Hostname: page-component-78c5997874-8bhkd Total loading time: 0 Render date: 2024-11-05T02:00:27.478Z Has data issue: false hasContentIssue false

More than meets the ITT: A guide for anticipating and investigating nonsignificant results in survey experiments

Published online by Cambridge University Press:  19 February 2024

John V. Kane*
Affiliation:
New York University, New York, NY, USA
Rights & Permissions [Opens in a new window]

Abstract

Survey experiments often yield intention-to-treat effects that are either statistically and/or practically “non-significant.” There has been a commendable shift toward publishing such results, either to avoid the “file drawer problem” and/or to encourage studies that conclude in favor of the null hypothesis. But how can researchers more confidently adjudicate between true, versus erroneous, nonsignificant results? Guidance on this critically important question has yet to be synthesized into a single, comprehensive text. The present essay therefore highlights seven “alternative explanations” that can lead to (erroneous) nonsignificant findings. It details how researchers can more rigorously anticipate and investigate these alternative explanations in the design and analysis stages of their studies, and also offers recommendations for subsequent studies. Researchers are thus provided with a set of strategies for better designing their experiments, and more thoroughly investigating their survey-experimental data, before concluding that a given result is indicative of “no significant effect.”

Type
Research Article
Creative Commons
Creative Common License - CCCreative Common License - BY
This is an Open Access article, distributed under the terms of the Creative Commons Attribution licence (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted re-use, distribution and reproduction, provided the original article is properly cited.
Copyright
© The Author(s), 2024. Published by Cambridge University Press on behalf of American Political Science Association

Survey experiments are an increasingly popular method for testing whether particular types of information and stimuli can causally affect politically relevant beliefs, attitudes, and behaviors (e.g., Druckman and Green Reference Druckman and Green2021; Druckman Reference Druckman2022; Mutz Reference Mutz2011). However, little scholarship has attempted to concisely detail and address the various factors that can often undermine a researcher’s survey experiment – i.e., yield what appears to be a “non-significant” result (whether in the statistical and/or practical sense) despite a hypothesis actually being correct.

How can researchers be more confident that a nonsignificant result is actually indicative of “no effect” vis-à-vis a consequence of one or more of these undermining factors? An inability to address this crucial question stands to greatly diminish the theoretical and empirical value of one’s study. Thus, being able to rigorously investigate nonsignificant results is valuable, especially given the growing awareness of the “file drawer problem” within scholarly research (Alrababa’h et al. Reference Alrababa’h2022; Franco, Malhotra, and Simonovits Reference Franco, Malhotra and Simonovits2014), as well as greater scholarly appreciation for nonsignificant results that occur in well-designed experiments and/or studies that conclude in favor of the null hypothesis (see Chambers and Tzavella Reference Chambers and Tzavella2022; Journal of Experimental Political Science 2023; The Journal of Politics 2022; Nature 2023).

A typical survey experiment randomly assigns respondents to one of at least two conditions within a survey. The condition to which one is assigned represents one value of the independent variable, X. Researchers then statistically test whether values of X are significantly associated with the values of an outcome (Y) that is measured for all respondents. When conducted for the entire sample, researchers refer to this difference as an estimate of the intention-to-treat (ITT) effect (Gerber and Green Reference Gerber and Green2012, 142).Footnote 1

When is an ITT nonsignificant? Per the null hypothesis significance-testing (NHST) paradigm (e.g., see Gill Reference Gill1999), researchers fail to reject the null hypothesis – i.e., deem a result “not statistically significant” – when a p-value exceeds a particular threshold (e.g., α=0.05). Apart from its statistical significance, an estimated effect can also be so small as to be practically (or “substantively”) nonsignificant (Rainey Reference Rainey2014).

Suppose a researcher fields a survey experiment and the ITT is nonsignificant (i.e., not statistically discernible from zero and/or substantively negligible in size). The researcher may infer that the hypothesis being tested, and/or underlying theory, is incorrect. This is one explanation for the result. However, there exist alternative explanations (AEs) that researchers should consider before concluding a treatment to be truly nonsignificant. Even if one disregards significance-testing and focuses only on the range of likely effect sizes (e.g., confidence intervals or credible sets see Gill Reference Gill1999, 662–63; Rainey Reference Rainey2014), understanding these AEs is vital as they tend to lower the center of that range toward zero (i.e., toward practical nonsignificance). In short, the AEs identified here can undermine both hypothesis testing as well as point estimation of treatment effects, making it difficult for researchers to determine what can be learned from a nonsignificant result.

The key purpose of this essay, then, is to detail the variety of AEs that increase the likelihood of nonsignificant results in survey experiments. Knowledge of these AEs is relevant to researchers at two key stages of a research project: (1) when designing their survey experiments, and (2) when investigating the robustness of their nonsignificant findings after data collection. Ultimately, with this knowledge, researchers can minimize the threat of AEs before data are collected and better detect erroneously nonsignificant findings once data are in hand. In addition, researchers concluding in favor of a treatment having “no significant effect” can offer far more persuasive evidence by showing not only a nonsignificant ITT but also that these various AEs can be ruled out reasonably confidently.Footnote 2 , Footnote 3 Finally, this essay provides guidance for how researchers might design a subsequent study should they find evidence for one or more AEs in their initial study.

Importantly, the aim is not to provide experimentalists with more avenues to “find significant results,” raising the risk of Type I errors (“false positives”) in the process. To guard against this possibility, researchers should pre-register their studies and analysis plans, particularly the analyses they would conduct to detect and address the various AEs identified here (Blair et al. Reference Blair, Cooper, Coppock and Humphreys2019; Druckman Reference Druckman2022, 143–44; Nosek et al. Reference Nosek, Ebersole, DeHaven and Mellor2018).

