Continuously Cumulating Meta-Analysis and Replicability

Abstract

The current crisis in scientific psychology about whether our findings are irreproducible was presaged years ago by Tversky and Kahneman (1971), who noted that even sophisticated researchers believe in the fallacious Law of Small Numbers-erroneous intuitions about how imprecisely sample data reflect population phenomena. Combined with the low power of most current work, this often leads to the use of misleading criteria about whether an effect has replicated. Rosenthal (1990) suggested more appropriate criteria, here labeled the continuously cumulating meta-analytic (CCMA) approach. For example, a CCMA analysis on a replication attempt that does not reach significance might nonetheless provide more, not less, evidence that the effect is real. Alternatively, measures of heterogeneity might show that two studies that differ in whether they are significant might have only trivially different effect sizes. We present a nontechnical introduction to the CCMA framework (referencing relevant software), and then explain how it can be used to address aspects of replicability or more generally to assess quantitative evidence from numerous studies. We then present some examples and simulation results using the CCMA approach that show how the combination of evidence can yield improved results over the consideration of single studies.
© The Author(s) 2014.

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DOI: 10.1177/1745691614529796
2014 9: 333Perspectives on Psychological Science
Sanford L. Braver, Felix J. Thoemmes and Robert Rosenthal
Continuously Cumulating Meta-Analysis and Replicability
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Over 40 years ago, future Nobel Prize winner Daniel
Kahneman and Amos Tversky1 proved their perspicacity
by anticipating the current crisis of replicability—the
doubt that the same or another researcher can reproduce
(repeatedly) the same phenomenon or empirical rela-
tionship with subsequent empirical investigations, imply-
ing that the phenomenon may be illusory. Presciently, in
their 1971 Psychological Bulletin article entitled “Belief in
the Law of Small Numbers,” Tversky and Kahneman
wrote that “most psychologists have an exaggerated
belief in the likelihood of successfully replicating an
obtained finding” (p. 105). Their article title was a play on
The Law of Large Numbers. This well-proved law dates
back to Jacob Bernoulli in 1713, and “guarantees that
very large samples will indeed be highly representative
of the population from which they are drawn” (Bernoulli,
1713, p. 106). But Tversky and Kahneman noted that
humans, even highly sophisticated researchers, have
“strong” but “wrong” intuitions that “the law of large
numbers applies to small numbers as well” (p. 106).
In the last 2 years, these powerful but misguided intu-
itions have contributed to a profound reconsideration of
social science practice and culture. The replicability of
the totality of psychology’s findings is now being ques-
tioned and challenged. Critics note that disturbingly few
successful replication studies are in our literature
(Carpenter, 2012; Makel, Plucker, & Hegarty, 2012; Open
Science Collaboration, 2012; Yong, 2012; but see the
“many labs” project, Klein et al., 2014). This serves as
proof either that our phenomena are fundamentally false
(i.e., those replication studies that have been attempted
fail to produce supportive findings) or that journals are
biased against replication studies whatever their result
(Giner-Sorolla, 2012; Neuliep & Crandall, 1990, 1993;
Rosenthal, 1979). This feeling of mistrust was further
529796PPSXXX10.1177/1745691614529796Braver et al.Cumulative Meta-Analysis and Replicability
research-article2014
Corresponding Author:
Sanford Braver, Arizona State University, Department of Psychology,
PO Box 876005, Tempe, AZ 85287-6005
E-mail: sanford.braver@asu.edu
Continuously Cumulating Meta-Analysis
and Replicability
Sanford L. Braver1, Felix J. Thoemmes2, and
Robert Rosenthal3
1Arizona State University & University of California, Riverside; 2Cornell University; and
3University of California, Riverside
Abstract
The current crisis in scientific psychology about whether our findings are irreproducible was presaged years ago by
Tversky and Kahneman (1971), who noted that even sophisticated researchers believe in the fallacious Law of Small
Numbers—erroneous intuitions about how imprecisely sample data reflect population phenomena. Combined with
the low power of most current work, this often leads to the use of misleading criteria about whether an effect has
replicated. Rosenthal (1990) suggested more appropriate criteria, here labeled the continuously cumulating meta-
analytic (CCMA) approach. For example, a CCMA analysis on a replication attempt that does not reach significance
might nonetheless provide more, not less, evidence that the effect is real. Alternatively, measures of heterogeneity
might show that two studies that differ in whether they are significant might have only trivially different effect sizes. We
present a nontechnical introduction to the CCMA framework (referencing relevant software), and then explain how it
can be used to address aspects of replicability or more generally to assess quantitative evidence from numerous studies.
