, the median hazard ratio was about 0.7, i.e. a moderate effect [15]. However, early trials may have inflated effect sizes. Largescale evaluation of about a quarter of a million trials suggests that large effects may be seen in some small trials, but typically do not hold up upon further evaluation; thus most treatment effects of effective interventions are likely to be small or modest [16]. In the case of antidepressants like citalopram, the estimated standardized treatment effect in large metaanalysis is about 0.3 [17].
For each distribution of effect size simulation set, we ran four different kinds of number of participants per group in each trial: n = 20, n = 50, n = 100, and n = 400. These numbers are typical of what is seen in much of the biomedical literature. For example, the mean sample size (both arms combined) of the 743 randomized trials discussed above was 400 participants (200 per arm) [13] with substantial variability across different interventions and the average randomized trial published in 2000–2006 had a median sample size of 80 (both arms combined) [18]. For antidepressants, randomized trials with between 20 and 50 participants per arm are not uncommon, and in some cases arms with fewer than 20 participants are analyzed by FDA [7].
Thus, to sum up, our simulations varied along the following dimensions:
 1.
Prevalence of true null effect size: 25, 50, 75, and 0%
 2.
Number of participants per group: 20, 50, 100, and 400
This resulted in a total of 16 types of simulations. We replicated each simulation type 2000 times. Every individual simulation contained data from 2, 3, or 5 clinical trials, each containing a control (placebo or reference standard of care treatment) group and an experimental group.
We replicated this set of simulations with one important modification: we replaced the fixed effects model with a random effects model. Specifically, the fixed effects model prescribes e ~ N(δ, 1) with δ~ N (0.4, 0.13). The random effects model prescribes e ~ N (δ_{i}, 1) with δ_{i} ~ N(δ, 0.1) and δ ~ N (0.4, 0.13), where δ indicates the population effect size for a given iteration and δ_{i} indicates the population effect size for a given trial i and an iteration. Results of these sensitivity analyses are qualitatively similar and may be found in the Additional file 1, available at https://osf.io/9yvd2/.
For each replication, we performed three types of analyses. Firstly, we conducted onesided independentsamples ttests for each of the trials. This resulted in a single pvalue for each trial. Secondly, we calculated three kinds of metaanalytic 95% confidence intervals (CI) for the underlying effect size: a fixed effect method using inverse variance weighting, the DerSimonian and Laird (DSL) random effect method and the more conservative Hartung, Knapp, Sidik, and Jonkman (HKSJ) random effect method (see e.g., Appendix 1 in [19] for statistical details).
Thirdly, we conducted a onesided independentsamples Bayesian ttest for the data of all trials combined. The vehicle of choice for quantifying the evidence was the onesided Jeffreys ZellnerSiow (JZS) Bayes factor [20]. This onesided Bayes factor quantifies the relative likelihood of the onesided alternative hypothesis, the experimental group has a higher mean than the control group, against the null hypothesis, the experimental group has the same mean as the control group. The JZS Bayes factor is calculated by comparing the marginal likelihood of the data under the point null hypothesis to the marginal likelihood of the data under the alternative hypothesis, integrated over a range of plausible alternative hypotheses. The range of alternative hypotheses is given by a prior on the effect size parameter δ, which follows a Cauchy distribution centered on zero with a scale parameter of r = √2/2 (see [20], Equation in note 4). The Cauchy prior is typically referred to as an objective prior, because it satisfies a number of general desiderata [21, 22]. These include model selection consistency (data generated under a model should lead to a Bayes factor for this model converging to infinite as sample size increases) and predictive matching (there exists a minimum sample size for which one should not be able to distinguish between models, leading to a Bayes factor of 1). Contrary to a Normal prior, the Cauchy prior in addition satisfies the criterion of information consistency (different sequences of data with the same sample size for which likelihood ratios go to infinity should have corresponding Bayes factors that also go to infinity). We omit further details here for brevity but point the interested reader to [21].