This concern notwithstanding, given the great deal of effort that goes into designing and fielding a survey experiment, and the prevalence of obtaining “nonsignificant results,” knowledge of how to anticipate, investigate, and more confidently rule out these AEs can assist researchers in getting the most of out of their studies.

Seven alternative explanations (AEs) for nonsignificant results

Alternative explanation #1: Respondent inattentiveness

The more that a sample is inattentive to a treatment, the more that a treatment group’s experience resembles that of the control group. To the extent this occurs, we should expect a smaller difference in Y between the two groups. Because of respondent inattentiveness, therefore, a treatment effect (if one truly exists) will tend to be biased toward zero, making the ITT more difficult to precisely estimate, reliably detect, and attain statistical significance (given a particular sample size and level of α (Bailey Reference Bailey2021)). By the same logic, inattentiveness will increase the likelihood of observing a failed manipulation (see AE #2 below). In short, attentiveness is often a precondition for having an efficacious treatment.

Researchers should therefore plan to investigate inattentiveness in their sample. There exists a variety of ways to conduct such an investigation using specialized “checks.” Instructional manipulation checks (i.e., “screeners” Berinsky, Margolis, and Sances Reference Berinsky, Margolis and Sances2014; Oppenheimer, Meyvis, and Davidenko Reference Oppenheimer, Meyvis and Davidenko2009) and factual manipulation checks (Kane and Barabas Reference Kane and Barabas2019), for example, are questions with only one correct answer. The latter asks respondents about specific content that was manipulated across experimental conditions. Incorrect answers to such questions indicate insufficient respondent attentiveness. Overly fast response times (per question timers) are an additional method for gauging respondent inattentiveness.Footnote 4

Existing studies using these techniques find substantial rates of inattentiveness, with estimates often ranging from approximately 15% to 40% (e.g., see Aronow et al. Reference Aronow, Kalla, Orr and Ternovski2020; Kane and Barabas Reference Kane and Barabas2019). Importantly, there exists no agreed-upon acceptable level of inattentiveness in survey experiments. Such a level would depend greatly upon other aspects of the study (e.g., for NHST, sample size and treatment strength would also matter).Footnote 5 Nevertheless, the crucial point is that any amount of inattentiveness will tend to attenuate ITT estimates.

If substantial inattentiveness is found, what can be done? Researchers should first confirm whether treatment assignment substantially covaries with an item measuring attention to the treatment (Kane & Barabas Reference Kane and Barabas2019). This enables the researcher to more confidently conclude that respondents in one condition attended (on average) to different information than respondents in another condition – a crucial assumption of most survey experiments.Footnote 6

Researchers can also employ pre-treatment attention checks and use these to analyze how treatment effects differ across varying levels of attentiveness (Druckman Reference Druckman2022, 56). Such checks enable the researcher to test whether – as one would expect if a treatment is truly effective – treatment effects are substantially larger for subsamples that were more likely to have attended to the treatment, and without the risk of post-treatment bias (see Kane, Velez, and Barabas Reference Kane, Velez and Barabas2023).Footnote 7 , Footnote 8 Critically, researchers should avoid using any post-treatment measure of attentiveness to re-estimate treatment effects (e.g., dropping respondents who fail post-treatment attention checks, or (per a timer) rushed through an experimental vignette). This practice has been shown to risk undermining random assignment and inducing statistical bias (Aronow, Baron, and Pinson Reference Aronow, Baron and Pinson2019; Montgomery, Nyhan, and Torres Reference Montgomery, Nyhan and Torres2018; Varaine Reference Varaine2022).

Alternative explanation #2: Failure to vary the independent variable of interest

A second potential AE is that one’s independent variable was not actually varied by the treatment (Mutz and Pemantle Reference Mutz and Pemantle2015). For example, suppose that a researcher attempts to increase respondents’ belief that a military draft is likely to be reinstated (to study if it affects respondents’ support for war (Y)).Footnote 9 Whether the treatment actually accomplishes this objective is, of course, an empirical question.

The key recommendation is to include a classic manipulation check (Mutz Reference Mutz, James and Donald2021).Footnote 10 This is a survey item that (1) is asked after exposure to a control/treatment condition, and (2) measures the underlying construct that the researcher is attempting to manipulate. As in the above example, if a treatment is designed to make respondents perceive that a military draft is more likely, then the manipulation check should measure respondents’ perceived likelihood of a draft; if a treatment is designed to make respondents feel more anxious, the manipulation check should measure anxiety, etc.

Empirically, a researcher could then confirm that a treatment group significantly differs from the control group on this measure and, ideally, to a substantively large degree. When this occurs, it is additional evidence that the treatment accomplished what the researcher intended. It also indicates that, whatever the sample’s level of inattentiveness (see AE #1), it was not substantial enough to prevent the researcher from successfully manipulating the independent variable of interest.Footnote 11

As Mutz (Reference Mutz2011, 84–85) argues, instances in which researchers should consider such manipulation checks “optional” are “relatively few and far between.” Yet, in spite of their simplicity and enormous value, such manipulation checks remain remarkably under-utilized: well under 50% of published experimental studies in political science feature a manipulation check (Kane and Barabas Reference Kane and Barabas2019; Mutz Reference Mutz, James and Donald2021).

What if treatment assignment is not significantly associated with the manipulation check (i.e., the manipulation “failed”)? Here, there exist several possible explanations. First, it may be a result of the inattentiveness problem described above: if respondents are not attentive to the treatment, we should expect an attenuated effect on the manipulation check (just as we expect an attenuated effect on Y).

If attentiveness levels are reasonably high (and, ideally, treatment assignment is found to correlate with a measure of attention to the treatment), a second possibility is that the manipulation check measure is flawed with respect to either its validity and/or reliability. In other words, we need to be confident that the manipulation check is a reasonably valid measure of the independent variable we intend to manipulate and also that it is not an overly “noisy” measure. These concerns can be investigated by testing whether theoretically relevant variables (e.g., education, age, and political attitudes) significantly correlate with the manipulation check measure. That is, we can investigate the manipulation check’s criterion validity (e.g., Druckman Reference Druckman2022, 22–27). If substantial correlations are found, it suggests that the check is to some extent valid and reliable and, thus, should in principle be manipulable.