We then present some examples and simulation results using the CCMA approach that show how the combination of
evidence can yield improved results over the consideration of single studies.
Keywords
replication, meta-analysis, statistical intuition, effect-size heterogeneity
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334 Braver et al.
fueled by high-profile failures to replicate effects (see
e.g., Bargh, Chen, & Burrow, 1996, and the subsequent
failed replications by Doyen, Klein, Pichon, & Cleeremans,
2012; Harris, Coburn, Rohrer, & Pashler, 2013). The ulti-
mate result, some conclude, is that the “scientific litera-
ture is too good to be true” (Bakker, van Dijk, & Wicherts,
2012, p. 543; Francis, 2012); one cannot believe anything
published, and psychology is filled with mostly invalid
and false explanations. An article in The Chronicle of
Higher Education (Bartlett, 2012) was titled “Is Psychology
About to Become Undone?”
In this article, we argue that the erroneous belief in the
Law of Small Numbers, in combination with the typically
low levels of statistical power of psychological (and other
similar types of) research, has contributed to this crisis by
leading to inappropriate criteria applied to deem an
attempt at a replication unsuccessful. We present an alter-
native and, we believe, superior way to assess evidence
of replication.
The Criterion of Successful Replication
Tversky and Kahneman (1971) posed the following
hypothetical question to sophisticated researchers,
including members of the elite Mathematical Psychology
Group:
Suppose you have run an experiment on 20
subjects, and have obtained a significant result
which confirms your theory (z = 2.23, p < .05, two
tailed). You now have cause to run an additional
group of 10 subjects. What do you think the
probability is that the results will be significant, by
a one-tailed test, separately for this group? (p. 105)
The median answer they obtained from their panel
of expert researchers was .85, which was almost
double the actual probability (which they show to
be about .48). The authors attribute their
respondents’ extraordinary inaccuracy to the
ingrained but fallacious idea that a rather small
sample “randomly drawn from a population is
highly representative, that is, similar to the
population in all essential characteristics.” (p. 105)
The correct general answer to such a hypothetical is
precisely whatever is the statistical power of the test per-
formed in the replication study. Power is commonly des-
ignated 1-β (where β is the probability of a Type II, or
false negative, error). Power is generally determined by
four factors: (a) the population effect size, which is tech-
nically unknown, but is commonly estimated or guessed
at; (b) the total sample size, N; (c) the “sidedness” of the
test (whether one tailed, directional; or two tailed,
nondirectional); and (d) the chosen alpha level, which in
psychology is typically fixed at .05.2 Cohen (1962) esti-
mated that the typical power of published psychological
studies does not exceed 0.5; Sedlmeier and Gigerenzer
(1989) found a similar value among studies conducted in
the subsequent 25 years, indicating that the low power of
most earlier published behavioral research was not recti-
fied by Cohen’s revelation. It has apparently escaped rec-
ognition by most that, with the low levels of power that
replication attempts generally have, even a true effect
will disturbingly often fail to appear successfully repli-
cated if we apply the criterion that Simonsohn (2013)
notes is typically employed in the literature: achieving
conventional levels of significance.
The Continuously Cumulating Meta-
Analytic (CCMA) Approach
In the lead chapter for the book entitled Handbook of
Replication Research in the Behavioral and Social Sciences,
Rosenthal (1990) critiqued the practice we highlighted
above (i.e., determining successful replication based on
whether or not the study also achieved significance). He
described several more appropriate criteria derived from
the meta-analytic framework he helped to popularize.
Standard meta-analysis is generally seen as retrospective
in nature—a literature review that looks backward to
summarize a large set of completed studies. The slight
variation we now term continuously cumulating meta-
analysis (CCMA) performs the exact same meta-analytic
calculations but does so in a continuing fashion after each
new replication attempt completes. In CCMA, instead of
misleadingly noting simply whether each replication
attempt did or did not reach significance, we combine the
data from all the studies completed so far and compute
various meta-analytic indexes3 to index the degree of con-
fidence we can have that a bona fide phenomenon is
being investigated. In other words, the individual effect
sizes of the entirety of completed studies are pooled into
a single estimate. The resulting pooled estimate generally
is more trustworthy because it is based on far more data
than each individual study. As we discuss below, meta-
analysis also allows quantification of the heterogeneity of
results. The CCMA approach therefore shifts the question
from whether or not a single study provided evidential
weight for a phenomenon to the question of how well all
studies conducted thus far support conclusions in regards
to a phenomenon of interest.