Bayes factors were calculated using the BayesFactor R package [23]. For comparison, we calculated minimum Bayes factors [6, 24] using the pCalibrate package, also available in R [25]. Minimum Bayes factors quantify the upper bound of evidence against the null hypothesis for a number of priors under the alternative. As a result, it is more liberal than the JZS Bayes factor, leading to higher true and false positive rates. The reader interested in a comparison of the two Bayes factors is referred to the Additional file 1.
Once pvalues, metaanalytic 95% CIs, and Bayes factors were obtained, different evidential thresholds and thresholds for clinical meaningfulness were combined to obtain true positive and false positive rates. For the null hypothesis significance test, the main manuscript reports a significance level α of 0.025, which corresponds to a twosided test with significance level 0.05, followed by a check for the direction of the effect. Alternative significance levels α of 0.05 and 0.005 are reported in the Additional file 1. For the metaanalytic 95% CIs, the lower bound was used. For the Bayesian tests, Bayes Factor thresholds of 3, 10, and 50 were used. In order to decide whether a positive result counts as a true or false positive, a threshold needs to be established for an effect being clinically meaningful. We varied the clinically meaningful threshold from 0 (corresponding to a scenario where each nonzero effect is meaningful, no matter how small), 0.15, 0.3, and 0.45 (where only effect sizes higher than the respective numbers are clinically meaningful). There is a large literature on the clinically minimum important difference (CMID) in the biomedical literature and we used this as rough guidance for selecting these values. A simple approach is that a standardized effect of at least 0.5 is needed [26]. However, we erred on the side of being more lenient, since small effects may still be clinically meaningful, depending on the type of outcome, the setting, and the baseline risk involved [27, 28].
The quantification of true positives and false positives proceeds as follows. Taking as an example an α of 0.05 and a clinically meaningful threshold of 0.15, four scenarios are possible:
True positive: The true effect size is higher than 0.15, and at least two trials produced a pvalue lower than 0.05
False negative: The true effect size is higher than 0.15, and fewer than two trials produced a pvalue lower than 0.05
False positive: The true effect size is lower than 0.15, and at least two trials produced a pvalue lower than 0.05
True negative: The true effect size is lower than 0.15, and fewer than two trials produced a pvalue lower than 0.05
The false negative rate is equal to 1 minus the true positive rate and the true negative rate is equal to 1 minus the false positive rate. For the metaanalytic 95% CI, taking as an example a clinically meaningful threshold of 0.15, four scenarios are possible:
True positive: The true effect size is higher than 0.15, and the lower bound of the metaanalytic 95% CI is higher than zero
False negative: The true effect size is higher than 0.15, and the lower bound of the metaanalytic 95% CI is lower than zero
False positive: The true effect size is lower than 0.15, and the lower bound of the metaanalytic 95% CI is higher than zero
True negative: The true effect size is lower than 0.15, and the lower bound of the metaanalytic 95% CI is lower than zero
For the Bayesian tests, taking as an example a Bayes Factor threshold of 10 and a clinically meaningful threshold of 0.15, four scenarios are possible:
True positive: The true effect size is higher than 0.15, and the Bayes Factor is higher than 10
False negative: The true effect size is higher than 0.15, and the Bayes Factor is lower than 10
False positive: The true effect size is lower than 0.15, and the Bayes Factor is higher than 10
True negative: The true effect size is lower than 0.15, and the Bayes Factor is lower than 10
The code for these simulations is freely available on https://osf.io/9yvd2/.
Results
For the simulation scenario of five clinical trials, true positives are plotted against false positives for different evidence criteria and for different thresholds for a clinically meaningful effect when the prevalence of the true null effect is 25% in Fig. 1. In all panels, the yaxis represents the proportion of true positives and the xaxis represents the proportion of false positives. Different panels indicate different numbers of participants per trial, and different colors represent different thresholds of a clinical meaningful effect. The ideal scenario of detecting 100% true positives and 0% false positives is represented by the topleft of each panel. Note that for the conventional statistical significance results and a clinically meaningful threshold of 0, false positive rates can be analytically calculated with 1((1α)^5 + (1α)^4*α*5). The expression for the false positive rates is less straightforward when the effect size of 0 tested in null hypothesis significance testing differs from the clinically meaningful effect value used to categorize the underlying population effect as true or false. To keep results consistent, we display simulation results for all levels of clinical meaningful effects.