The third, more fundamental possibility is that the treatment is not actually manipulating what it is designed to manipulate. As an extreme example, imagine a single sentence of manipulated (i.e., treatment) material contained within several paragraphs of non-manipulated text, images, etc. Whatever this treatment might affect, its efficacy is potentially being overwhelmed and attenuated by the other information that respondents are being asked to process (e.g., see Mutz Reference Mutz2011, 58), even if this additional content is contextually relevant (see Brutger et al. Reference Brutger2023). In short, this treatment is not salient enough to induce variance in the independent variable. As a result, the treatment will not be significantly predictive of the manipulation check, nor is it likely, therefore, to predict Y (see Brophy and Mullinix Reference Brophy and Mullinix2023 for an applied example).

Being able to rule out one or more of these possibilities allows the researcher to better understand both their nonsignificant manipulation check result and, more broadly, their nonsignificant ITT result (see Supplemental Appendix C for additional details).

Like AE #1, this AE has important implications for the design stage of one’s study. In addition to including a manipulation check, researchers must think carefully about what one’s treatment actually involves, ideally pretesting alternative versions to determine which is most strongly associated with the manipulation check item (Chong and Junn Reference Chong, Junn, James, Donald, James and Lupia2011, 329–30; Mutz Reference Mutz2011, 65). Searles and Mattes (Reference Searles and Mattes2015), for example, test several anger-induction techniques in one sample and then, based on the manipulation check results, use the best-performing technique for their subsequent study.

Alternative explanation #3: Pre-treated respondents

A related AE is a “pre-treatment effect” (see Druckman and Leeper Reference Druckman and Leeper2012; Gaines, Kuklinski, and Quirk Reference Gaines, Kuklinski and Quirk2007). Specifically, a treatment may be efficacious, but perhaps respondents have been treated prior to the study, in the real world, with information similar to what the researcher is employing in the experiment.

For example, at the height of the COVID-19 pandemic, a survey experiment that randomly assigned respondents to read information that the coronavirus is dangerous to one’s health may have been thwarted by a pre-treatment effect: this information – though powerful – would have undoubtedly been absorbed by respondents prior to the experiment. Thus, the treatment may appear to have a nonsignificant effect on Y, not because the treatment is ineffective, but because it has already occurred. As Slothuus (Reference Slothuus2016, 303) writes of the effect of party cues, “paradoxically, experimenters will be most likely to find no relationship at the very time that the relationship is strongest outside the experimental context.” Indeed, pre-treatment will tend to bias treatment effects toward zero (see Gaines, Kuklinski, and Quirk Reference Gaines, Kuklinski and Quirk2007) and thus increase the likelihood of a nonsignificant result.Footnote 12

Importantly, a pre-treatment effect should therefore also tend to result in a failed manipulation check. In the presence of nonsignificant ITT estimates and a failed manipulation check, therefore, researchers should carefully consider their treatment vis-à-vis what respondents may have been already exposed to in the real world prior to the experiment.

Again, this has important implications for how researchers design their survey experiments. The likelihood of pre-treatment will, naturally, depend upon what the researcher employs as treatment stimuli. In contexts wherein a pre-treatment effect is more likely, researchers might err on the side of having a relatively stronger treatment to compensate for the attenuating effects of pre-treatment. This should provide a better test of the hypothesis insofar as the experimental treatment is more powerful than what respondents have already been exposed to (though it may potentially diminish the external validity of the stimulus (see Druckman Reference Druckman2022, Ch.3)). Additionally, researchers can include a (pre-treatment) survey question that gauges whether substantial pre-treatment has occurred (e.g., asking how closely one has been following a particular topic in the news), and then estimate the ITT among those who are less likely to have been pre-treated (e.g., see Linos and Twist Reference Linos and Twist2018). In the extreme case wherein all respondents are likely to have been heavily pre-treated, researchers might consider an alternative research design to test the hypothesis of interest or postpone the study until the threat of pre-treatment subsides.

Alternative explanation #4: Insufficient statistical power

Within the NHST paradigm, insufficient power is a well-established reason for statistically nonsignificant (i.e., “null”) results (Alrababa’h et al. Reference Alrababa’h2022). Nevertheless, political science research remains severely underpowered (Arel-Bundock et al. Reference Arel-Bundock2022). A small sample – given the number of experimental groups and anticipated magnitude of the treatment(s) – is a common means by which null results become more likely in survey experiments, even when a treatment truly has an effect. In the extreme case, too small a sample will yield null findings no matter how efficacious one’s treatment is (e.g., see Perugini, Gallucci, and Costantini Reference Perugini, Gallucci and Costantini2018).Footnote 13

The most direct approach for guarding against this AE is to have a sufficient sample size. When designing their survey experiment, researchers should conduct statistical power analyses, and assume the smallest substantively meaningful effect size, to determine an appropriate sample size for the study (Lakens Reference Lakens2022). In so doing, researchers should also be mindful of (1) the possibility of substantial inattentiveness (AE #1), (2) the number of experimental conditions, and (3) whether any subgroup analyses will be performed, adjusting their power analyses accordingly.Footnote 14 A sample size of 1000, for example, may seem sufficiently powered. However, if the experiment involves five conditions, and will involve subsetting the data on racial identification, for example, the researcher could ultimately be estimating treatment effects among only a few dozen respondents (and only a fraction of these respondents will have actually attended to the experiment).

Thus, while researchers may have limited control over the total sample size (e.g., because of resource constraints), greater discretion can be exercised over (1) the number of experimental conditions (and whether some of these conditions can potentially be “collapsed” together because of a common element between them), and (2) the degree to which any subgroup analyses are necessary for testing a particular hypothesis.