Simulating Replication Attempts
To illustrate the CCMA framework and how it can outper-
form a focus on individual studies (and their significance
level), we performed a set of simulations.4 We drew
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Cumulative Meta-Analysis and Replicability 335
random samples from two normal populations with the
identical standard deviations (σ = 1), but the mean of one
population (µI) was .5 greater than the other (µII). Thus,
in these populations, Cohen’s d=
µµ
σ
II
I
- = 0.5, which
is commonly categorized as a “medium” effect size
(Cohen, 1988; r = 0.243), and is in the range of effect
sizes typically found in published psychological research
by recent reviews (Anderson, Lindsay, & Bushman, 1999;
Hall, 1998; Lipsey & Wilson, 1993; Meyer et al., 2001;
Richard, Bond, & Stokes-Zoota, 2003; Tett, Meyer, &
Roese, 1994). We set our cell size at 25 (nI = nII = 25) in
each of two groups for a total sample size of N1 = 50),5
which reflects the median cell size found in recent
summaries of extant research (Marszalek, Barber,
Kohlhart, & Holmes, 2011; Wetzels et al., 2011). Power
calculators, (e.g., http://www.danielsoper.com/statcalc3/
calc.aspx?id=49) show that power = .41 for a two-tailed
test with these parameters (one-tailed power = .54),
which is consistent with the median levels of power that
Cohen (1962) and Sedlmeier and Gigerenzer (1989)
found in published research.
We drew 10,000 random samples per population
group, calculated t tests on each, and tabulated the pro-
portion of samples for which the test reached the .05
level. All of our results for the sample sizes and effect
sizes above, as well as several other possible sample
sizes and effect sizes, are presented in Table 1 (we also
list various criteria by which a replication attempt could
be evaluated; we discuss each criterion in turn through-
out the article).
As a specific example, the results for just the very first
of the 10,000 simulated Study 1s are presented in the top
row of Table 2.
As shown, this simulated Study 1 yielded a mean dif-
ference between the two groups of 0.64 (compared with
the population value of 0.5) and a pooled standard devi-
ation of 1.03 (compared with the population 1.0), yield-
ing an effect size estimate of 0.62 (compared with the
population value of 0.50), and t(48) = 2.20, p = .033 (two
tailed), which fell below the hallowed .05 level and
would therefore be declared significant. Overall, as
shown in the first Criterion 1 entry in Table 1, 42% (very
close to the power calculator value of .41 noted earlier
and listed in the 4th row of Table 1) of the 10,000 sam-
ples had results that similarly reached this level. In other
words, across 10,000 simulated Study 1s testing this real,
medium-sized effect, 42% reached significance.
Then, to simulate a replication attempt with the same
sample size N (i.e., N1 = N2), we drew a second set of
two samples from the same two populations. As a spe-
cific example, examining just the very first of the 10,000
replication attempt samples, whose results are pre-
sented in the second row of Table 2, and comparing to
the illustrative Study 1 in the line above, we found it
yielded a substantially smaller mean difference of 0.40,
and a slightly larger pooled standard deviation of 1.07.
The effect size estimate here, as a result, was substan-
tially smaller (0.37), as was the t test, t = 1.31, p=.198
(two tailed), which failed to reach the .05 level. Many
researchers might regard the second study with the very
nonsignificant results as a failure to replicate and would
express doubt about the robustness of the effect and
perhaps even abandon this line of inquiry. Over the
10,000 samples, as shown in Criterion 2 of Table 1, only
41% of the replication attempt samples reached signifi-
cance (the value of power again, as Tversky &
Kahneman, 1971, noted) and would be declared a suc-
cessful replication by the “achieve significance” dichoto-
mous standard.
Thus, with typical levels of power and effect sizes, if
one uses p < .05 as the criterion for a successful replica-
tion, both power calculations and our simulations show
one will only attain this criterion about 40% of the time
when the phenomenon under study is real. Moreover, in
only 17% (~.422) of the 10,000 samples were both the
original and the replication study significant at .05
(Criterion 3 in Table 1).
Clearly, we expect too much from low power attempts
at replication. We could only appropriately use the
“achieve significance” dichotomous standard for a suc-
cessful replication if studies in the field commonly had
much higher power: the .80–.95 that so many writers
(e.g., Cohen, 1962, 1988; Ellis, 2010) advocate. Until and
unless behavioral science research typically proceeds
with a much higher degree of power than it currently
does, we cannot hope for our discoveries to have the
high levels of reproducibility (at conventional levels of
significance) that other sciences enjoy. Similar points
have been argued by Cumming (2008), for example, who
discourages the use of p values to indicate replication
and champions confidence intervals instead.