The results show to what extent working with more stringent criteria for statistical evidence reduces the proportion of false positives at the expense of reducing the proportion of true positives. This is as it should be, more conservative decision criteria trade off a reduction in the endorsement of ineffective medication against a lower endorsement of effective medication.
When looking at the performance of the metaanalytic 95% CI, we see that across the board the metaanalytic methods are associated with a higher true positive and a higher false positive rate. Regardless of sample size and clinical significance threshold, the HKSJ method is more conservative than the DSL method, which is in turn more conservative than the fixed effects method.
Next, we compare the results of the conventional statistical significance results to Bayesian testing results. Across the board, the panels show that Bayesian criteria for decision making are slightly more to the top and more to the left of conventional decision criteria in particular when small sample sizes are involved. For instance, for n = 20, compared to two trials with p < 0.025, a decision rule based on an overall Bayes factor higher than 50 results in a slightly higher proportion of true positives and a slightly lower proportion of false positives. Using more stringent or more relaxed criteria for statistical evidence shifts the balance between proportions true and false positives, but does not change the fact that for every twosignificanttrial criterion, there is a corresponding BF > x criterion with more true positives and fewer false positives combined (see Additional file 1 for details). The BF criteria seem better than both the conventional criteria and the metaanalytic methods in particular with large meaningful clinical difference thresholds. The difference between the two inferential methods becomes smaller with larger trials and is not discernible with 400 participants per arm.
To what extent do the results differ when we assume a higher prevalence of true null effects? The answer for a nulleffect prevalence of 50% can be found in Fig. 2. The layout is similar to that of Fig. 1.
Comparing the results for a 50% prevalence of true null effects to those for a 25% prevalence of true null effects, one clear observation is that the proportion of false positives dwindles across the board. The majority of false positives are caused by effects that come from the nonnull normal distribution, but do not pass the clinically meaningful threshold. This means that the more true negatives there are, the lower the proportion of false positives is. The proportion of true positives is unaffected, which is again as it should be, given that nothing changed across these simulations within the distribution of nonnull effects.
Importantly, we again find the pattern that Bayesian criteria are typically associated with a combination of higher true positive rates and lower false positive rates than conventional statistical significancebased decision criteria, especially with small sample sizes (n = 20 per arm) and somehow more prominently with larger clinically meaningful differences. We also replicate the result that the Bayesian methods perform slightly better than both the pvalue criterion and the metaanalytic CIs when employed for decision making purposes.
Results for a nulleffect prevalence of 75% can be found in Fig. 3. The layout is similar to that of Fig. 2.
Consistent with the comparison of previous results, we see the reduction in false positives across the board. The better performance of the Bayesian evaluation criterion, both in terms of true positives and in terms of false positives is seen again with small sample sizes.
Lastly, results are plotted for an ideal scenario in which there exist only nonnull effects, or a prevalence of true null effects of 0% (all tested medications are truly effective). Results can be found in Fig. 4.
The scenario of no null effects displays the previous pattern of results in its most extreme: identical true positive rates, relatively bad false positive rates when the clinically meaningful threshold is anything higher than zero, and better performance of the Bayesian evaluation criterion.
Results for the simulation scenarios of three clinical trials were qualitatively similar to those for five clinical trials reported here. For two clinical trials, the significance method (i.e., both trials were significant) performed very similar to the Bayesian method. Detailed results can be found in the Additional file 1.
In order to get a better handle on the performance of the different types of metaanalysis, we examined for different sample sizes how often the metaanalytic confidence intervals included the true population effect size. The results are plotted in Table 1.
Inspection of the table shows that the coverage of the HKSJ method (the probability that the true effect is included in the 95% confidence interval) was better than the coverage of the DSL method which was in turn better than the coverage of the fixed effects method. HKSJ is wellknown to be a better method in most circumstances and this is also consistent with what we observed.
