Questions and Answers: Reproducibility and a Stricter Threshold for Statistical Significance

“Redefine statistical significance,” a paper recently published in Nature Human Behavior (Benjamin et al., 2017) generated a substantial amount of discussion in methodological circles. This paper proposes to lower the \alpha threshold for statistical significance from the conventional level of 0.05 to a new, more stringent level of 0.005 and to apply this threshold specifically to newly discovered relationships (i.e., relationships that have not yet been demonstrated in multiple studies). This proposal touched off a debate about the effect null hypothesis significance testing (NHST) has on published work in the social and behavioral sciences in which many statisticians and social scientists have participated. Some have proposed alternative reforms that they believe will be more effective at improving the replicability of published results.

To facilitate further discussion of these proposals—and perhaps to begin to develop an actionable plan for reform—the International Methods Colloquium (IMC) hosted a panel discussion on “reproducibility and a stricter threshold for statistical significance” on October 27, 2017. The one-hour discussion included six panelists and over 240 attendees, with each panelist giving a brief initial statement concerning the proposal to “redefine statistical significance” and the remainder of the time being devoted to questions and answers from the audience. The event was recorded and can be viewed online for free at the International Methods Colloquium website.

Unfortunately, the IMC’s time limit of one hour prevented many audience members from asking their questions and having a chance to hear our panelists respond. Panelists and audience members alike agreed that the time limit was not adequate to fully explore all the issues raised by Benjamin et al. (2017). Consequently, questions that were not answered during the presentation were forwarded to all panelists, who were given a chance to respond.

The questions and answers, both minimally edited for clarity, are presented in this article. The full series of questions and answers (and this introduction) are embedded in the PDF below.

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New Print Edition Released!

Volume 24, Number 2 of The Political Methodologist has just been released!


You can find a direct link to a downloadable version of the print edition here [update: a version with a minor correction has been added as of 5:23 PM on 9/26/2017]:

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Minnesota Political Methodology Colloquium Graduate Student Conference 2018

(Post by Carly Potz-Nielsen and Robert Ralston)

We are very excited to announce a new Minnesota Political Methodology Colloquium (MPMC) initiative: the Minnesota Political Methodology Graduate Student Conference.  The conference is scheduled for May 4 & May 5, 2018.

The Minnesota Political Methodology Graduate Student Conference is designed to provide doctoral students with feedback on their research from peers and faculty. Research papers may focus on any substantive topic, employ any research methodology, and/or be purely methodological. We are particularly interested in novel applied work to interesting and important questions in political science, sociology, psychology, and related fields.

The conference represents a unique opportunity for graduate students in different programs, across different disciplines, and with different substantive interests to network and receive feedback on their work.  Papers will receive feedback from a faculty discussant, written feedback from other panelists, and comments/suggestions from audience members.  

The conference will occur over two days (May 4 and May 5, 2018) and feature at least 24 presentations in 6 panels. Proposals are due December 1, 2017.

Our keynote speaker for the event is Sara Mitchell, F. Wendell Miller Professor of Political Science at the University of Iowa. 

Details about the conference may be found here.

Questions should be addressed to

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Response to MacKinnon and Webb

Barry C. Burden, David T. Canon, Kenneth R. Mayer, and Donald P. Moynihan

MacKinnon and Webb offer a useful analysis of how the uncertainty of causal effects can be underestimated when observations are clustered and the treatment is applied to a very large or vary small share of the clusters. Their mathematical exposition, simulation exercises, and replication analysis provide a helpful guide for how to proceed when data are poorly behaved in this way. These are valuable lessons for researchers studying impacts of policy in observational data where policies tend to be sluggish and thus do not generate much variability in the key explanatory variables.

Correction of Two Errors

MacKinnon and Webb find two errors in our analysis, while nonetheless concluding “we do not regard these findings as challenging the conclusions of Burden et al. (2017).” Although we are embarrassed by the mistakes, we are also grateful for their discovery.1 Our commitment to transparency is reflected by the fact the data was been made public for replication purposes since well before the article was published. We have posted corrected versions of the replication files and published a corrigendum with the journal where the article was original published.