In the absence of higher levels of power in typical
social science studies, the CCMA perspective we propose
recommends an alternative, and more appropriate, crite-
rion that can be used in place of achieving significance to
decide the robustness of a phenomenon under study and
whether or not a replication was successful (Rosenthal,
1990). A researcher following CCMA procedures, instead
of regarding the second study in isolation and making a
dichotomous decision about whether it replicated, would
combine both studies.6 Combining the results of the first
sample and first replication study in Table 2 yields, as
shown, Zoverall = 2.42 and an overall p value (two-tailed)
of .016, which is smaller than that of the first study alone
(see Table 2). The effect-size confidence interval, of
course, is similarly narrower after the second study’s
results are combined with the original (not shown). Thus,
a CCMA approach would conclude that after both studies
were conducted, there is more, not less, evidence that the
effect is real. Criterion 4 in Table 1 shows the impact of
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336 Braver et al.
using this superior approach over the 10,000 samples:
69% reached significance (as opposed to only 41% when
considering only Study 2’s results in isolation.) Note that
the second power line of Table 1 shows what a power
calculator would show when the N entered is the sum of
the two sample sizes: 70%, virtually the same as the
CCMA simulated value.
Meta-analysis also provides tests of whether the two
studies results differ from one another. This issue of the
difference in results was similarly presaged by another of
Tversky and Kahneman’s (1971) hypotheticals:
Suppose one of your doctoral students has
completed a difficult and time-consuming
experiment on 40 animals . . . One comparison
yields a highly significant t = 2.70, which is surprising
and could be of major theoretical significance.
Now suppose the student has repeated the initial
study with 20 additional animals, and has obtained
an insignificant result in the same direction, t = 1.24.
What would you recommend now?
Check one (the number of respondents checking
each alternative is in parentheses):
(a) He should pool the results and publish his
conclusion. (0)
(b) He should report the results as a tentative
finding. (26)
(c) He should run another group of [median —
20] animals. (21)
(d) He should try to find an explanation for the
difference between the two groups. (30) (pp.
107–108)
As can be seen, not a single one of the Tversky and
Kahneman (1971) expert respondents thought that (a)
was the best answer.7 The meta-analytic and CCMA
approach, on the other hand, advocates exactly that. But
Alternative (d), which was the modal response, suggests
we should directly compare (as well as combine) the two
studies’ results.
Again, human intuition cannot be relied upon, as the
experts succumbed once more to belief in the false Law
of Small Numbers by perceiving the difference between
the two results as sizable and worthy of explanation.
Tversky and Kahneman declared “Response d is indefen-
sible . . . the difference between the two studies does not
even approach significance . . . the attempt to ‘find an
explanation for the difference between the two groups’ is
in all probability an exercise in explaining noise” (p. 108).
The CCMA framework again offers the appropriate
way to correct fallible intuition and assess quantitatively
whether the two studies in Table 2 have obtained results
that differ.8 The question of whether effect sizes are
homogenous or heterogeneous can be tested in different
ways. Here, we focus on two such methods: The Q statis-
tic, which can be compared against the χ2 distribution to
provide a significance test for effect-size heterogeneity,9
Table 1. Probability of Significance (p < .05) by Various Criteria, for a Range of Study Sample Size (N) Cases and Effect Size(d)
Cases
Variable Case 1 Case 2 Case 3 Case 4 Case 5 Case 6 Case 7 Case 8 Case 9
Study 1 N (N1) 50 50 80 80 50 50 80 80 50
Study 2 N (N2) 50 80 50 80 50 80 50 80 50
d0.5 0.5 0.5 0.5 0.2 0.2 0.2 0.2 0.0
Power (two tailed) according to power calculator
for Study 1, given its N
.41 .41 .60 .60 .10 .10 .14 .14 0
Power (two tailed) according to power calculator
with combined Study 1 & 2 Ns
.70 .79 .79 .88 .17 .20 .20 .24 0
Criterion
1. Study 1 achieves .05 .42 .41 .61 .60 .10 .11 .14 .15 .05
2. Study 2 achieves .05 .41 .60 .42 .60 .11 .14 .11 .14 .05
3. Studies 1 & 2 both achieve .05 .17 .25 .26 .36 .01 .02 .01 .02 .00
4. CCMA achieves .05 .69 .80 .81 .88 .16 .19 .20 .25 .05
5. CCMA achieves .05 and Q-test non significant .65 .76 .77 .84 .15 .18 .19 .23 .05
6. CCMA achieves .05 and I2 is below 50% .58 .67 .68 .74 .13 .16 .17 .21 .04
7. Study 2 achieves .05 .41 .60 .42 .60 .11 .15 .10 .15 .04
8. CCMA achieves .05 .92 .95 .96 .98 .62 .58 .71 .68 .30
9. CCMA achieves .05 and Q-test non significant .87 .90 .92 .94 .58 .54 .67 .64 .28
10. CCMA achieves .05 and I2 below 50% .78 .79 .84 .85 .49 .43 .60 .56 .25
Note: Criterion 7–10 are all based on the samples in which Study 1 achieves p < .05. CCMA = continuously cumulating meta-analysis.