Further, researchers can also improve statistical power by employing “blocking” to ensure that the experimental groups are perfectly balanced on a key covariate (e.g., Bailey Reference Bailey2021, 346–49; Dolan Reference Dolan2023; see Mousa Reference Mousa2020 for an applied example). Power can also be improved (via increasing precision of a point estimate) by estimating the ITT while controlling/adjusting for prespecified covariates (in particular, significant predictors of the dependent variable (see Gerber et al. Reference Gerber2014; Mutz and Pemantle Reference Mutz and Pemantle2015)). Wuttke et al. (Reference Wuttke, Sichart and Foos2023) offer an applied example of this technique with survey-experimental data (see also Gerber et al. Reference Gerber2014). Finally, Clifford et al. (Reference Clifford, Sheagley and Piston2021) find that utilizing pre and posttreatment measures of Y yields similar ITT estimates to the more common between-subjects design, but with substantially greater precision and, thus, greater statistical power.

Alternative explanation #5: Poor measurement of the dependent variable

Another vexing alternative explanation is measurement error in the dependent variable (Y). Assuming one is using a valid measure of Y, greater noise in this measure will often raise the likelihood of a result that, per the NHST paradigm, is not statistically significant. Specifically, measurement error in Y is expected to increase the ITT’s standard error and thus increase the likelihood of null results when significance-testing (Bailey Reference Bailey2021, 148–50; Berry and Feldman Reference Berry and Feldman1985, 26–33). Yet measurement error in Y can potentially matter for point estimation as well. For example, per Clayton et al. (Reference Clayton2023), measurement error in the dependent variable within conjoint experiments can bias treatment-effect estimates downward toward zero.

When designing their study, researchers should consider including multiple indicators of Y and then combining them into a single measure (e.g., an additive scale). Doing so can substantially reduce Y’s degree of random measurement error (e.g., see Mousa Reference Mousa2020 for an applied example). This practice therefore offers a notable advantage over using only one indicator of Y (Ansolabehere, Rodden, and Snyder Reference Ansolabehere, Rodden and Snyder2008; Berry and Feldman Reference Berry and Feldman1985, 33–34). In addition, using measures of Y that have been previously validated (either in other studies or in pretests) is a wise strategy for having a dependent variable with the best signal-to-noise ratio possible.

Once data have been collected, researchers can investigate this AE by ensuring that other measures that should, theoretically, significantly correlate with Y actually do so. If substantial correlations are found, then the measure may be considered reasonably satisfactory, even if imperfect to some extent. This, of course, requires that, during the design stage, researchers include theoretically relevant covariates in their survey (pre-treatment). Existing literature provides detailed discussions of examining measurement properties of variables (Carmines and Zeller Reference Carmines and Zeller1979; Druckman Reference Druckman2022, 22–27). See Supplemental Appendix E for additional discussion.

Alternative explanation #6: Ceiling and floor effects

Related to concerns involving the measurement of Y, another well-known problem in experiments is that of either a “ceiling” or a “floor” effect (e.g., see Mullinix et al. Reference Mullinix, Leeper, Druckman and Freese2015, 116). A treatment may fail to produce a significant change in Y because values of Y in the control condition are already (on average) very high (a “ceiling effect”) or very low (a “floor effect”). This AE therefore restricts the substantive magnitude of the ITT estimate. Further, per NHST, this AE will tend to increase the p-value and thus the likelihood of a null result. As with all AEs, an inability to rule out this alternative explanation renders it more difficult to determine what a nonsignificant result indicates and, thus, more difficult to assess a study’s value.

In the analysis stage, one simple technique for investigating this AE is to obtain descriptive statistics (e.g., means, proportions, etc.) of Y in the control condition. Ideally, one wants to observe moderate values, or values in the direction opposite the effect of concern (e.g., low values if the concern is a ceiling effect), which would indicate that Y had “room” to significantly change. Brierly and Pereira (Reference Brierley and Pereira2023, endnote 9), for example, cite their outcome variable’s mean being substantially below the highest value as evidence that “ceiling effects cannot explain the [nonsignificant] result.” Though somewhat uncommon in survey experiments, accounting for this AE (specifically, right- and/or left-censoring of Y) can take the form of specifying a Tobit regression model (Muthén Reference Muthén1989; see Bechtel and Scheve Reference Bechtel and Scheve2017 for an applied example).

In the design stage, there are several proactive strategies that can be employed. First, researchers should focus on preventing ceiling/floor effects that are artifactual – i.e., arising from the measure itself, rather than what is theoretically possible. To guard against this, researchers can feature survey measures of Y that will not have extreme means. In other words, researchers can utilize measures with a more (conceptually) extreme and/or less coarse range of response options. As Vanderweedt (Reference Vandeweerdt2022, 833) writes of their nonsignificant findings, “effects…might have been clearer with more nuanced (less compressed) attitude response scales.” Employing multiple measures of Y can often assist toward this end as it is unlikely that respondents will have an extreme value on every survey item comprising the scale. Researchers can also examine means of measures that have been featured in publicly available data to help ensure, a priori, that such measures will not induce ceiling/floor effects if used in their own survey experiments.

Alternative explanation #7: Countervailing treatment effects

Finally, a treatment may of course have substantially different-sized (i.e., heterogeneous) effects among different subgroups within the sample (e.g., Kam and Trussler Reference Kam and Trussler2017). Thus, a possible explanation for nonsignificant results is that one has a special case of heterogeneous effects wherein an overall ITT can be near zero because treatment effects occur in opposite directions for different subgroups.