Fortunately, none of the other analyses in our article were affected. It is only Table 7 where errors affect the analysis. Tables 2 through 6 remain intact.

We concede that when corrections are made the effect of early voting drops from statistical significance in the model of the difference in the Democratic vote between 2008 and 2012. All of the various standard errors they report are far too large to reject the null hypothesis.

The Problem of Limited Variation

The episode highlights the tradeoffs that researchers face between applying what appears to be a theoretically superior estimation technique (i.e., difference-in-difference) and the practical constraints of a particular application (i.e., limited variation in treatment variables) that make its use intractable. In the case of our analysis, election laws do not change rapidly, and the conclusions of our analysis were largely based on cross-sectional analyses (Tables 2-6), with the difference-in-difference largely offered as a supplemental analysis.

We are in agreement with MacKinnon and Webb that models designed to estimate causal effects (or even simple relationships) may be quite tenuous when the number of clusters is small and the clusters are treated in a highly unbalanced fashion. In fact, we explained our reluctance to apply the difference-in-difference model to our data because of the limited leverage available. We were explicit about our reservations in this regard. As our article stated:

“A limitation of the difference-in-difference approach in our application is that few states actually changed their election laws between elections. As Table A1 (see Supplemental Material) shows, for some combinations of laws there are no changes at all. For others, the number of states changing is as low as one or two. As result, we cannot include some of the variables in the model because they do not change. For some other variables, the interpretation of the coefficients would be ambiguous given the small number of states involved; the dummy variables essentially become fixed effects for one or two states” (p. 572).

This is unfortunate in our application because the difference-in-difference models are likely to be viewed as more convincing than the cross-sectional models. This is why we offered theory suggesting that the more robust cross-sectional results were not likely to suffer from endogeneity.

The null result in the difference-in-difference models is not especially surprising given our warning above about the limited leverage provided by the dataset. Indeed, the same variable was insignificant in our model of the Democratic vote between 2004 and 2008 that we also reported in Table 7. We are left to conclude that the data are not amenable to detecting effects using difference-in-difference models. Perhaps researchers will collect data from more elections to provide more variation in the key variable and estimate parameters more efficiently.

In addition to simply replicating our analysis, MacKinnon and Webb also conduct an extension to explore asymmetric effects. They separate the treated states into those where early voting was adopted and where early voting was repealed. We agree that researchers ought to investigate such asymmetries. We recommended as much in our article: “As early voting is being rolled back in some states, future research should explore the potential asymmetry between the expansion and contraction of election practices” (p. 573). However, we think this is not feasible with existing data. As MacKinnon and Webb note, only two states adopted early voting and only one state repealed early voting. As a result, analyzing these cases separately as they do essentially renders the treatment variables to be little more than fixed effects for one or two states, as we warned in our article. The coefficients might be statistically significant using various standard error calculations, but it is not clear that MacKinnon and Webb are actually estimating the treatment effects rather than something idiosyncratic about one or two states.


While the errors made in our difference-in-difference analysis were regrettable, we think the greater lesson from the skilled analysis of MacKinnon and Webb is to raise further doubt about whether this tool is simply unsuitable in such a policy setting. While all else is equal, it may offer a superior mode of analysis; but all else is not equal. Researchers need to find the best mode of analysis to fit with the limitations of the data.


  1. The mistake in coding Alaska is inconsequential because, as MacKinnon and Webb note, observations from Alaska and Hawaii are dropped from the multivariate analysis.
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Pitfalls when Estimating Treatment Effects Using Clustered Data

James G. MacKinnon, Department of Economics, Queen’s University1
Matthew D. Webb, Department of Economics, Carleton University

Extended Abstract

There is a large and rapidly growing literature on inference with clustered data, that is, data where the disturbances (error terms) are correlated within clusters. This type of correlation is commonly observed whenever multiple observations are associated with the same political jurisdictions. Observations might also be clustered by time periods, industries, or institutions such as hospitals or schools.