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Cumulative Meta-Analysis and Replicability 337
and the I2 measure (Higgins, Thompson, Deeks, & Altman,
2003), which is purely descriptive (rather than involving a
significance test). Readers can find formulas and exam-
ples for calculating each of these by going to Rosenthal
and Rubin (1982) and Higgins et al., respectively. The
developers of the I2 index (Higgins et al., 2003) recom-
mend the standard of 25% and 50% for designating small
and moderate degrees of heterogeneity, respectively.
Patsopoulos, Evangelou, and Ioannidis (2008), consider
both of those values. Ioannidis, Patsopoulos, and
Evangelou (2007) recommend that confidence intervals
around I2 should be routinely computed.
As applied to the illustrative Study 1 and replication
attempt portrayed in Table 2, Q = .38, p =.54, and I2 = .0.
Any intuition that suggested the initial results failed to
replicate would have to confront the reality that there
was barely any statistical difference between the two
study’s results. Additional results (not shown) indicate
that, over all 10,000 samples, only 4.8% of the simulated
replication attempts had a significant Q statistic (just
about what would be expected, since the null hypothesis
of homogeneity was true); moreover, 76% of all the sam-
ples had a very small I2 of 25% or less, and 85% had an
I2 of less than 50%.
If one had found substantially different effect sizes for
the two studies (e.g., a significant Q value and/or a
descriptively large I2 value), this result would indicate
that homogeneity of effect size is violated, even if the
effect sizes are in the same direction—in other words,
these indicators would suggest that the two studies yield
divergent results. In the context of replication, some
would consider this a failure to replicate (Valentine et al.,
2011). In any event, it should certainly caution us against
interpreting the pooled result as an appropriate summary
measure of effect sizes (since the effect sizes were so dis-
similar that it is not meaningful to consider a common
effect), and spark instead a search for the explanation for
the difference between the two groups (i.e., the modera-
tors of effect size).
In contrast, if the second study’s results meet the com-
bined criterion that the difference in effect sizes between
studies is descriptively quite small and nonsignificant,
whereas the pooled result itself is significant, it should
increase our confidence that the phenomenon is genuine.
The proportion of samples that achieved a significant
pooled estimate and had a nonsignificant heterogeneity Q
statistic (Criterion 5, Table 1) was 65%, only slightly
reduced from the 69% in which heterogeneity was not
considered. The proportion of samples that achieved a sig-
nificant pooled CCMA value and whose descriptive I2 was
below 50% was 58%, only slightly lower. We argue that, in
the face of the typically low levels of power of current
behavioral research, these CCMA values are among the
more appropriate indices of the robustness of effects and
also give a more appropriate picture of what should count
as a successful replication. To aid researchers in obtaining
results from a CCMA analysis as described above, we pro-
vide supplementary materials (also available online at
http://www.human.cornell.edu/hd/qml/software.cfm) in
the form of an annotated Excel spreadsheet and a tem-
plate for R code that uses the “meta” package by Schwarzer
(2007). (See the Supplementary Materials section.)
Attempting Replications Only After the
Initial Study Is Significant
A number of writers (e.g., Pashler & Harris, 2012) have
pointed out that replication studies are generally under-
taken, even by the original researchers, when the original
study achieves significance. Initial studies investigating a
clearly nonsignificant relationship or phenomenon are
shelved (or “file-drawer”-ed; Cooper, 1979; Rosenthal,
1979; see also, http://www.psychfiledrawer.org/about
.php), not published, and largely dismissed as false starts.
Thus, if we are to accurately assess how our proposed
criteria would fare in the face of this real-world tendency
for researchers to only follow up significant Study 1s, we
need to investigate the above alternatives as conditional
criteria of a successful replication (i.e., conditional on the
initial study being significant.) To do so, our simulation
set aside those 58% of samples in which Study 1 did not
achieve significance, and we studied these various crite-
ria only for the 42% of Study 1s that attained significance.
