Category Archives: False Positives

Replicability 101: How to interpret the results of replication studies

Even statistically sophisticated psychologists struggle with the interpretation of replication studies (Maxwell et al., 2015).  This article gives a basic introduction to the interpretation of statistical results within the Neyman Pearson approach to statistical inferences.

I make two important points and correct some potential misunderstandings in Maxwell et al.’s discussion of replication failures.  First, there is a difference between providing sufficient evidence for the null-hypothesis (evidence of absence) and providing insufficient evidence against the null-hypothesis (absence of evidence).  Replication studies are useful even if they simply produce absence of evidence without evidence that an effect is absent.  Second, I  point out that publication bias undermines the credibility of significant results in original studies.  When publication bias is present, open replication studies are valuable because they provide an unbiased test of the null-hypothesis, while original studies are rigged to reject the null-hypothesis.

DEFINITION OF REPLICATING A STATISTICAL RESULT

Replicating something means to get the same result.  If I make the first free throw, replicating this outcome means to also make the second free throw.  When we talk about replication studies in psychology we borrow from the common meaning of the term “to replicate.”

If we conduct psychological studies, we can control many factors, but some factors are not under our control.  Participants in two independent studies differ from each other and the variation in the dependent variable across samples introduces sampling error. Hence, it is practically impossible to get identical results, even if the two studies are exact copies of each other.  It is therefore more complicated to compare the results of two studies than to compare the outcome of two free throws.

To determine whether the results of two studies are identical or not, we need to focus on the outcome of a study.  The most common outcome in psychological studies is a significant or non-significant result.  The goal of a study is to produce a significant result and for this reason a significant result is often called a success.  A successful replication study is a study that also produces a significant result.  Obtaining two significant results is akin to making two free throws.  This is one of the few agreements between Maxwell and me.

“Generally speaking, a published  original study has in all likelihood demonstrated a statistically significant effect. In the current zeitgeist, a replication study is usually interpreted as successful if it also demonstrates a statistically significant effect.” (p. 488)

The more interesting and controversial scenario is a replication failure. That is, the original study produced a significant result (success) and the replication study produced a non-significant result (failure).

I propose that a lot of confusion arises from the distinction between original and replication studies. If a replication study is an exact copy of the first study, the outcome probabilities of original and replication studies are identical.  Otherwise, the replication study is not really a replication study.

There are only three possible outcomes in a set of two studies: (a) both studies are successful, (b) one study is a success and one is a failure, or (c) both studies are failures.  The probability of these outcomes depends on whether the significance criterion (the type-I error probability) when the null-hypothesis is true and the statistical power of a study when the null-hypothesis is false.

Table 1 shows the probability of the outcomes in two studies.  The uncontroversial scenario of two significant results is very unlikely, if the null-hypothesis is true. With conventional alpha = .05, the probability is .0025 or 1 out of 400 attempts.  This shows the value of replication studies. False positives are unlikely to repeat themselves and a series of replication studies with significant results is unlikely to occur by chance alone.

2 sig, 0 ns 1 sig, 1 ns 0 sig, 2 ns
H0 is True alpha^2 2*alpha*(1-alpha) (1-alpha^2)
H1 is True (1-beta)^2 2*(1-beta)*beta beta^2

The probability of a successful replication of a true effect is a function of statistical power (1 – type-II error probability).  High power is needed to get significant results in a pair of studies (an original study and a replication study).  For example, if power is only 50%, the chance of this outcome is only 25% (Schimmack, 2012).  Even with conventionally acceptable power of 80%, only 2/3 (64%) of replication attempts would produce this outcome.  However, studies in psychology do not have 80% power and estimates of power can be as low as 37% (OSC, 2015). With 40% power, a pair of studies would produce significant results in no more than 16 out of 100 attempts.   Although successful replications of true effects with low power are unlikely, they are still much more likely then significant results when the null-hypothesis is true (16/100 vs. 1/400 = 64:1).  It is therefore reasonable to infer from two significant results that the null-hypothesis is false.