When estimating regression models with clustered data, it is very common to use a “cluster-robust variance estimator” or CRVE. However, inference for estimates of treatment effects with clustered data requires great care when treatment is assigned at the group level. This is true for both pure treatment models and difference-in-differences regressions, where the data have both a time dimension and a cross-section dimension and it is common to cluster at the cross-section level.

Even when the number of clusters is quite large, cluster-robust standard errors can be much too small if the number of treated (or control) clusters is small. Standard errors also tend to be too small when cluster sizes vary a lot, resulting in too many false positives. Bootstrap methods based on the wild bootstrap generally perform better than t-tests, but they can also yield very misleading inferences in some cases. In particular, what would otherwise be the best variant of the wild bootstrap can underreject extremely severely when the number of treated clusters is very small. Other bootstrap methods can overreject extremely severely in that case.

In Section 2, we briefly review the key ideas of cluster-robust covariance matrices and standard errors. In Section 3, we then explain why inference based on these standard errors can fail when there are few treated clusters. In Section 4, we discuss bootstrap methods for cluster-robust inference. In Section 5, we report (graphically) the results of several simulation experiments which illustrate just how severely both conventional and bootstrap methods can overreject or underreject when there are few treated clusters. In Section 6, the implications of these results are illustrated using an empirical example from Burden, Canon, Mayer, and Moynihan (2017). The final section concludes and provides some recommendations for empirical work.

Full Article


Replication File

Replication files for the Monte Carlo simulations and the empirical example can be found at: doi:10.7910/DVN/GBEKTO .

  1. We are grateful to Justin Esarey for several very helpful suggestions and to Joshua Roxborough for valuable research assistance. This research was supported, in part, by a grant from the Social Sciences and Humanities Research Council of Canada. Some of the computations were performed at the Centre for Advanced Computing at Queen’s University.
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International Methods Colloquium Schedule for AY 2017-2018

I’m pleased to announce the schedule of speakers in the International Methods Colloquium Series for 2017-2018!

Arthur Spirling (New York University) October 20th
Roundtable on Reproducibility and a Stricter Threshold for Statistical Significance: Dan Benjamin (University of Southern California), Daniel Lakens (Eindhoven University of Technology), and E.J. Wagenmakers(University of Amsterdam) October 27th
Will Hobbs (Northeastern University) November 3rd
Adeline Lo (Princeton University) November 10th
Olga Chyzh (Iowa State University) November 17th
Pamela Ban (Harvard University) December 1st
Teppei Yamamoto (Massachussetts Institute of Technology) February 2nd
Clay Webb (University of Kansas) February 16th
Mark Pickup (Simon Fraser University) February 23rd
Erik Peterson (Dartmouth College) March 2nd
Casey Crisman-Cox (Washington University in St. Louis) March 9th
Erin Hartman (University of California, Los Angeles) March 23rd

Note that all presentations will begin at noon Eastern time and last for one hour. Additional information for each presentation (including a title and link to relevant paper) will be released closer to its date. You can preregister to attend a presentation by clicking on the link in the Google Calendar entry corresponding to the talk; the IMC’s Google Calendar is available at (Anyone can show up the day of the presentation without pre-registering if they wish as long as room remains; there are 500 seats available in each webinar.)

The International Methods Colloquium (IMC) is a weekly seminar series of methodology-related talks and roundtable discussions focusing on political methodology; the series is supported by Rice University and a grant from the National Science Foundation. The IMC is free to attend from anywhere around the world using a PC or Mac, a broadband internet connection, and our free software. You can find out more about the IMC at our website,, where you can register for any of these talks and/or join a talk in progress using the “Watch Now!” link. You can also watch archived talks from previous IMC seasons at this site.