Consider an example in which our treatment (X) is whether or not a U.S. political candidate adopts a stance opposing access to abortion, and our outcome (Y) is the perceived favorability of the candidate. Given Republicans’ (Democrats’) generally anti-abortion (pro-choice) views, we should expect the treatment to increase Y among Republicans but decrease Y among Democrats. Thus, if we fail to account for partisanship and simply estimate the ITT for the whole sample, the ITT may be extremely small. Again, this would not be because the treatment was inefficacious; rather, it is because the effect occurred in opposite directions for large subsets of the sample. We might therefore refer to this as a problem of countervailing effects.

One strategy for investigating this AE in the analysis stage (assuming the source of potential heterogeneity is unknown) would be to compare variances of Y across treatment and control groups. This can be done visually using overlaid histograms of Y over values of X, or statistically with tests of equivalent standard deviations of Y over values of X (see Bryk and Raudenbush Reference Bryk and Raudenbush1988 and Ding, Feller, and Miratrix Reference Ding, Feller and Miratrix2016). Continuing with the above example, we should observe that the variance of candidate favorability in the treatment condition is substantially larger than in the control condition, suggesting that our treatment pushed subgroups in opposite directions. As Bryk and Raudenbush (Reference Bryk and Raudenbush1988, 396) contend, “To ignore variance heterogeneity…is tantamount to interpreting main effects while concealing significant interaction effects.” Coppock et al. (Reference Coppock, Hill and Vavreck2020, Appendix C) offer additional techniques for estimating the variance of effect sizes and formally testing for treatment-effect homogeneity.

Discovering heterogeneity in treatment effects naturally raises the question of where this heterogeneity is coming from. But when investigating this, ideally, researchers should theorize about such heterogeneous effects a priori (in the design stage). A measure of the theorized moderating variable (M) can then be included in the survey (pre-treatment), enabling researchers to identify the source of countervailing effects by exploring how the ITT estimate varies across M (e.g., via specifying an interaction in a regression model).Footnote 15

Crucially, researchers should exercise great caution here because, with enough exploration of interactions, one is bound to find some statistically significant (yet spurious) interactive effect. Again, testing for heterogeneous effects should be theorized – and pre-registered – before data are collected. Further, researchers should first report the ITT as a matter of transparency and also explicitly state whether any countervailing effect (if discovered) was an exploratory – rather than hypothesized – finding.

Discussion & conclusion

Survey experiments can and do yield nonsignificant ITTs, often much to the chagrin of researchers and, in some cases, potentially resulting in abandonment of the project (i.e., the “file drawer” problem). In other cases, researchers may point to a nonsignificant ITT as evidence that X has no causal effect upon Y. Yet while the lack of a true causal effect represents one explanation for a nonsignificant result, this essay stresses that there exist at least seven AEs for nonsignificant findings in survey experiments.

The purpose of this essay is to assist researchers with more thoroughly anticipating and investigating these AEs. Failure to do so means that one (or more) of the aforementioned AEs cannot be confidently ruled out, leaving open the possibility that a nonsignificant result is due to an AE rather than being indicative of no actual effect. Toward this end, Table 1 provides recommendations that researchers can implement in the design stage of their experiment (see second column) that will help (1) guard against, and (2) allow for investigation of, each of the seven AEs.

Table 1. Design recommendations & a checklist of potential alternative explanations for nonsignificant results

Note: Within the “Checklist” column, if “No” is answered for any AE, it suggests that a nonsignificant ITT may not be entirely due to an incorrect hypothesis or theory. Note there is debate regarding the utility of post-hoc power analysis (see Perugini, Gallucci, and Costantini Reference Perugini, Gallucci and Costantini2018). The final column discusses possibilities for follow-up study assuming all procedures in “Recommended Practices in Design Stage” column were followed.

Table 1 also provides a simple checklist that can be employed during the analysis stage (see third column). If the researcher has sufficient reason to answer “No” to any of the questions in this checklist, an AE cannot be confidently ruled out, and thus an incorrect hypothesis (or theory) might not be the reason for a nonsignificant result. Alternatively, when a researcher can confidently answer “Yes” to each item in the checklist, they should more strongly suspect that X has no meaningful effect on Y.

As illustrated above, it is not wholly uncommon for survey experimentalists to report investigating some limited number of AEs. Wuttke et al. (Reference Wuttke, Sichart and Foos2023), notably, report investigating inattentiveness (AE#1), manipulation of the independent variable (AE#2), and ceiling effects (AE#6). At present, however, the degree to which researchers habitually consider each one of these AEs – either in the analysis or design stages – remains unclear.

This raises an additional point: experiments can be beset by multiple AEs. For example, Haas and Khadka (Reference Haas and Khadka2020, 995) fielded a study in which a nonsignificant finding could be attributable to a pre-treatment effect (AE #3) or to a ceiling effect (AE #6). Thus, researchers must be mindful of the distinct pathways by which experimental hypothesis tests can be undermined, and how to both proactively and retroactively address them. On this point, the final column of Table 1 provides recommendations for researchers who wish to field a subsequent study after (1) discovering evidence for one or more AEs in their initial study, and (2) being unable to confidently determine the extent to which a nonsignificant finding is attributable to a particular AE. These latter recommendations are therefore designed to help researchers conduct an improved test of their hypothesis based on the AE(s) discovered in their first study (see Supplemental Appendix G for further elaboration).

Notably, this essay has focused on how these AEs apply to survey experiments. Yet, while inattentiveness (AE#1) may be most relevant to survey experiments, each of the other AEs can be problematic for other types of experiments. For example, field experiments may fail to manipulate the independent variable (AE#2), while lab-based experiments may suffer from insufficient statistical power (AE#4).

In sum, the value of one’s study is undermined when there exist competing explanations for the same nonsignificant result. Importantly, preventing AEs is likely far more tractable than attempting to “correct for” them ex post. Thus, by becoming aware of these AEs, researchers can design their studies to be better safeguarded against, and (consequently) better equipped to investigate, them once results are in-hand. This stands to enable researchers to learn far more from their survey experiments than what a naïve, nonsignificant ITT alone can provide.