If the null-hypothesis is true, it is extremely likely that both studies produce a non-significant result (.95^2 = 90.25%).  In contrast, it is unlikely that even a study with modest power would produce two non-significant results.  For example, if power is 50%, there is a 75% chance that at least one of the two studies produces a significant result. If power is 80%, the probability of obtaining two non-significant results is only 4%.  This means, it is much more likely (22.5 : 1) that the null-hypothesis is true than that the alternative hypothesis is true.  This does not mean that the null-hypothesis is true in an absolute sense because power depends on the effect size.  For example, if 80% power were obtained with a standardized effect size of Cohen’s d = .5,  two non-significant results would suggest that the effect size is smaller than .5, but it does not warrant the conclusion that H0 is true and the effect size is exactly 0.  Once more, it is important to distinguish between the absence of evidence for an effect and the evidence of absence of an effect.

The most controversial scenario assumes that the two studies produced inconsistent outcomes.  Although theoretically there is no difference between the first and the second study, it is common to focus on a successful outcome followed by a replication failure  (Maxwell et al., 2015). When the null-hypothesis is true, the probability of this outcome is low;  .05 * (1-.05) = .0425.  The same probability exists for the reverse pattern that a non-significant result is followed by a significant one.  A probability of 4.25% shows that it is unlikely to observe a significant result followed by a non-significant result when the null-hypothesis is true. However, the low probability is mostly due to the low probability of obtaining a significant result in the first study, while the replication failure is extremely likely.

Although inconsistent results are unlikely when the null-hypothesis is true, they can also be unlikely when the null-hypothesis is false.  The probability of this outcome depends on statistical power.  A pair of studies with very high power (95%) is very unlikely to produce an inconsistent outcome because both studies are expected to produce a significant result.  The probability of this rare event can be as low, or lower, than the probability with a true null effect; .95 * (1-.95) = .0425.  Thus, an inconsistent result provides little information about the probability of a type-I or type-II  error and is difficult to interpret.

In conclusion, a pair of significance tests can produce three outcomes. All three outcomes can occur when the null-hypothesis is true and when it is false.  Inconsistent outcomes are likely unless the null-hypothesis is true or the null-hypothesis is false and power is very high.  When two studies produce inconsistent results, statistical significance provides no basis for statistical inferences.

Meta-Analysis 

The counting of successes and failures is an old way to integrate information from multiple studies.  This approach has low power and is no longer used.  A more powerful approach is effect size meta-analysis.  Effect size meta-analysis was one way to interpret replication results in the Open Science Collaboration (2015) reproducibility project.  Surprisingly, Maxwell et al. (2015) do not consider this approach to the interpretation of failed replication studies. To be clear, Maxwell et al. (2015) mention meta-analysis, but they are talking about meta-analyzing a larger set of replication studies, rather than meta-analyzing the results of an original and a replication study.

“This raises a question about how to analyze the data obtained from multiple studies. The natural answer is to use meta-analysis.” (p. 495)

I am going to show that effect-size meta-analysis solves the problem of interpreting inconsistent results in pairs of studies. Importantly, effect size meta-analysis does not care about significance in individual studies.  A meta-analysis of a pair of studies with inconsistent results is no different from a meta-analysis of a pair of studies with consistent results.

Maxwell et al.’s (2015) introduced an example of a between-subject (BS) design with n = 40 per group (total N = 80) and a standardized effect size of Cohen’s d = .5 (a medium effect size).  This study has 59% power to obtain a significant result.  Thus, it is quite likely that a pair of studies produces inconsistent results (48.38%).   However, a pair of studies with N = 80 has the power of a total sample size of N = 160, which means a fixed-effects meta-analysis will produce a significant result in 88% of all attempts.  Thus, it is not difficult at all to interpret the results of pairs of studies with inconsistent results if the studies have acceptable power (> 50%).   Even if the results are inconsistent, a meta-analysis will provide the correct answer that there is an effect most of the time.