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Lowering the threshold of statistical significance to p < 0.005 to encourage enriched theories of politics

by Justin Esarey, Associate Professor of Political Science at Rice University1


A large and interdisciplinary group of researchers recently proposed redefining the conventional threshold of statistical significance from p < 0.05 to p < 0.005, both two-tailed (Benjamin et al. 2017). The purpose of the reform is to “immediately improve the reproducibility of scientific research in many fields” (p. 5); this comes in the context of recent large-scale replication efforts that have uncovered startlingly low rates of replicability among published results (e.g., Klein et al. 2014; Open Science Collaboration 2015). Recent work suggests that results that meet a more stringent standard for statistical significance will indeed be more reproducible (V. E. Johnson 2013; Esarey and Wu 2016; V. E. Johnson et al. 2017). Reproducibility should be improved by this reform because the false discovery rate, or the proportion of statistically significant findings that are null relationships (Benjamini and Hochberg 1995), is reduced by its implementation. Benjamin et al. (2017) explicitly disavow a requirement that results meet the stricter standard in order to be publishable, but in the past statistical significance has been used as a necessary condition for publication (T. D. Sterling 1959; T. Sterling, Rosenbaum, and Winkam 1995) and we must therefore anticipate that a redefinition of the threshold for significance may lead to a redefinition of standards for publishability.

As a method of screening empirical results for publishability, the conventional p < 0.05 null hypothesis significance test (NHST) procedure lies on a kind of Pareto frontier: it is difficult to improve its qualities on one dimension (i.e., increasing the replicability of published research) without degrading its qualities on some other important dimension. This makes it hard for any proposal to displace the conventional NHST: such a proposal will almost certainly be worse in some ways, even if it is better in others. For moving the threshold for statistical significance from 0.05 to 0.005, the most obvious tradeoff is that the power of the test to detect non-null relationships is harmed at the same time that the size of the test (i.e., its propensity to mistakenly reject a true null hypothesis) is reduced. The usual way of increasing the power of a study is to increase the sample size, N; given the fixed nature of historical time-series cross-sectional data sets and the limited budgets of those who use experimental methods, this means that many researchers may feel forced to accept less powerful studies and therefore have fewer opportunities to publish. Additionally, reducing the threshold for statistical significance can exacerbate publication bias, i.e., the extent to which the published literature exaggerates the magnitude of an relationship by publishing only the largest findings from the sampling distribution of a relationship (T. Sterling, Rosenbaum, and Winkam 1995; Scargle 2000; Schooler 2011; Esarey and Wu 2016).

Simply accepting lower power in exchange for a lower false discovery rate would increase the burden on the most vulnerable members of our community: assistant professors and graduate students, who must publish enough work in a short time frame to stay in the field. However, there is a way of maintaining adequate power using p < 0.005 significance tests without dramatically increasing sample sizes: design studies that conduct conjoint tests of multiple predictions from a single theory (instead of individual tests of single predictions). When K-many statistically independent tests are performed on pre-specified hypotheses that must be jointly confirmed in order to support a theory, the chance of simultaneously rejecting them all by chance is αK where p < α is the critical condition for statistical significance in an individual test. As K increases, the α value for each individual study can fall and the overall power of the study often (though not always) increases. It is important that hypotheses be specified before data analysis and that failed predictions are reported; simply conducting many tests and reporting the statistically significant results creates a multiple comparison problem that inflates the false positive rate (Sidak 1967; Abdi 2007). Because it is usually more feasible to collect a greater depth of information about a fixed-size sample rather than to greatly expand the sample size, this version of the reform imposes fewer hardships on scientists at the beginning of their careers.

I do not think that an NHST with a lowered α is the best choice for adjudicating whether a result is statistically meaningful; approaches rooted in statistical decision theory and with explicit assessment of out-of-sample prediction have advantages that I consider decisive. However, if reducing α prompts us to design research stressing the simultaneous testing of multiple theoretical hypotheses, I believe this change would improve upon the status quo—even if passing this more selective significance test becomes a requirement for publication.