Supplementary material

The supplementary material for this article can be found at https://doi.org/10.1017/XPS.2024.1

Acknowledgements

I would like to express immense gratitude to Jamie Druckman, Carlisle Rainey, Yamil R. Velez, Jason Barabas, Brendan Nyhan, Daniel Lakens, Charles Crabtree, Yusaku Horiuchi, and the Dartmouth Department of Government for providing extremely thoughtful feedback on early drafts of this manuscript. In addition, the four anonymous reviewers and JEPS Editors provided truly invaluable guidance on ways to improve the manuscript’s clarity, contribution, and usefulness to researchers. I am deeply thankful for their efforts.

Competing interests

The author declares that there were no conflicts of interest in this study.

Ethics statement

Approval from an Institutional Review Board was not needed as this study did not contain any collection or analysis of original data.

Footnotes

1 The ITT differs from the commonly-employed average treatment effect (ATE) insofar as the latter implicitly assumes full compliance (Harden et al. Reference Harden, Sokhey and Runge2019, 200).

2 Naturally, as this involves somewhat subjective determinations, motivated reasoning is a potential concern (e.g., in deciding whether a particular piece of evidence permits “a reasonable degree of confidence”). Nevertheless, ceteris paribus, being able to present more evidence in favor of a nonsignificant ITT is preferable to presenting less.

3 It is worth emphasizing a common criticism of the NHST paradigm, which is that meaningfully large ITT estimates are often dismissed as “null” because the p-value was not below α. In other words, the null hypothesis is “accepted” rather than merely “not rejected” (Gill Reference Gill1999; see also Hartman and Hidalgo Reference Hartman and Daniel Hidalgo2018). To more persuasively argue that there is no meaningful effect, one would ideally want to show a negligibly-sized ITT that is precisely estimated and/or (using a two one-sided test approach) that an ITT is smaller than – and statistically distinguishable from – the smallest substantively meaningful effect (e.g., see Rainey Reference Rainey2014).

4 See the Supplemental Appendix A for extended discussion of attentiveness measures.

5 These aspects can also matter in different ways. A larger sample and/or fewer conditions may still permit the detection of statistically significant effects even in the presence of high inattentiveness – however, the inattentiveness is still likely to bias the ITT downward.

6 Importantly, this type of analysis is not possible for other attention check types, the answers to which do not depend upon treatment assignment.

7 Researchers should report the extent to which the attentive subsample compositionally differs from the original sample.

8 See Supplemental Appendix B for additional discussion.

9 This example comes from Horwitz and Levendusky (Reference Horowitz and Levendusky2011).

10 Kane and Barabas (Reference Kane and Barabas2019) specifically refer to these as subjective manipulation checks as there are no correct/incorrect answers (unlike other types of manipulation checks).

11 Crucially, this kind of manipulation check assumes – rather than tests for – sufficient attentiveness. Thus, researchers can also conduct this check across different levels of attentiveness (measured pre-treatment) to determine whether the treatment significantly predicts manipulation check responses among the most attentive.

12 Notably, however, Linos and Twist (Reference Linos and Twist2018) find that pre-treatment can lead to overestimation of an effect when a treatment runs counter to information absorbed prior to the experiment.

13 Of course, small samples matter for point estimation of effect sizes as well, with smaller samples yielding a wider variance of ITT estimates.

14 In general, a priori power analysis is more informative than post-hoc, though the latter can help determine whether n was sufficient given the observed ITT, pooled SD of Y, and (predetermined) desired level of power (Perugini, Gallucci, and Costantini Reference Perugini, Gallucci and Costantini2018). See Supplemental Appendix D for additional guidance.

15 See Hainmueller et al. (Reference Hainmueller, Mummolo and Xu2019) for excellent guidance on specifying interaction models.