A more interesting scenario are inconsistent results when the null-hypothesis is true.  I turned to simulations to examine this scenario more closely.   The simulation showed that a meta-analysis of inconsistent studies produced a significant result in 34% of all cases.  The percentage slightly varies as a function of sample size.  With a small sample of N = 40, the percentage is 35%. With a large sample of  1,000 participants it is 33%.  This finding shows that in two-thirds of attempts, a failed replication reverses the inference about the null-hypothesis based on a significant original study.  Thus, if an original study produced a false-positive results, a failed replication study corrects this error in 2 out of 3 cases.  Importantly, this finding does not warrant the conclusion that the null-hypothesis is true. It merely reverses the result of the original study that falsely rejected the null-hypothesis.

In conclusion, meta-analysis of effect sizes is a powerful tool to interpret the results of replication studies, especially failed replication studies.  If the null-hypothesis is true, failed replication studies can reduce false positives by 66%.

DIFFERENCES IN SAMPLE SIZES

We can all agree that, everything else being equal, larger samples are better than smaller samples (Cohen, 1990).  This rule applies equally to original and replication studies. Sometimes it is recommended that replication studies should use much larger samples than original studies, but it is not clear to me why researchers who conduct replication studies should have to invest more resources than original researchers.  If original researchers conducted studies with adequate power,  an exact replication study with the same sample size would also have adequate power.  If the original study was a type-I error, the replication study is unlikely to replicate the result no matter what the sample size.  As demonstrated above, even a replication study with the same sample size as the original study can be effective in reversing false rejections of the null-hypothesis.

From a meta-analytic perspective, it does not matter whether a replication study had a larger or smaller sample size.  Studies with larger sample sizes are given more weight than studies with smaller samples.  Thus, researchers who invest more resources are rewarded by giving their studies more weight.  Large original studies require large replication studies to reverse false inferences, whereas small original studies require only small replication studies to do the same.  Nevertheless, failed replications with larger samples are more likely to reverse false rejections of the null-hypothesis, but there is no magical number about the size of a replication study to be useful.

I simulated a scenario with a sample size of N = 80 in the original study and a sample size of N = 200 in the replication study (a factor of 2.5).  In this simulation, only 21% of meta-analyses produced a significant result.  This is 13 percentage points lower than in the simulation with equal sample sizes (34%).  If the sample size of the replication study is 10 times larger (N = 80 and N = 800), the percentage of remaining false positive results in the meta-analysis shrinks to 10%.

The main conclusion is that even replication studies with the same sample size as the original study have value and can help to reverse false positive findings.  Larger sample sizes simply give replication studies more weight than original studies, but it is by no means necessary to increase sample sizes of replication studies to make replication failures meaningful.  Given unlimited resources, larger replications are better, but these analysis show that large replication studies are not necessary.  A replication study with the same sample size as the original study is more valuable than no replication study at all.

CONFUSING ABSENCE OF EVIDENCE WITH EVIDENCE OF ABSENCE

One problem in Maxwell et al’s (2015) article is to conflate two possible goals of replication studies.  One goal is to probe the robustness of the evidence against the null-hypothesis. If the original result was a false positive result, an unsuccessful replication study can reverse the initial inference and produce a non-significant result in a meta-analysis.  This finding would mean that evidence for an effect is absent.  The status of a hypothesis (e.g., humans have supernatural abilities; Bem, 2011) is back to where it was before the original study found a significant result and the burden of proof is shifted back to proponents of the hypothesis to provide unbiased credible evidence for it.

Another goal of replication studies can be to provide conclusive evidence that an original study reported a false positive result (i..e, humans do not have supernatural abilities).  Throughout their article, Maxwell et al. assume that the goal of replication studies is to prove the absence of an effect.  They make many correct observations about the difficulties of achieving this goal, but it is not clear why replication studies have to be conclusive when original studies are not held to the same standard.

This makes it easy to produce (potentially false) positive results and very hard to remove false positive results from the literature.   It also creates a perverse incentive to conduct underpowered original studies and to claim victory when a large replication study finds a significant result with an effect size that is 90% smaller than the effect size in an original study.  The authors of the original article may claim that they do not care about effect sizes and that their theoretical claim was supported.  To avoid this problem that replication researchers have to invest large amount of resources for little gain, it is important to realize that even a failure to replicate an original finding with the same sample size can undermine original claims and force researchers to provide stronger evidence for their original ideas in original articles.  If they are right and the evidence is strong, others will be able to replicate the result in an exact replication study with the same sample size.