False discovery rates and the null hypothesis significance test

Based on the extant literature, I believe that requiring published results to pass a two-tailed NHST with α = 0.05 is at least partly responsible for the “replication crisis” now underway in the social and medical sciences (Wasserstein and Lazar 2016). I also anticipate that studies that can meet a lowered threshold for statistical significance will be more reproducible. In fact, I argued these two points in a recent paper (Esarey and Wu 2016). Figure 1 reproduces a relevant figure from that article; the y-axis in that figure is the false discovery rate (Benjamini and Hochberg 1995), or FDR, of a conventional NHST procedure with an α given by the value on the x-axis. Written very generically, the false discovery rate is:

FDR = \Pr(\text{null hypothesis is true} | \text{result is stat. sig.}) = \frac{A}{A+B}

A = \Pr(\text{result is stat. sig.}|\text{null hypothesis is true})\Pr(\text{null hypothesis is true})

B = \Pr(\text{result is stat. sig.}|\text{null hypothesis is false})(1-\Pr(\text{null hypothesis is true}))

or, the proportion of statistically significant results (“discoveries”) that correspond to true null hypotheses. A is a function of the power of the test, Pr(stat. sig.|null hypothesis is true). B is a function of the size of the test, Pr(stat. sig.|null hypothesis is false). Both A and B are a function of the underlying proportion of null hypotheses being proposed by researchers, Pr(null hypothesis is true).


As Figure 1 shows, when Pr(null hypothesis is true) is large, there is a very disappointing FDR among results that pass a two-tailed NHST with α = 0.05. For example, when 90% of the hypotheses tested by researchers are false leads (i.e., Pr(null hypothesis is true)=0.9), we may expect nearly ≈30% of discoveries to be false when all studies have perfect power (i.e., Pr(stat. sig.|null hypothesis is false)=1). Two different studies applying disparate methods to data from the Open Science Collaboration’s replication project data (2015) have determined that approximately 90% of researcher hypotheses are false (V. E. Johnson et al. 2017; Esarey and Liu 2017); consequently, an FDR in the published literature of at least 30% is attributable to this mechanism. Even higher FDRs will result if studies have less than perfect power.

By contrast, Figure 1 also shows that setting α ≈ 0.005 would greatly reduce the false discovery rate, even when the proportion of null hypotheses posed by researchers is extremely high. For example, if 90% of hypotheses proposed by researchers are false, the lower bound FDR in the published literature among studies meeting the higher standard would be about 5%. Although non-null results are not always perfectly replicable in underpowered studies (and null results have a small chance of being successfully replicated), a reduction in the FDR from ≈30% to ≈5% would almost certainty and drastically improve the replicability of published results.

The Pareto frontier of adjudicating statistically meaningful results

Despite this and other known weaknesses of the current NHST, it lies on or near a Pareto frontier of possible ways to classify results as “statistically meaningful” (one aspect of being suitable for publication). That is, it is challenging to propose a revision to the NHST that will bring improvements without also bringing new or worsened problems, some of which may disproportionately impact certain segments of the discipline. Consider some dimensions on which we might rate a statistical test procedure, the first few of which I have already discussed above:

  1. the false discovery rate created by the procedure, itself a function of:
    1. the power of the procedure to detect non-zero relationships, and
    2. the size of the procedure, its probability of rejecting true null hypotheses;
  2. the degree of publication bias created by the procedure, i.e., the extent to which the published literature exaggerates the size of an effect by publishing only the largest findings from the sampling distribution of a relationship (T. Sterling, Rosenbaum, and Winkam 1995; Scargle 2000; Schooler 2011; Esarey and Wu 2016);
  3. the number of researcher assumptions needed to execute the procedure, a criterion related to the consistency of the standards implied by use of the test; and
  4. the complexity, or ease of use and interpretability, of the procedure.

It is hard to improve on the NHST in one of these dimensions without hurting performance in another area. In particular, lowering α from 0.05 to 0.005 would certainly lower the power of most researchers’ studies and might increase the publication bias in the literature.

Size/power tradeoffs of lowering α

Changing the α of the NHST from 0.05 to 0.005 is a textbook example of moving along a Pareto frontier because the size and the power of the test are in direct tension with one another. Because powerful research designs are more likely to produce publishable results when the null is false, maintaining adequate study power is especially critical to junior researchers who need publications in order to stay in the field and advance their careers. The size/power tradeoff is depicted in Figure 2.