Given a significant effect in Study 1, how often is the
effect in Study 2 significant? Of course, this value was
within simulation-rounding error of the power calculator
value of the test: 41% (see Criterion 7 in Table 1).10 The
probability that the CCMA pooled value over the two
studies achieved significance was a reassuring 92% of the
samples, as noted by Criterion 8 in Table 1. Likewise, in
87% of the samples in which Study 1 reached p < .05,
significance was also achieved for the CCMA pooled
effect and heterogeneity was nonsignificant (Criterion 9
in Table 1). Finally, in 78% of the samples in which Study
1 reached p < .05, significance was achieved for the
CCMA pooled effect and I2 was less than 50% (Criterion
Table 2. Results From a Simulated Study and a Replication
Attempt, With a CCMA Analysis
Study
Mean
diff spooled t p
ES (Cohen’s
d)Z
Original 0.64 1.03 2.19 0.033 0.62 2.13
Replication
attempt
0.40 1.07 1.31 0.198 0.37 1.29
CCMA results 0.016 0.49 2.42
Note: Homogeneity test was nonsignificant, Q(1) = .38, p = .54, I2 =
0.00. ES = effect size.
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338 Braver et al.
10 in Table 1). Thus, after an original study obtains sig-
nificance, the proper course for the subsequent attempt
is to pool its result with Study 1 and look for differences
in effect sizes using either significance tests and the Q
statistic, the descriptive I2 measure, or some other descrip-
tive index of heterogeneity. The bottom line about the
Case 1 results in Table 1 (which were based on the typi-
cal sample sizes of 25 per group and the typical effect
size of 0.50) is that the chances of running another study
(with the same N) and obtaining a successful replication
by this CCMA approach is about 80%.
Table 1 also contains additional columns for other pos-
sible sample sizes (80 and 50 for each of the two studies—
either 40 or 25 per group) and other effect sizes (d = 0.2,
commonly deemed a “small” effect size, as well as a null
effect of d = 0.0; see Cases 8 and 9 of Table 1). As can be
seen, small effect-size studies have a disappointing likeli-
hood of achieving significance (generally less than a 20%
chance) either individually or even when pooled.
Nevertheless, Table 1 shows that if the initial N = 50 study
does achieve significance (despite the low odds), the
pooled result (Criterion 8) has a power of .71 (Case 8) to
be significant in the large sample size (N = 80, with 40 per
group) condition. And even if both the original and the
replication attempt study use only 25 subjects per group,
the combined pooled criterion is above 60%. True null
effects (Case 9 of Table 1), however, tend not to obtain
significance by any criteria (other than the conditional
ones, due to the fact that the original study was a Type 1
error—in such cases, the cumulative estimate of the effect
will move closer and closer to zero as additional studies
accumulate, as discussed later in this article).
Additional Replication Attempts and
the Life-Course of Replications
The CCMA approach advocates recomputing meta-ana-
lytic indices described in the first section as each new
replication attempt is completed. Our confidence should
increase that the phenomenon under study is genuine
and true to the degree that the combined criterion
remains significant, whereas indices of heterogeneity
(e.g., Q and I2) remain small and nonsignificant. Larger Q
and I2 values should prompt the search for plausible
moderator variables (i.e., dissimilar features of those
studies with distinctly differing effect size values).
Figure 1 depicts this outcome (using the combined
criterion of significant CCMA and nonsignificant Q sta-
tistic) over the course of a series of replication attempts,
given various effect sizes. These “life-course trajectories”
in Figure 1 are for the example of the following sequence
of total sample sizes in replication Studies 1 through 7:
50, 50, 20, 70, 70, 50, 80. (We also examined other sam-
ple sizes and effect sizes, but figures did not differ
appreciably.) Compared with what appears a more-or-
less random walk trajectory for the probability that indi-
vidual studies attain significance, the CCMA approach
tends toward consistently higher pooled significance. As
can also be seen, the CCMA life course of a true effect
is much different than for a null effect (i.e., when d = 0).
Even for a small effect size, undertaking a series of rep-
lication attempts and cumulating their results eventually
leads to high probabilities of (combined-pooled) signifi-
cance. Incidentally, this was exactly the result of a recent
replication conducted by the Many Labs project” (Klein
et al., 2014). The authors of this orchestrated replication
attempt found that of 13 classic findings in psychology
(e.g., the anchoring effect), 10 soundly replicated. As an
example, the replication attempts of the Quote
Attribution study (Lorge & Curtiss, 1936), saw several
nonsignificant replications (some even with opposite
signs); however, the pooled effect estimate of all repli-
cations was extremely narrow and centered around a
positive effect of about d = 0.25.