THE DIRTY BIG SECRET

The main problem of Maxwell et al.’s (2015) article is that the authors blissfully ignore the problem of publication bias.  They mention publication bias twice to warn readers that publication bias inflates effect sizes and biases power analyses, but they completely ignore the influence of publication bias on the credibility of successful original results (Schimmack, 2012; Sterling; 1959; Sterling et al., 1995).

It is hard to believe that Maxwell is unaware of this problem, if only because Maxwell was action editor of my article that demonstrated how publication bias undermines the credibility of replication studies that are selected for significance  (Schimmack, 2012).

I used Bem’s infamous article on supernatural abilities as an example, which appeared to show 8 successful replications of supernatural abilities.  Ironically, Maxwell et al. (2015) also cites Bem’s article to argue that failed replication studies can be misinterpreted as evidence of absence of an effect.

“Similarly, Ritchie, Wiseman, and French (2012) state that their failure to obtain significant results in attempting to replicate Bem (2011) “leads us to favor the ‘experimental artifacts’ explanation for Bem’s original result” (p. 4)”

This quote is not only an insult to Ritchie et al.; it also ignores the concerns that have been raised about Bem’s research practices. First, Ritchie et al. do not claim that they have provided conclusive evidence against ESP.  They merely express their own opinion that they “favor the ‘experimental artifacts’ explanation.  There is nothing wrong with this statement, even if it is grounded in a healthy skepticism about supernatural abilities.

More important, Maxwell et al. ignore the broader context of these studies.  Schimmack (2012) discussed many questionable practices in Bem’s original studies and I presented statistical evidence that the significant results in Bem’s article were obtained with the help of questionable research practices.  Given this wider context, it is entirely reasonable to favor the experimental artifact explanation over the alternative hypothesis that learning after an exam can still alter the exam outcome.

It is not clear why Maxwell et al. (2015) picked Bem’s article to discuss problems with failed replication studies and ignores that questionable research practices undermine the credibility of significant results in original research articles. One reason why failed replication studies are so credible is that insiders know how incredible some original findings are.

Maxwell et al. (2015) were not aware that in the same year, the OSC (2015) reproducibilty project would replicate only 37% of statistically significant results in top psychology journals, while the apparent success rate in these journals is over 90%.  The stark contrast between the apparent success rate and the true power to produce successful outcomes in original studies provided strong evidence that psychology is suffering from a replication crisis. This does not mean that all failed replications are false positives, but it does mean that it is not clear which findings are false positives and which findings are not.  Whether this makes things better is a matter of opinion.

Publication bias also undermines the usefulness of meta-analysis for hypothesis testing.  In the OSC reproducibility project, a meta-analysis of original and replication studies produced 68% significant results.  This result is meaningless because publication bias inflates effect sizes and the probability of obtaining a false positive result in the meta-analysis. Thus, when publication bias is present, unbiased replication studies provide the most credible evidence and the large number of replication failures means that more replication studies with larger samples are needed to see which hypothesis predict real effects with practical significance.

DOES PSYCHOLOGY HAVE A REPLICATION CRISIS?

Maxwell et al.’s (2015) answer to this question is captured in this sentence. “Despite raising doubts about the extent to which apparent failures to replicate necessarily reveal that psychology is in crisis,we do not intend to dismiss concerns about documented methodological flaws in the field.” (p. 496).  The most important part of this quote is “raising doubt,” the rest is Orwellian double-talk.

The whole point of Maxwell et al.’s article is to assure fellow psychologists that psychology is not in crisis and that failed replication studies should not be a major concern.  As I have pointed out, this conclusion is based on some misconceptions about the purpose of replication studies and by blissful ignorance about publication bias and questionable research practices that made it possible to publish successful replications of supernatural phenomena, while discrediting authors who spend time and resources on demonstrating that unbiased replication studies fail.

The real answer to Maxwell et al.’s question was provided by the OSC (2015) finding that only 37% of published significant results could be replicated.  In my opinion that is not only a crisis, but a scandal because psychologists routinely apply for funding with power analyses that claim 80% power.  The reproducibilty project shows that the true power to obtain significant results in original and replication studies is much lower than this and that the 90% success rate is no more meaningful than 90% votes for a candidate in communist elections.