References

Alrababa’h, Ala’ et al. 2022. “Learning from Null Effects: A Bottom-Up Approach.” Political Analysis 31(3): 448–56.CrossRefGoogle Scholar
Ansolabehere, Stephen, Rodden, Jonathan, and Snyder, James M. Jr. 2008. “The Strength of Issues: Using Multiple Measures to Gauge Preference Stability, Ideological Constraint, and Issue Voting.” American Political Science Review 102(02): 215–32.CrossRefGoogle Scholar
Arel-Bundock, Vincent et al. 2022. Quantitative Political Science Research Is Greatly Underpowered. I4R Discussion Paper Series. Working Paper. https://www.econstor.eu/handle/10419/265531 (May 18, 2023).CrossRefGoogle Scholar
Aronow, P. M., Kalla, Joshua, Orr, Lilla, and Ternovski, John. 2020. “Evidence of Rising Rates of Inattentiveness on Lucid in 2020.” https://osf.io/preprints/socarxiv/8sbe4/ (December 29, 2022).CrossRefGoogle Scholar
Aronow, Peter M., Baron, Jonathon, and Pinson, Lauren. 2019. “A Note on Dropping Experimental Subjects Who Fail a Manipulation Check.” Political Analysis 27(4): 572–89.CrossRefGoogle Scholar
Bailey, Michael A. 2021. Real Stats: Using Econometrics for Political Science and Public Policy. 2nd ed. New York, NY: Oxford University Press. https://www.amazon.com/Real-Stats-Econometrics-Political-Science/dp/0190859547 (December 5, 2022).Google Scholar
Bechtel, Michael M., and Scheve, Kenneth F.. 2017. “Who Cooperates? Reciprocity and the Causal Effect of Expected Cooperation in Representative Samples.” Journal of Experimental Political Science 4(3): 206–28.CrossRefGoogle Scholar
Berinsky, Adam J., Margolis, Michele F., and Sances, Michael W.. 2014. “Separating the Shirkers from the Workers? Making Sure Respondents Pay Attention on Self-Administered Surveys.” American Journal of Political Science 58(3): 739–53.CrossRefGoogle Scholar
Berry, William D., and Feldman, Stanley. 1985. Multiple Regression in Practice. Newbury Park, CA: SAGE Publications.CrossRefGoogle Scholar
Blair, Graeme, Cooper, Jasper, Coppock, Alexander, and Humphreys, Macartan. 2019. “Declaring and Diagnosing Research Designs.” The American Political Science Review 113(3): 838–59.CrossRefGoogle ScholarPubMed
Brierley, Sarah, and Pereira, Miguel M.. 2023. “Women Bureaucrats and Petty Corruption. Experimental Evidence from Ghana.” Research & Politics 10(1): 17.CrossRefGoogle Scholar
Brophy, Nathan, and Mullinix, Kevin J.. 2023. “Partisan Motivated Empathy and Policy Attitudes.” Political Behavior. https://doi.org/10.1007/s11109-023-09890-x.CrossRefGoogle Scholar
Brutger, Ryan et al. 2023. “Abstraction and Detail in Experimental Design.” American Journal of Political Science 67(4): 979–95.CrossRefGoogle Scholar
Bryk, Anthony S., and Raudenbush, Stephen W.. 1988. “Heterogeneity of Variance in Experimental Studies: A Challenge to Conventional Interpretations.” Psychological Bulletin 104(3): 396404.CrossRefGoogle Scholar
Carmines, Edward G., and Zeller, Richard A.. 1979. Reliability and Validity Assessment. Beverly Hills, CA: SAGE Publications.CrossRefGoogle Scholar
Chambers, Christopher D., and Tzavella, Loukia. 2022. “The Past, Present and Future of Registered Reports.” Nature Human Behaviour 6(1): 2942.CrossRefGoogle ScholarPubMed
Chong, Dennis, and Junn, Jane. 2011. “Politics from the Perspective of Minority Populations.” In Cambridge Handbook of Experimental Political Science, ed. James, N. Druckman, Donald, P. Greene, James, H. Kuklinski and Lupia, Arthur. Cambridge University Press, 320–35.CrossRefGoogle Scholar
Clayton, Katherine et al. 2023. “Correcting Measurement Error Bias in Conjoint Survey Experiments.” https://gking.harvard.edu/sites/scholar.harvard.edu/files/gking/files/conerr.pdf.Google Scholar
Clifford, Scott, Sheagley, Geoffrey, and Piston, Spencer. 2021. “Increasing Precision without Altering Treatment Effects: Repeated Measures Designs in Survey Experiments.” American Political Science Review 115(3): 1048–65.CrossRefGoogle Scholar
Coppock, Alexander, Hill, Seth J., and Vavreck, Lynn. 2020. “The Small Effects of Political Advertising Are Small Regardless of Context, Message, Sender, or Receiver: Evidence from 59 Real-Time Randomized Experiments.” Science Advances 6(36): eabc4046.CrossRefGoogle ScholarPubMed
Ding, Peng, Feller, Avi, and Miratrix, Luke. 2016. “Randomization Inference for Treatment Effect Variation.” Journal of the Royal Statistical Society Series B: Statistical Methodology 78(3): 655–71.CrossRefGoogle Scholar
Dolan, Lindsay. 2023. “10 Things to Know About Randomization.” EGAP. https://egap.org/resource/10-things-to-know-about-randomization/ (January 2, 2023).Google Scholar
Druckman, James, and Green, Donald P.. 2021. Advances in Experimental Political Science. New York: Cambridge University Press.CrossRefGoogle Scholar
Druckman, James N. 2022. Experimental Thinking: A Primer on Social Science Experiments. New York, NY: Cambridge University Press. ∼https://faculty.wcas.northwestern.edu/∼jnd260/pub/Druckman%20Experimental%20Thinking%20Fall%202020%20Submitted.pdf.CrossRefGoogle Scholar
Druckman, James N., and Leeper, Thomas J.. 2012. “Learning More from Political Communication Experiments: Pretreatment and Its Effects.” American Journal of Political Science 56(4): 875–96.CrossRefGoogle Scholar
Franco, Annie, Malhotra, Neil, and Simonovits, Gabor. 2014. “Publication Bias in the Social Sciences: Unlocking the File Drawer.” Science 345(6203): 1502–5.CrossRefGoogle ScholarPubMed
Gaines, Brian J., Kuklinski, James H., and Quirk, Paul J.. 2007. “The Logic of the Survey Experiment Reexamined.” Political Analysis 15(1): 120.CrossRefGoogle Scholar
Gerber, Alan et al. 2014. “Reporting Guidelines for Experimental Research: A Report from the Experimental Research Section Standards Committee.” Journal of Experimental Political Science 1(1): 8198.CrossRefGoogle Scholar
Gerber, Alan S., and Green, Donald P.. 2012. Field Experiments: Design, Analysis, and Interpretation. New York: W. W. Norton & Company.Google Scholar