Discussion
In this study, we simulated clinical trial data comparing an experimental group to a control group (placebo or other standard of care). Simulations differed in the number of clinical trials conducted, the proportion of true null effects versus nonnull effects, and the number of participants in each trial. For all simulations, we compared the true and false positive rates when strength of evidence was quantified by counting the number of significant results, quantified by pvalues lower than a certain significance level α, by constructing metaanalytic 95% confidence intervals and assessing their overlap with a clinically meaningful effect, or by Bayes factor assessing the overall strength of evidence provided by the five trials. True and false positive rates were defined using four different thresholds of an effect being considered clinically meaningful.
The takehome message when surveying the results of all simulations together is that quantifying evidence with Bayes factors compared to counting the number of statistically significant results or metaanalytic confidence intervals leads to a higher true positive rate for a given false positive rate, or a lower false positive rate for a given true positive rate, especially when relatively small trials are involved. We find this result irrespective of the significance level or Bayes factor threshold chosen. Our results get more pronounced as the incidence rate of true null effects gets lower. The latter should be particularly relevant in the assessment of stage III clinical trials, where the prevalence of truly null effects is arguably lower than for stage I and II trials.
Metaanalysis is a powerful tool for estimating the size of an unknown population effect size across the results of several independent studies. In our simulations, we confirmed that the metaanalytic confidence intervals often captured the true population effect size, and HKSJ performed better than DSL random effects which in turn performed better than fixed effects. For purposes of making a dichotomous yes/no decision however, Bayesian methods appeared to be the (slightly) superior choice in scenarios where sample size was low. Apparently, the strength of metaanalytic methods is in making assessments about the continuum of the effect size and its uncertainty, rather than binary decisions.
Bayesian methods for statistical inference have been recommended for use in the analysis of clinical trials before [29, 30], and have been discussed in the context of the regulatory process ([31], see also the rest of this special issue), but they are still much less commonly used than pvalues from null hypothesis significance testing. In fact, across the biomedical literature, null hypothesis significance testing seems to be about 100fold more commonly used than Bayesian inference [32]. While previously underuse of Bayesian methods may have been excused by the unavailability of means to carry out these analyses, recently a number of free and userfriendly types of software have been developed [23, 33, 34], such that technical limitations should no longer be a concern.
Some caveats need to be discussed. It is important to stress that the approval process does not hinge exclusively on an evaluation of the available statistical evidence in a strictly quantitative manner, nor do we wish for quantitative automation to replace nuanced reasoning. Rather, qualitative aspects of the appropriateness of the design, conduct and analysis of the trial should continue to be evaluated as well as the relevance of the outcomes used, potential safety implications, and sideeffects and harms that could affect the benefitrisk ratio. Each of these considerations will factor into the endorsement process and can lead to a different desired tradeoff for maximizing true positives versus minimizing false positives. Our simulations should provide some guidance on how this tradeoff should be influenced by the anticipated distribution of effects in the relevant drug group or subfield. Our results and subsequent recommendations should be taken to apply to the statistical component of the evaluation process, and should be combined with other utilities to come to the appropriate analysis strategy.
We should also caution that the absolute magnitude of difference in performance between the Bayesian and pvaluebased criteria was often small or negligible in several of the simulations. Moreover, it is typically difficult to know what the likely values are for the frequency of null effects in specific fields and applications. The advantage of the Bayesian criteria seemed clearer when sample sizes were small and clinically meaningful differences were not small. With large sample sizes and small clinically meaningful differences, the three inferential approaches seemed to have very similar performance.
Finally, we used popular but arbitrary cutoffs for both statistical significance and Bayes factors and in fact both of these take continuous values. Such dichotomization may cause loss of information for both types of criteria.
The modest superiority of the Bayesian approach may be due to the fact that it considers all evidence in a cumulative manner, while the rule of having two statistically significant results adds a further dichotomization in counting “positive” and “negative” trials, with further loss of information.
Conclusion
Allowing for these caveats, evaluating the results of multiple clinical trials with Bayes factors is a useful approach that, in some circumstances may lead to a higher true positive rate for the same false positive rate, compared to an analysis strategy based on simply counting the number of significant results. Decisions on the appropriate Bayes factor threshold should be based on additional utilities that are not part of the statistical process and may also be informed by the anticipated prevalence of true null effects.
Availability of data and materials
Code for reproducing the analyses reported in the manuscript may be obtained from https://osf.io/9yvd2/.