In the end, Maxwell et al. draw the misleading conclusion that “the proper design and interpretation of replication studies is less straightforward than conventional practice would suggest.”  They suggest that “most importantly, the mere fact that a replication study yields a nonsignificant statistical result should not by itself lead to a conclusion that the corresponding original study was somehow deficient and should no longer be trusted.”

As I have demonstrated, this is exactly the conclusion that readers should draw from failed replication studies, especially if (a) the original study was not preregistered, (b) the original study produced weak evidence (e.g., p = .04), the original study was published in a journal that only publishes significant results, (d) the replication study had a larger sample, (e) the replication study would have been published independent of outcome, and (f) the replication study was preregistered.

We can only speculate why the American Psychologists published a flawed and misleading article that gives original studies the benefit of the doubt and casts doubt on the value of replication studies when they fail.  Fortunately, APA can no longer control what is published because scientists can avoid the censorship of peer-reviewed journals by publishing blogs and by criticize peer-reviewed articles in open post-publication peer review on social media.

Long life the replicability revolution.  !!!

REFERENCES

Cohen, J. (1990). Things I have learned (so far). American Psychologist, 45(12), 1304-1312.

http://dx.doi.org/10.1037/0003-066X.45.12.1304

Maxwell, S.E, Lau, M. Y., & Howard, G. S. (2015). Is psychology suffering from a replication crisis? What does ‘failure to replicate’ really mean? American Psychologist, 70, 487-498. http://dx.doi.org/10.1037/a0039400.

Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17(4), 551-566. http://dx.doi.org/10.1037/a0029487

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

 

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Are Most Published Results in Psychology False? An Empirical Study

Why Most Published Research Findings  are False by John P. A. Ioannidis

In 2005, John P. A. Ioannidis wrote an influential article with the title “Why Most Published Research Findings are False.” The article starts with the observation that “there is increasing concern that most current published research findings are false” (e124). Later on, however, the concern becomes a fact. “It can be proven that most claimed research findings are false” (e124). It is not surprising that an article that claims to have proof for such a stunning claim has received a lot of attention (2,199 citations and 399 citations in 2016 alone in Web of Science).

Most citing articles focus on the possibility that many or even more than half of all published results could be false. Few articles cite Ioannidis to make the factual statement that most published results are false, and there appears to be no critical examination of Ioannidis’s simulations that he used to support his claim.

This blog post shows that these simulations make questionable assumptions and shows with empirical data that Ioannidis’s simulations are inconsistent with actual data.

Critical Examination of Ioannidis’s Simulations

First, it is important to define what a false finding is. In many sciences, a finding is published when a statistical test produced a significant result (p < .05). For example, a drug trial may show a significant difference between a drug and a placebo control condition with a p-value of .02. This finding is then interpreted as evidence for the effectiveness of the drug.

How could this published finding be false? The logic of significance testing makes this clear. The only inference that is being made is that the population effect size (i.e., the effect size that could be obtained if the same experiment were repeated with an infinite number of participants) is different from zero and in the same direction as the one observed in the study. Thus, the claim that most significant results are false implies that in more than 50% of all published significant results the null-hypothesis was true. That is, a false positive result was reported.

Ioannidis then introduces the positive predictive value (PPV). The positive predictive value is the proportion of positive results (p < .05) that are true positives.

(1) PPV = TP/(TP + FP)

PTP = True Positive Results, FP = False Positive Results

The proportion of true positive results (TP) depends on the percentage of true hypothesis (PTH) and the probability of producing a significant result when a hypothesis is true. This probability is known as statistical power. Statistical power is typically defined as 1 minus the type-II error (beta).

(2) TP = PTH * Power = PTH * (1 – beta)

The probability of a false positive result depends on the proportion of false hypotheses (PFH) and the criterion for significance (alpha).

(3) FP = PFH * alpha

This means that the actual proportion of true significant results is a function of the ratio of true and false hypotheses (PTH:PFH), power, and alpha.