Gill, Jeff. 1999. “The Insignificance of Null Hypothesis Significance Testing.” Political Research Quarterly 52(3): 647–74.CrossRefGoogle Scholar
Haas, Nicholas, and Khadka, Prabin B.. 2020. “If They Endorse It, I Can’t Trust It: How Outgroup Leader Endorsements Undercut Public Support for Civil War Peace Settlements.” American Journal of Political Science 64(4): 9821000.CrossRefGoogle Scholar
Hainmueller, Jens, Mummolo, Jonathan, and Xu, Yiqing. 2019. “How Much Should We Trust Estimates from Multiplicative Interaction Models? Simple Tools to Improve Empirical Practice.” Political Analysis 27(2): 163–92.CrossRefGoogle Scholar
Harden, Jeffrey J., Sokhey, Anand E., and Runge, Katherine L.. 2019. “Accounting for Noncompliance in Survey Experiments.” Journal of Experimental Political Science 6(3): 199202.CrossRefGoogle Scholar
Hartman, Erin, and Daniel Hidalgo, F.. 2018. “An Equivalence Approach to Balance and Placebo Tests.” American Journal of Political Science 62(4): 10001013.CrossRefGoogle Scholar
Horowitz, Michael C., and Levendusky, Matthew S.. 2011. “Drafting Support for War: Conscription and Mass Support for Warfare.” The Journal of Politics 73(02): 524–34.CrossRefGoogle Scholar
“Journal of Experimental Political Science.” 2023. Cambridge Core. https://www.cambridge.org/core/journals/journal-of-experimental-political-science/information/about-this-journal (January 2, 2023).Google Scholar
Kam, Cindy D., and Trussler, Marc J.. 2017. “At the Nexus of Observational and Experimental Research: Theory, Specification, and Analysis of Experiments with Heterogeneous Treatment Effects.” Political Behavior 39(4): 789815.CrossRefGoogle Scholar
Kane, John V., and Barabas, Jason. 2019. “No Harm in Checking: Using Factual Manipulation Checks to Assess Attentiveness in Experiments.” American Journal of Political Science 63(1): 234–49.CrossRefGoogle Scholar
Kane, John V., Velez, Yamil R., and Barabas, Jason. 2023. “Analyze the Attentive and Bypass Bias: Mock Vignette Checks in Survey Experiments.” Political Science Research and Methods 11(2): 293310.CrossRefGoogle Scholar
Linos, Katerina, and Twist, Kimberly. 2018. “Diverse Pre-Treatment Effects in Survey Experiments.” Journal of Experimental Political Science 5(2): 148–58.CrossRefGoogle Scholar
Montgomery, Jacob M., Nyhan, Brendan, and Torres, Michelle. 2018. “How Conditioning on Post-Treatment Variables Can Ruin Your Experiment and What to Do about It.” American Journal of Political Science 62(3): 760–75.CrossRefGoogle Scholar
Mousa, Salma. 2020. “Building Social Cohesion between Christians and Muslims through Soccer in Post-ISIS Iraq | Science.” Science 369(6505): 866–70.CrossRefGoogle ScholarPubMed
Mullinix, Kevin J., Leeper, Thomas J., Druckman, James N., and Freese, Jeremy. 2015. “The Generalizability of Survey Experiments.” Journal of Experimental Political Science 2(02): 109–38.CrossRefGoogle Scholar
Muthén, Bengt O. 1989. “Tobit Factor Analysis.” British Journal of Mathematical and Statistical Psychology 42(2): 241–50.CrossRefGoogle Scholar
Mutz, Diana C. 2011. Population-Based Survey Experiments. Princeton: Princeton University Press.Google Scholar
Mutz, Diana C. 2021. “Improving Experimental Treatments in Political Science.” In Advances in Experimental Political Science, ed. James, N. Druckman and Donald, P. Green. Cambridge University Press, 219–38.CrossRefGoogle Scholar
Mutz, Diana C., and Pemantle, Robin. 2015. “Standards for Experimental Research: Encouraging a Better Understanding of Experimental Methods.” Journal of Experimental Political Science 2(02): 192215.CrossRefGoogle Scholar
Nature. 2023. “Nature Welcomes Registered Reports.” Nature. https://www.nature.com/articles/d41586-023-00506-2 (May 17, 2023).Google Scholar
Nosek, Brian A., Ebersole, Charles R., DeHaven, Alexander C., and Mellor, David T.. 2018. “The Preregistration Revolution.” Proceedings of the National Academy of Sciences 115(11): 2600–06.CrossRefGoogle ScholarPubMed
Oppenheimer, Daniel M., Meyvis, Tom, and Davidenko, Nicolas. 2009. “Instructional Manipulation Checks: Detecting Satisficing to Increase Statistical Power.” Journal of Experimental Social Psychology 45(4): 867–72.CrossRefGoogle Scholar
Perugini, Marco, Gallucci, Marcello, and Costantini, Giulio. 2018. “A Practical Primer To Power Analysis for Simple Experimental Designs.” International Review of Social Psychology 31(1): 20.CrossRefGoogle Scholar
Rainey, Carlisle. 2014. “Arguing for a Negligible Effect.” American Journal of Political Science 58(4): 1083–91.CrossRefGoogle Scholar
Searles, Kathleen, and Mattes, Kyle. 2015. “It’s a Mad, Mad World: Using Emotion Inductions in a Survey.” Journal of Experimental Political Science 2(2): 172–82.CrossRefGoogle Scholar
Slothuus, Rune. 2016. “Assessing the Influence of Political Parties on Public Opinion: The Challenge from Pretreatment Effects.” Political Communication 33(2): 302–27.CrossRefGoogle Scholar
“The Journal of Politics: Registered Report Guidelines.” 2022. The Journal of Politics. https://www.journals.uchicago.edu/journals/jop/registered-report-guidelines?doi=10.1086%2Fjop&publicationCode=jop (January 2, 2023).Google Scholar
Vandeweerdt, Clara. 2022. “In-Group Interest Cues Do Not Change Issue Attitudes.” Politics, Groups, and Identities 10(5): 828–36.CrossRefGoogle Scholar
Varaine, Simon. 2023. “How Dropping Subjects Who Failed Manipulation Checks Can Bias Your Results: An Illustrative Case.” Journal of Experimental Political Science 10(2): 299305.CrossRefGoogle Scholar
Wuttke, Alexander, Sichart, Florian, and Foos, Florian. 2023. “Null Effects of Pro-Democracy Speeches by U.S. Republicans in the Aftermath of January 6th.” Journal of Experimental Political Science: 115. https://doi.org/10.1017/XPS.2023.17.CrossRefGoogle Scholar
Figure 0

Table 1. Design recommendations & a checklist of potential alternative explanations for nonsignificant results

Supplementary material: File

Kane supplementary material

Kane supplementary material
Download Kane supplementary material(File)
File 77.2 KB