In fact, the meta-analytic perspective discourages alto-
gether dichotomous decisions based on .05, even for
meta-analytic results such as CCMA tests, and instead
advocates employing only continuous descriptive crite-
ria—for example, effect size estimates and their confi-
dence intervals (continuous p levels can also be useful,
but not dividing them into two categories, the “signifi-
cant” and the non-significant). This general preference
for confidence intervals and effect sizes (and confidence
intervals around effect sizes) has been advocated by
numerous authors (e.g., Cumming, 2013; Cumming &
Finch, 2001; Thompson, 2002). As is well-known, the .05
criterion for what constitutes convincing evidence is
completely arbitrary. As Rozeboom (1960) states,
“Acceptance of a proposition is not an all-or-none affair;
rather it is a matter of degree” (pp. 420–421). In Rosnow
and Rosenthal’s (1989) words, “surely, God loves the .06
nearly as much as the .05” (p. 1277). Imagine how
research reports would change if the word significant
were stricken from our scientific vocabulary. Researchers
would need to argue for each finding’s importance anew
without relying on rarely applicable one-size-fits-all rules
of thumb.
Recommendations
Our recommendations on how to improve the assess-
ment of evidential weight of numerous studies are based
on our understanding of the perfidious impact of belief
in the Law of Small Numbers and on the CCMA approach
presented here. First, and most important, we need to
recognize that the core problem is the very low statistical
power of most research in psychological and behavioral
science combined with the failure of our intuition to
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Cumulative Meta-Analysis and Replicability 339
anticipate its pernicious effects. The call for higher power
is certainly not a new one (see, e.g., Cohen, 1962; Lakens
& Evers, 2014, this issue; Sedlmeier & Gigerenzer, 1989),
however it is worth repeating. In fact, there are some
reassuring signs that this trend is very recently changing
(e.g., the Many Labs replication project prioritized ade-
quately powered replication attempts; Perugini, Gallucci,
& Costantini, 2014, this issue; Stanley & Spence, 2014, this
issue). If all psychological research were carried out with
power near .95—or even .80—replication problems
would arguably diminish. True effects would virtually
always achieve significance and virtually always be repli-
cable, and researchers would start being more interested
in effect sizes. We wouldn’t have to contend with falla-
cious beliefs such as the Law of Small Numbers, we’d
instead have suitably large numbers. Arguably, p hacking
(Simmons, Nelson, & Simonsohn, 2011) and other ques-
tionable research practices ( John, Loewenstein, & Prelec,
2012) would diminish, because significance in high-pow-
ered studies would in fact be achieved without tricks. If
psychology is serious about solving its inferential prob-
lems and achieving the credibility and reproducibility of
the physical sciences, this requirement will do the trick
(Cohen, 1994).
It is interesting to note that Tversky and Kahneman’s
(1971) own intuition failed on this point. They wrote “We
refuse to believe that a serious investigator will know-
ingly accept a .50 risk of failing to confirm a valid research
hypothesis” (p. 110). On this they were clearly overly
optimistic. Virtually all investigators and almost all publi-
cation outlets have contributed to the field being overrun
with very underpowered studies despite decades of
knowing of the problem.
In any event, we need a better lens with which to view
replication efforts than whether they achieve significance.
The field has come to accept meta-analysis as the stan-
dard for conducting retrospective literature reviews. We
need to adopt a similar perspective, a continuously
cumulating meta-analysis (CCMA), to evaluate the valid-
ity of research results as each replication attempt is
obtained. We have demonstrated that such an approach
yields not only a more accurate, but also a richer picture
of the pooled effect of numerous studies. The pooled
effect estimates are a mathematically sound way to
Fig. 1. Probability of achieving a significant result for a single study (dashed line) or a significant CCMA estimate (solid lines) using Criterion
5 from Table 1 for a sequence of studies with the sample sizes specified along the x axis when testing effect sizes ranging from d = 0 to d = .5.
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340 Braver et al.
combine effects and indices of heterogeneity help to
quantify the amount of discrepancies among studies.
The CCMA approach however is no panacea to fix
each and every problem in the field. If studies in the lit-
erature have been p hacked and thereby overestimate
effect sizes, this will bias the CCMA estimate as well.
Likewise, publication bias (and the omission of negative
results in the literature) can influence CCMA estimates.
However, indices of heterogeneity and measures like the
funnel plot (Sterne & Egger, 2001) can help to identify
publication bias. In addition, alternative measures such
as p curves (Lakens, 2014; Nelson, Simonsohn, &
Simmons, 2014; Schimmack, 2012) can help to identify if
studies have been severely p hacked and such studies
could be excluded from a CCMA. Using and encouraging
others to use CCMA could also help decrease p hacking
and publication bias: If a nonsignificant Study 2 can be
published as part of a package of studies that together
produce a significant CCMA, researchers will be more
likely to include nonsignificant individual findings in
their papers (see also Maner, 2014, this issue).