(4) PPV = (PTH*power) / ((PTH*power) + (PFH * alpha))

Ioannidis translates his claim that most published findings are false into a PPV below 50%. This would mean that the null-hypothesis is true in more than 50% of published results that falsely rejected it.

(5) (PTH*power) / ((PTH*power) + (PFH * alpha))  < .50

Equation (5) can be simplied to the inequality equation

(6) alpha > PTH/PFH * power

We can rearrange formula (6) and substitute PFH with (1-PHT) to determine the maximum proportion of true hypotheses to produce over 50% false positive results.

(7a)  =  alpha = PTH/(1-PTH) * power

(7b) = alpha*(1-PTH) = PTH * power

(7c) = alpha – PTH*alpha = PTH * power

(7d) =  alpha = PTH*alpha + PTH*power

(7e) = alpha = PTH(alpha + power)

(7f) =  alpha/(power + alpha) = PTH

 

Table 1 shows the results.

Power                  PTH / PFH             
90%                       5  / 95
80%                       6  / 94
70%                       7  / 93
60%                       8  / 92
50%                       9  / 91
40%                      11 / 89
30%                       14 / 86
20%                      20 / 80
10%                       33 / 67                     

Even if researchers would conduct studies with only 20% power to discover true positive results, we would only obtain more than 50% false positive results if only 20% of hypothesis were true. This makes it rather implausible that most published results could be false.

To justify his bold claim, Ioannidis introduces the notion of bias. Bias can be introduced due to various questionable research practices that help researchers to report significant results. The main effect of these practices is that the probability of a false positive result to become significant increases.

Simmons et al. (2011) showed that massive use several questionable research practices (p-hacking) can increase the risk of a false positive result from the nominal 5% to 60%. If we assume that bias is rampant and substitute the nominal alpha of 5% with an assumed alpha of 50%, fewer false hypotheses are needed to produce more false than true positives (Table 2).

Power                 PTH/PFH             
90%                     40 / 60
80%                     43 / 57
70%                     46 / 54
60%                     50 / 50
50%                     55 / 45
40%                     60 / 40
30%                     67 / 33
20%                     75 / 25
10%                      86 / 14                    

If we assume that bias inflates the risk of type-I errors from 5% to 60%, it is no longer implausible that most research findings are false. In fact, more than 50% of published results would be false if researchers tested hypothesis with 50% power and 50% of tested hypothesis are false.

However, the calculations in Table 2 ignore the fact that questionable research practices that inflate false positives also decrease the rate of false negatives. For example, a researcher who continues testing until a significant result is obtained, increases the chances of obtaining a significant result no matter whether the hypothesis is true or false.

Ioannidis recognizes this, but he assumes that bias has the same effect for true hypothesis and false hypothesis. This assumption is questionable because it is easier to produce a significant result if an effect exists than if no effect exists. Ioannidis’s assumption implies that bias increases the proportion of false positive results a lot more than the proportion of true positive results.

For example, if power is 50%, only 50% of true hypothesis produce a significant result. However, with a bias factor of .4, another 40% of the false negative results will become significant, adding another .4*.5 = 20% true positive results to the number of true positive results. This gives a total of 70% positive results, which is a 40% increase over the number of positive results that would have been obtained without bias. However, this increase in true positive results pales in comparison to the effect that 40% bias has on the rate of false positives. As there are 95% true negatives, 40% bias produces another .95*.40 = 38% of false positive results. So instead of 5% false positive results, bias increases the percentage of false positive results from 5% to 43%, an increase by 760%. Thus, the effect of bias on the PPV is not equal. A 40% increase of false positives has a much stronger impact on the PPV than a 40% increase of true positives. Ioannidis provides no rational for this bias model.

A bigger concern is that Ioannidis makes sweeping claims about the proportion of false published findings based on untested assumptions about the proportion of null-effects, statistical power, and the amount of bias due to questionable research practices.
For example, he suggests that 4 out of 5 discoveries in adequately powered (80% power) exploratory epidemiological studies are false positives (PPV = .20). To arrive at this estimate, he assumes that only 1 out of 11 hypotheses is true and that for every 1000 studies, bias adds only 1000* .30*.10*.20 = 6 true positives results compared to 1000* .30*.90*.95 = 265 false positive results (i.e., 44:1 ratio). The assumed bias turns a PPV of 62% without bias into a PPV of 20% with bias. These untested assumptions are used to support the claim that “simulations show that for most study designs and settings, it is more likely for a research claim to be false than true.” (e124).