Figure 2 depicts two size and power analyses for a coefficient of interest β. I assume that \sigma_{\hat{\beta}}, the standard deviation of the sampling distribution of β, is equal to 1; I also assume 100 degrees of freedom (typically corresponding to a sample size slightly larger than 100. In the left panel (Figure 2a), the conventional NHST with α = 0.05 is depicted. In the right panel (Figure 2b), the Benjamin et al. (2017) proposal to decrease α to 0.005 is shown. The power analyses assume that the true β = 3, while the size analyses assume that β = 0.

The most darkly shaded area under the right hand tail of the t-distribution under the null is the probability of incorrectly rejecting a true null hypothesis, α. As the figure shows, it is impossible to shrink α without simultaneously shrinking the lighter shaded area, where the lighter shading depicts the power of a hypothesis test to correctly reject a false null hypothesis. This tradeoff can be more or less severe (depending on β and \sigma_{\hat{\beta}}), but always exists. The false discovery rate will still (almost always) improve when α falls from 0.05 to 0.005, despite the loss in power, but many more true relationships will not be discovered under the latter standard.

Increased publication bias associated with lowered α

The size/power tradeoff is not the only compromise associated with lowering α: in some situations, decreased α can increase the publication bias associated with using statistical significance tests as a filter for publication. Of course, (Benjamin et al. 2017) explicitly disavow using an NHST with lowered α as a necessary condition for publication; they say that “results that would currently be called ‘significant’ but do not meet the new threshold should instead be called ‘suggestive’” (p. 5). However, given the fifty year history of of requiring results to be statistically significant to be publishable (T. D. Sterling 1959; T. Sterling, Rosenbaum, and Winkam 1995), we must anticipate that this pattern could continue into the future.

Consider Figure 3, which shows two perspectives on how decreased α might impact publication bias. The left panel (Figure 3a) shows the percentage difference in magnitude between a true coefficient β = 3 and the average statistically significant coefficient using an NHST with various values of α.2 The figure shows that decreased values of α increase the degree of publication bias; this occurs because stricter significance tests tend to reject only the largest estimates from a sampling distribution, as also shown in Figure 2. On the other hand, the right panel (Figure 3b) shows the percentage difference in magnitude from a true coefficient drawn from a spike-and-normal prior density of coefficients:

f(\beta) \sim 1(\beta=0)*0.5 + \phi(\mu=0, \sigma=3)*0.5

where there is a substantial (50%) chance of a null relationship being studied by a researcher; 1(\beta=0) is the indicator function for a null relationship.3 In this case, increasingly strict significance tests tend to decrease publication bias, because the effect of screening out null relationships (which are greatly overestimated by any false positive result) is stronger than the effect of estimating only a portion of the sampling distribution of non-null relationships (which drives the result in the left panel).


Adapting to a lowered α

If the proposal of (Benjamin et al. 2017) is simply to accept lowered power in exchange for lower false discovery rates, it is a difficult proposal to accept. First and foremost, assistant professors and graduate students must publish a lot of high-quality research in a short time frame and may be forced to leave the discipline if they cannot; higher standards that are an inconvenience to tenured faculty may be harmful to them unless standards for hiring and tenure adapt accordingly. In addition, even within a particular level of seniority, this reform may unlevel the playing field. Political scientists in areas that often observational data with essentially fixed N, such as International Relations, would be disproportionately affected by such a change: more historical data cannot be created in order to raise the power of a study. Among experimenters and survey researchers, those with smaller budgets would also be disproportionately affected: they cannot afford to simply buy larger samples to achieve the necessary power. Needless to say, the effect of this reform on the scientific ecosystem would be difficult to predict and not necessarily beneficial; at first glance, such a reform seems to benefit the most senior scholars and people at the wealthiest institutions.