However, the CCMA approach need not be confined
to replication studies, but can likewise be used to com-
bine internal replications of multistudy articles. This
would be far more informative then simply reporting
whether each single study succeeded or failed. We have
reviewed the statistical tools to conduct CCMA analyses
and hope that readers will implement these tools in their
own research and encourage others to do so when
reviewing articles or replication proposals.
Acknowledgments
The authors are grateful to the following readers of earlier
drafts for helpful comments: Todd S. Braver, David Funder,
Robert J. MacCoun, Irwin N. Sandler, and Stephen G. West. We
also benefitted from discussions with Deanna M. Barch, Daniel
Ozer, Piotr Winkielman, and the participants in the Quantitative
Seminar at University of California, Riverside.
Declaration of Conflicting Interests
The authors declared that they had no conflicts of interest with
respect to their authorship or the publication of this article.
Notes
1. Tversky passed away before the Nobel prize was given to
Kahneman, but Kahneman (2002) acknowledged they were
essentially joint winners.
2. A fifth determinant is the properties of the exact statistical
procedure conducted.
3. A huge literature exists on meta-analytic techniques.
Good readable summaries are Lipsey and Wilson (2001) and
Rosenthal (1984). Many reasonable meta-analytic indices have
been proposed, and we don’t mean to imply by our choices
of ones to feature here that these are necessarily the superior
ones. The indices we feature are Zoverall, which we refer to as
CCMA (for formulas and discussion, see Rosenthal, 1984, 1990;
Rosenthal & Rubin, 1979, 1982); Q (Hedges, 1982; Rosenthal,
1984; Rosenthal & Rubin, 1982); and I2 (Higgins et al., 2003).
4. Many of the results presented herein can be analytically
derived, but we used simulations throughout for consistency
and to make the points concrete.
5. Our notation uses lower case n with Roman numeral sub-
scripts to refer to sample size per group (generally we consider
only two groups of equal size, so nI = nII), and capital N with
numeric subscripts to refer to sample size per study.
6. The easiest way of doing so is by converting each of the one-
tailed p values to a Z. The Excel function NORMSINV is one
way of obtaining these values. For example, consider the sec-
ond row of Table 2, in which t = 1.31 and p = .198. The .198 is
the two-tailed p value. To obtain the Z for the one-tailed p value
(which is shown to equal 1.29), use “=NORMSINV(1−.198/2)”.
Then the various resulting Z values are summed and the total
is divided by the square-root of the number of Zs (or studies),
in this case √2. Alternative meta-analytic formulas (for exam-
ple, those given by Borenstein, Hedges, Higgins, & Rothstein,
2011) are also available for computing a significance test of
the pooled effect estimate. These meta-analytic pooled esti-
mates can be based on either fixed or random-effects models.
If assuming direct replications, a fixed-effect model is appropri-
ate. Our results in Tables 1 and 2 are based on fixed-effects
models. Random-effects models have slightly larger standard
errors and thus wider confidence intervals. We obtained results
for random-effects models as well, but other than being slightly
less powerful, patterns of results did not change.
7. Tversky and Kahneman (1971) actually added the words “as
fact” at the end of the phrase for Alternative (a), which is per-
haps why not a single respondent chose it. They also thought
that Alternatives (b) and (c) were acceptable and could “be
justified on some grounds” (p. 108).
8. The CCMA approach produces the same mean estimate of
the cumulative effect size as a standard Bayesian approach but
adds the investigation of homogeneity. On the other hand, it
loses information about the distribution of the posterior, which
might also be quite interesting.
9. These indices weight large N studies more highly than low N
studies, based on the recognition that their respective effect-size
estimates are differentially precise. The statistical power of the
Q test has been frequently recognized as rather low (Huedo-
Medina, Sánchez-Meca, Marín-Martínez, & Botella, 2006), in that
it fails to detect as significant even sizable differences in effect
size. This poses an especial problem for tests of homogeneity
because the researcher commonly hopes not to reject the null
hypothesis. Some (e.g., Berlin, Laird, Sacks, & Chalmers, 1989;
Fleiss, 1993; Petitti, 2001) recommend raising the power of such
tests by raising their alpha to .10 rather than .05.
10. The homogeneity of the effect size Q-statistics being signifi-
cant remained quite similar at 5.6% (not shown).
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