Many of these assumptions can be challenged. For example, statisticians have pointed out that the null-hypothesis is unlikely to be true in most studies (Cohen, 1994). This does not mean that all published results are true, but Ioannidis’ claims rest on the opposite assumption that most hypothesis are a priori false. This makes little sense when the a priori hypothesis is specified as a null-effect and even a small effect size is sufficient for a hypothesis to be correct.

Ioannidis also ignores attempts to estimate the typical power of studies (Cohen, 1962). At least in psychology, the typical power is estimated to be around 50%. As shown in Table 2, even massive bias would still produce more true than false positive results, if the null-hypothesis is false in no more than 50% of all statistical tests.

In conclusion, Ioannidis’s claim that most published results are false depends heavily on untested assumptions and cannot be considered a factual assessment of the actual number of false results in published journals.

Testing Ioannidis’s Simulations

10 years after the publication of “Why Most Published Research Findings Are False,”  it is possible to put Ioannidis’s simulations to an empirical test. Powergraphs (Schimmack, 2015) can be used to estimate the average replicability of published test results. For this purpose, each test statistic is converted into a z-value. A powergraph is foremost a histogram of z-values. The distribution of z-values provides information about the average statistical power of published results because studies with higher power produce higher z-values.

Figure 1 illustrates the distribution of z-values that is expected for Ioanndis’s model for “adequately powered exploratory epidemiological study” (Simulation 6 in Figure 4). Ioannidis assumes that for every true positive, there are 10 false positives (R = 1:10). He also assumed that studies have 80% power to detect a true positive. In addition, he assumed 30% bias.

ioannidis-fig6

A 30% bias implies that for every 100 false hypotheses, there would be 33 (100*[.30*.95+.05]) rather than 5 false positive results (.95*.30+.05)/.95). The effect on false negatives is much smaller (100*[.30*.20 + .80]). Bias was modeled by increasing the number of attempts to produce a significant result so that proportion of true and false hypothesis matched the predicted proportions. Given an assumed 1:10 ratio of true to false hypothesis, the ratio is 335 false hypotheses to 86 true hypotheses. The simulation assumed that researchers tested 100,000 false hypotheses and observed 35000 false positive results and that they tested 10,000 true hypotheses and observed 8,600 true positive results. Bias was simulated by increasing the number of tests to produce the predicted ratio of true and false positive results.

Figure 1 only shows significant results because only significant results would be reported as positive results. Figure 1 shows that a high proportion of z-values are in the range between 1.95 (p = .05) and 3 (p = .001). Powergraphs use z-curve (Schimmack & Brunner, 2016) to estimate the probability that an exact replication study would replicate a significant result. In this simulation, this probability is a mixture of false positives and studies with 80% power. The true average probability is 20%. The z-curve estimate is 21%. Z-curve can also estimate the replicability for other sets of studies. The figure on the right shows replicability for studies that produced an observed z-score greater than 3 (p < .001). The estimate shows an average replicability of 59%. Thus, researchers can increase the chance of replicating published findings by adjusting the criterion value and ignoring significant results with p-values greater than p = .001, even if they were reported as significant with p < .05.

Figure 2 shows the distribution of z-values for Ioannidis’s example of a research program that produces more true than false positives, PPV = .85 (Simulation 1 in Table 4).

ioannidis-fig1

Visual inspection of Figure 1 and Figure 2 is sufficient to show that a robust research program produces a dramatically different distribution of z-values. The distribution of z-values in Figure 2 and a replicability estimate of 67% are impossible if most of the published significant results were false.  The maximum value that could be obtained is obtained with a PPV of 50% and 100% power for the true positive results, which yields a replicability estimate of .05*.50 + 1*.50 = 55%. As power is much lower than 100%, the real maximum value is below 50%.