However, I believe that acquiesence to lower power is not the only option. It may be difficult or impossible for researchers to collect larger N, but it is considerably easier for them to measure a larger number of variables of interest K from their extant samples. This creates the possibility that researchers can spend more time developing and enriching their theories so that these theories make multiple predictions. Testing these predictions jointly typically allows for much greater power than testing any single prediction alone, as long as any prediction is clearly laid out prior to analysis and all failed predictions are reported in order to avoid a multiple comparison problem (Sidak 1967; Abdi 2007); predictions must be specified in advance and failed predictions must be reported because simply testing numerous hypotheses and reporting any that were confirmed tends to generate an excess of false positive results.

When K-many statistically independent hypothesis tests are performed using a significance threshold of α and all must be passed in order to confirm a theory,4 the chance of simultaneously rejecting them all by chance is \tilde{\alpha} = \alpha^{K}. Fixing \tilde{\alpha} = 0.005, it is clear that increasing K allows the individual test’s α to be higher.5 Specifically, α must be equal to (\tilde{\alpha})^{1/K} in order to achieve the desired size. That means that two statistically independent hypothesis tests can have their individual α ≈ 0.07 in order to achieve a joint size of 0.005; this is a lower standard on the individual level than the current 0.05 convention. When k = 3, the individual α ≈ 0.17.

When will conducting a joint test of multiple hypotheses yield greater power than conducting a single test? If two hypothesis tests are statistically independent6 and conducted as part of a joint study, this will occur when:

P_{1}(\tilde{\alpha}) < P_{1}(\tilde{\alpha}^{1/2})P_{2}(\tilde{\alpha}^{1/2})          [1]

\frac{P_{1}(\tilde{\alpha})}{P_{1}(\tilde{\alpha}^{1/2})} < P_{2}(\tilde{\alpha}^{1/2})          [2]

P_{k}(a) = \tau_{k}(-t^\star(a)) + \left(1-\tau_{k}(t^\star(a)))\right)

Here, τk is the non-central cumulative t-density corresponding to the sampling distribution of βk, k ∈ {1, 2}; I presume that k is sorted so that tests are in descending order of power. t(a) is the positive critical tstatistic needed to create a single two-tailed hypothesis test of size a. The left hand side of equation (1) is the power of the single hypothesis test with the greatest power; the right hand side of equation (1) is the power of the joint test of two hypotheses. As equation (2) shows, the power of the joint test is larger when the proportional change in power for the test of β1 is less than the power for the test of β2. Whether this condition is met depends on many factors, including the magnitude and variability of β1 and β2.

To illustrate the potential for power gains, I numerically calculated the power of joint tests with size \tilde{\alpha} = 0.005 for the case of one, two, and three statistically independent individual tests. For this calculation, I assumed three relationships β = βk with equal magnitude and sign, k ∈ {1, 2, 3} with \sigma_{\hat{\beta}_k}=1; thus, each one of the three tests has identical power when conducted individually. I then calculated the power of each joint test \left(\tau_{k}(-t^\star(a)) + (1-\tau(t^\star((\tilde{\alpha})^{1/k})))\right)^k for each value of k and for varying values of β, where τ is the non-central cumulative t-density with non-centrality parameter equal to β. Note that, as before, I define t(a) as the critical t-statistic for a single two-tailed test with size a. The result is illustrated in Figure 4.


Figure 4 shows that joint hypothesis testing creates substantial gains in power over single hypothesis testing for most values of β. There is a small amount of power loss near the tails (where β ≈ 0 and β ≈ 6), but this is negligible.

Conclusion: the NHST with lowered α is an improvement, if we enrich our theories

There are reasons to be skeptical of the Benjamin et al. (2017) proposal to move the NHST threshold for statistical significance from α = 0.05 to α = 0.005. First, there is substantial potential for adverse effects on the scientific ecosystem: the proposal seems to advantage senior scholars at the most prominent institutions in fields that do not rely on fixed-N observational data. Second, the NHST with a reduced α is not my ideal approach to adjudicating which results are statistically meaningful; I believe it is more advantageous for political scientists to adopt a statistical decision theory-oriented approach to inference7 and give greater emphasis to cross-validation and out-of-sample prediction.