Abbreviations
 CI:

Confidence intervals
 CMID:

Clinically minimum important difference
 DSL:

DerSimonian and Laird random effect method
 FDA:

US Food and Drug Administration
 HKSJ:

Hartung, Knapp, Sidik, and Jonkman random effect method
 JZS:

Jeffreys ZellnerSiow
 RCT:

Registered clinical trial
References
 1.
Katz R. FDA: evidentiary standards for drug development and approval. NeuroRx. 2004;1:307–16.
 2.
Goodman SN. P values, hypothesis tests, and likelihood: implications for epidemiology of a neglected historical debate. Am J Epidemiol. 1993;137:485–96.
 3.
Goodman SN. Toward evidencebased medical statistics. 1: the P value fallacy. Ann Intern Med. 1999;130:995–1004.
 4.
Food and Drug Administration. Guidance for industry: providing clinical evidence of effectiveness for human drug and biological products. Maryland: United States Food and Drug Administration; 1998.
 5.
van Ravenzwaaij D, Ioannidis JP. A simulation study of the strength of evidence in the recommendation of medications based on two trials with statistically significant results. PLoS One. 2017;12:e0173184.
 6.
Goodman SN. Toward evidencebased medical statistics. 2: the Bayes factor. Ann Intern Med. 1999;130:1005–13.
 7.
Turner EH, Matthews AM, Linardatos E, Tell RA, Rosenthal R. Selective publication of antidepressant trials and its influence on apparent efficacy. N Engl J Med. 2008;358:252–60.
 8.
Monden R, Roest AM, van Ravenzwaaij D, Wagenmakers EJ, Morey R, Wardenaar KJ, de Jonge P. The comparative evidence basis for the efficacy of secondgeneration antidepressants in the treatment of depression in the US: a Bayesian metaanalysis of Food and Drug Administration reviews. J Affect Disord. 2018;235:393–8.
 9.
Ioannidis JPA. Why most published research findings are false. PLoS Med. 2005;2:e124.
 10.
Benjamin DJ, Berger JO, Johannesson M, Nosek BA, Wagenmakers EJ, Berk R, Bollen KA, Brembs B, Brown L, Camerer C, Cesarini D, et al. Redefine statistical significance. Nat Hum Behav. 2018;2:6.
 11.
Jeffreys H. Theory of probability. 1st ed. Oxford: Oxford University Press; 1961.
 12.
Kass RE, Raftery AE. Bayes factors. J Am Stat Assoc. 1995;90:773–95.
 13.
Djulbegovic B, Kumar A, Glasziou PP, Perera R, Reljic T, Dent L, Raftery J, Johansen M, Di Tanna GL, Miladinovic B, Soares HP. New treatments compared to established treatments in randomized trials. Cochrane Database Syst Rev. 2012;10:MR000024.
 14.
Djulbegovic B, Lacevic M, Cantor A, Fields KK, Bennett CL, Adams JR, Kuderer NM, Lyman GH. The uncertainty principle and industrysponsored research. Lancet. 2000;356:635–8.
 15.
Ocana A, Tannock IF. When are “positive” clinical trials in oncology truly positive? J Natl Cancer Inst. 2010;103:16–20.
 16.
Pereira TV, Horwitz RI, Ioannidis JPA. Empirical evaluation of very large treatment effects of medical interventions. JAMA. 2012;308:1676–84.
 17.
Cipriani A, Furukawa TA, Salanti G, Chaimani A, Atkinson LZ, Ogawa Y, Leucht S, Ruhe HG, Turner EH, Higgins JP, Egger M. Comparative efficacy and acceptability of 21 antidepressant drugs for the acute treatment of adults with major depressive disorder: a systematic review and network metaanalysis. Lancet. 2018;391:1357–66.
 18.
Hopewell S, Dutton S, Yu LM, Chan AW, Altman DG. The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed. BMJ. 2010;340:c723.
 19.
In’t Hout J, JPA I, Borm GF. The HartungKnappSidikJonkman method for random effects metaanalysis is straightforward and considerably outperforms the standard DerSimonianLaird method. BMC Med Res Methodol. 2014;14:25.