The powergraph on the right shows the replicability estimate for tests that produced a z-value greater than 3 (p < .001). As only a small proportion of false positives are included in this set, z-curve correctly estimates the average power of these studies as 80%. These examples demonstrate that it is possible to test Ioannidis’s claim that most published (significant) results are false empirically. The distribution of test results provides relevant information about the proportion of false positives and power. If actual data are more similar to the distribution in Figure 1, it is possible that most published results are false positives, although it is impossible to distinguish false positives from false negatives with extremely low power. In contrast, if data look more like those in Figure 2, the evidence would contradict Ioannidis’s bold and unsupported claim that most published results are false.

The maximum replicabiltiy that could be obtained with 50% false-positives would require that the true positive studies have 100% power. In this case, replicability would be .50*.05 + .50*1 = 52.5%.  However, 100% power is unrealistic. Figure 3 shows the distribution for a scenario with 90% power and 100% bias and an equal percentage of true and false hypotheses. The true replicabilty for this scenario is .05*.50 + .90 * .50 = 47.5%. z-curve slightly overestimates replicabilty and produced an estimate of 51%.  Even 90% power is unlikely in a real set of data. Thus, replicability estimates above 50% are inconsistent with Ioannidis’s hypothesis that most published positive results are false.  Moreover, the distribution of z-values greater than 3 is also informative. If positive results are a mixture of many false positive results and true positive results with high power, the replicabilty estimate for z-values greater than 3 should be high. In contrast, if this estimate is not much higher than the estimate for all z-values, it suggest that there is a high proportion of studies that produced true positive results with low power.

ioannidis-fig3

Empirical Evidence

I have produced powergraphs and replicability estimates for over 100 psychology journals (2015 Replicabilty Rankings). Not a single journal produced a replicability estimate below 50%. Below are a few selected examples.

The Journal of Experimental Psychology: Learning, Memory and Cognition publishes results from cognitive psychology. In 2015, a replication project (OSC, 2015) demonstrated that 50% of significant results produced a significant result in a replication study. It is unlikely that all non-significant results were false positives. Thus, the results show that Ioannidis’s claim that most published results are false does not apply to results published in this journal.

Powergraphs for JEP-LMC3.g

The powergraphs further support this conclusion. The graphs look a lot more like Figure 2 than Figure 1 and the replicability estimate is even higher than the one expected from Ioannidis’s simulation with a PPV of 85%.

Another journal that was subjected to replication attempts was Psychological Science. The success rate for Psychological Science was below 50%. However, it is important to keep in mind that a non-significant result in a replication study does not prove that the original result was a false positive. Thus, the PPV could still be greater than 50%.

Powergraphs for PsySci3.g

The powergraph for Psychological Science shows more z-values in the range between 2 and 3 (p > .001). Nevertheless, the replicability estimate is comparable to the one in Figure 2 which simulated a high PPV of 85%. Closer inspection of the results published in this journal would be required to determine whether a PPV below .50 is plausible.

The third journal that was subjected to a replication attempt was the Journal of Personality and Social Psychology. The journal has three sections, but I focus on the Attitude and Social Cognition section because many replication studies were from this section. The success rate of replication studies was only 25%. However, there is controversy about the reason for this high number of failed replications and once more it is not clear what percentage of failed replications were due to false positive results in the original studies.

Powergraphs for JPSP-ASC3.g

One problem with the journal rankings is that they are based on automated extraction of all test results. Ioannidis might argue that his claim focused only on test results that tested an original, novel, or an important finding, whereas articles also often report significance tests for other effects. For example, an intervention study may show a strong decrease in depression, when only the interaction with treatment is theoretically relevant.

I am currently working on powergraphs that are limited to theoretically important statistical tests. These results may show lower replicability estimates. Thus, it remains to be seen how consistent Ioannidis’s predictions are for tests of novel and original hypotheses. Powergraphs provide a valuable tool to address this important question.

Moreover, powergraphs can be used to examine whether science is improving. So far, powergraphs of psychology journals have shown no systematic improvement in response to concerns about high false positive rates in published journals. The powergraphs for 2016 will be published soon. Stay tuned.