However, based on the evidence presented here and in related work, I believe that moving the threshold for statistical significance from α = 0.05 to α = 0.005 would benefit political science if we adapt to this reform by developing richer, more robust theories that admit multiple predictions. Such a reform would reduce the false discovery rate without reducing power or unduly disadvantaging underfunded scholars or subfields that rely on historical observational data, even if meeting the stricter standard for significance became a necessary condition for publication. It would also force us to focus on improving our body of theory; our extant theories lead us to propose hypotheses that are wrong as much as 90% of the time (V. E. Johnson et al. 2017; Esarey and Liu 2017). Software that automates the calculation of appropriate critical t-statistics for correlated joint hypothesis tests would make it easier for substantive researchers to make this change, and ought to be developed in future work. This software has already been created for joint tests involving interaction terms in generalized linear models by Esarey and Sumner (2017), but the procedure needs to be adapted for the more general case of any type of joint hypothesis test.


Abdi, Herve. 2007. “The Bonferonni and Sidak Corrections for Multiple Comparisons.” In Encyclopedia of Measurement and Statistics, edited by Neil Salkind. Thousand Oaks, CA: Sage. URL: accessed 8/5/2017.

Benjamin, Daniel J., James O. Berger, Magnus Johannesson, Brian A. Nosek, E. J. Wagenmakers, Richard Berk, Kenneth A. Bollen, et al. 2017. “Redefine Statistical Significance.” Nature Human Behavior Forthcoming: 1–18. URL: accessed 7/31/2017.

Benjamini, Y., and Y. Hochberg. 1995. “Controlling the false discovery rate: a practical and powerful approach to multiple testing.” Journal of the Royal Statistical Society. Series B (Methodological) 57 (1). JSTOR: 289–300. URL:

Esarey, Justin, and Nathan Danneman. 2015. “A Quantitative Method for Substantive Robustness Assessment.” Political Science Research and Methods 3 (1). Cambridge University Press: 95–111.

Esarey, Justin, and Vera Liu. 2017. “A Prospective Test for Replicability and a Retrospective Analysis of Theoretical Prediction Strength in the Social Sciences.” Poster presented at the 2017 Texas Methods Meeting at the University of Houston.  URL: accessed 8/1/2017.

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Replication file

The code to replicate Figures 2-4 is available at Figure 1 is a reprint of a figure originally published in Esarey and Wu; the replication file for that publication is available at

  1. I thank Jeff Grim, Martin Kavka, Tim Salmon, and Mike Ward for helpful comments on a previous draft of this paper, particularly in regard to the effect of lowered α on junior scholars and the question of whether statistical significance should be required for publication.
  2. Specifically, I measure E[(\hat{\beta} - 3) / 3], where \hat{\beta} is a statistically significant estimate.
  3. Here, I measure E[(\hat{\beta} - \beta) / \mu_{beta}], where μβ is the mean of f(β).
  4. The points in this paragraph are similar to those made by Esarey and Sumner (2017, pp. 15–19).
  5. For statistically correlated tests, the degree to which \alpha > \tilde{\alpha} is smaller; at the limit where all the hypothesis tests are perfectly correlated, \alpha = \tilde{\alpha}.
  6. Correlated significance tests require the creation of a joint distribution τ on the right hand side of equation ([eq:power-gain-line-one]) and the determination of a critical value t such that \int_{t^\star}^{\infty} \int_{t^\star}^{\infty} \tau(t_1, t_2) dt_{1} dt_{2} = \tilde{\alpha}; while practically important, this analysis is not as demonstratively illuminating as the case of statistically independent tests.
  7. In a paper with Nathan Danneman (2015), I show that a simple, standardized approach could reduce the rate of false positives without harming our power to detect true positives (see Figure 4 in that paper). Failing this, I would prefer a statistical significance decision explicitly tied to expected replicability, which requires information about researchers’ propensity to test null hypotheses as well as their bias toward positive findings (Esarey and Liu 2017). These changes would increase the complexity and the number of researcher assumptions of a statistical assessment procedure relative to the NHST, but not (in my opinion) to a substantial degree.
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