 20.
Rouder JN, Speckman PL, Sun D, Morey RD, Iverson G. Bayesian t tests for accepting and rejecting the null hypothesis. Psychon Bull Rev. 2009;16:225–37.
 21.
Bayarri MJ, Berger JO, Forte A, GarcíaDonato G. Criteria for Bayesian model choice with application to variable selection. Ann Stat. 2012;40:1550–77.
 22.
Consonni G, Fouskakis D, Liseo B, Ntzoufras I. Prior distributions for objective Bayesian analysis. Bayesian Anal. 2018;13:627–79.
 23.
Morey RD, Rouder JN, Jamil T, Urbanek S, Forner K, Ly A. BayesFactor: Computation of Bayes factors for common designs. R package version 0.9.12–4.2; 2018.
 24.
Held L, Ott M. On pvalues and Bayes factors. Ann Rev Stat Appl. 2018;5:393–419.
 25.
Ott M, Held L. pCalibrate: Bayesian Calibrations of pvalues. R package version 0.1–1; 2017.
 26.
Norman GR, Sloan JA, Wyrwich KW. Interpretation of changes in healthrelated quality of life: the remarkable universality of half a standard deviation. Med Care. 2003;41:582–92.
 27.
Copay AG, Subach BR, Glassman SD, Polly DW Jr, Schuler TC. Understanding the minimum clinically important difference: a review of concepts and methods. Spine J. 2007;7:541–6.
 28.
Hays RD, Woolley JM. The concept of clinically meaningful difference in healthrelated qualityoflife research. Pharmacoeconomics. 2000;18:419–23.
 29.
Hobbs BP, Carlin BP. Practical Bayesian design and analysis for drug and device clinical trials. J Biopharm Stat. 2008;18:54–80.
 30.
Zaslavsky BG. Bayesian hypothesis testing in twoarm trials with dichotomous outcomes. Biometrics. 2013;69:157–63.
 31.
Woodcock J, Temple R, Midthun K, Schultz D, Sundlof S. FDA senior management perspectives. Clin Trials. 2005;2:373–8.
 32.
Chavalarias D, Wallach JD, Li AHT, Ioannidis JPA. Evolution of reporting p values in the biomedical literature, 19902015. J Am Med Assoc. 2016;315:1141–8.
 33.
JASP [computer program]. Version 0.7.5.6. The JASP Team; 2016. https://jaspstats.org/.
 34.
van Ravenzwaaij D, Monden R, Tendeiro JN, Ioannidis JP. Bayes factors for superiority, noninferiority, and equivalence designs. BMC Med Res Methodol. 2019;19:71.
Acknowledgements
Not applicable.
Funding
This research was supported by a Dutch scientific organization VIDI fellowship grant to DvR, which supported the writing of the manuscript (016.Vidi.188.001).
Author information
Affiliations
Contributions
DvR drafted the original manuscript and conducted the formal analyses. DvR and JI conceptualized the project. JI was a major contributor in writing the manuscript. All authors read and approved the final manuscript.
Corresponding author
Ethics declarations
Ethics approval and consent to participate
Not applicable.
Consent for publication
Not applicable.
Competing interests
The authors declare that they have no competing interests.
Additional information
Publisher’s Note
Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.
Supplementary information
Additional file 1.
True and false positive rates for different criteria of evaluating statistical evidence from clinical trials.
Rights and permissions
Open Access This article is distributed under the terms of the Creative Commons Attribution 4.0 International License (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons license, and indicate if changes were made. The Creative Commons Public Domain Dedication waiver (http://creativecommons.org/publicdomain/zero/1.0/) applies to the data made available in this article, unless otherwise stated.
About this article
Cite this article
van Ravenzwaaij, D., Ioannidis, J.P.A. True and false positive rates for different criteria of evaluating statistical evidence from clinical trials. BMC Med Res Methodol 19, 218 (2019). https://doi.org/10.1186/s128740190865y
Received:
Accepted:
Published:
Keywords
 US Food and Drug Administration
 pvalues
 Strength of Evidence
 Bayes Factors