Power struggles

Abstract

Conducting research on human relationships entails special challenges of design and analysis. Many important questions benefit from the study of dyads and families, and studies of relationships in natural settings often involve longitudinal and/or clustered designs. In turn, power analyses for such studies require additional considerations, because multilevel statistical models (or structural equation modeling equivalents) are often used to analyze relationships data. Power calculations in multilevel models involve the difficult task of specifying hypothesized values for a large number of parameters. Planning studies can also involve power trade-offs, including whether to prioritize the number of dyads sampled or the number of repeated measurements per dyad. Unfortunately, the relationships literature provides limited guidance on how to deal with these issues. In this article, we present a data simulation method for estimating power for commonly used relationships research designs. We also illustrate the method using two worked examples from relationships research.

Keywords

Close relationships dyadic data analysis multilevel modeling power analysis

Conducting research on close relationships brings with it many challenges that make data collection more difficult, time-consuming, and financially costly than many other topics within psychology. Studies frequently require substantial coordination between members of a large research team, as well as with the participants they wish to recruit and retain. Such coordination often involves repeated assessments of multiple relationship partners over periods of time that can stretch months and even years and may involve data collection during critical life stages such as marriage, childbirth, and death or dying. As a result, the stakes are high to successfully observe a hypothesized effect (if one actually exists in the population).

In the contemporary relationships literature, “successful” observation of a hypothesized effect generally means that one or more corresponding parameter estimates is statistically significant for some sample of data. However, in collecting samples from the population, we acknowledge the existence of sampling variability, which means that even if our effect exists, there is always some nonzero probability that we will fail to observe it in a single random sample (i.e., Type II error). The purpose of this article is to provide tools and suggestions for maximizing the chance that an existing hypothesized effect will be detected.¹ These tools are together referred to as power analysis (Cohen, 1962).

The concept of power is not new, but only recently have most relationships researchers begun to consider seriously the implications of statistically underpowered research (Bolger & Laurenceau, 2013; Finkel, Eastwick, & Reis, 2015). Moreover, even as a priori power analysis has risen in methodological prominence, sufficient tools and training to conduct such analyses for complicated relationships research have generally not followed. In the few cases where such tools do exist, virtually no previous work has provided guidance for the complex issue of determining reasonable parameter estimates for all but the most basic models or direct replications.

To address this critical gap, the current article offers a flexible procedure for conducting power analyses for relationships research. We focus on longitudinal and dyadic models, but the method can be extended to virtually any other empirical design. In order to contextualize this process, we introduce a substantive example from the relationships literature in which a researcher is interested in replicating and extending a previously reported finding. We consider four questions that are likely to arise when designing a study to test a hypothesized effect. Importantly, this includes being confident in the results regardless of whether the hypothesis is supported. These questions are as follows:

Q1: What information do I need to conduct a power analysis for a proposed study involving multiple individuals within dyads or families, at single or multiple time points?

Q2: How do I conduct a power analysis once I have collected the necessary information?

Q3: What factors are likely to have the strongest effect on power?

Q4: What if I do not have all of the information that I need?

After introducing our illustrative example, we provide a largely conceptual definition and discussion of power, with emphasis on the individual parameters that affect its calculation in between-subject (e.g., cross-sectional) designs. Importantly, we extend this description to illustrate how power calculations are complicated by designs that also vary within subjects (e.g., time intensive or dyadic). We then briefly review existing options available to researchers for conducting power analyses of multilevel models and note some advantages and disadvantages of each. We propose a flexible method for power analysis using simulation and walk through a worked example in detail from the literature on support receipt in close relationships. We build upon this example in a second worked analysis that uses a more complex design often utilized by relationship researchers—that is, when relationship processes are simultaneously examined for partner dyads within relationships. We recommend sensitivity analyses and demonstrate how they can be an important tool for understanding the differential impact of various factors on power and how they can be used to inform efficient study design. Lastly, we discuss how to generate estimates of model parameters when the researcher has little previous information on which to base predictions. We conclude by providing a summary of our recommended guidelines.

Illustrative example: The effect of support receipt on stress

Throughout this article, we situate our discussion within an example from the close relationships literature on social support by Bolger, Zuckerman, and Kessler (2000). Decades of research has documented a robust positive relationship between individuals’ perceptions of social support and various indicators of mental and physical well-being (House, Landis, & Umberson, 1988; LaRocco, House, & French, 1980; Taylor, 2007). The perceived availability of support is reliably associated with lower reports of psychological distress (Kessler & McLeod, 1985), improvements in individuals’ abilities to cope (Leavy, 1983), better adjustment to chronic stressors, and accelerated recovery from acute stressors (Cobb, 1976). However, reviews of the literature find that the association between perceptions of support and partners’ actual reports of enacted support is moderate (Barrera, 1986; Haber, Cohen, Lucas, & Baltes, 2007) and that often support provision attempts are associated with increased reports of stress and emotional distress on behalf of the recipient (Barrera, 1986).

In an early study of its type, Bolger et al. (2000) sought to examine if the inconsistent associations between support and (dis)stress could be accounted for by a support recipient’s awareness of having received support. They conducted a longitudinal diary study of romantic couples who were followed as one of the partners approached an important examination. Surprisingly, they found that on days when examinees reported receiving support they reported more stress, but there was not a corresponding increase in examinee stress when partners reported providing support. In addition, the effect of examinee reported support receipt on stress was significantly increased during the week prior to the exam (i.e., stress phase), while the effect of partner reported support provision on stress the week before the exam was again nonsignificant. In other words, examinee stress seemed to be associated—positively—with examinees’ report that they had received support from their partner but was independent of partners’ reports that such support had actually been provided.

Based on Bolger et al.’s (2000) research, in this article, we will conduct two sets of a priori power analyses for subsequent hypothetical research testing four hypotheses. First, given that the negative effects of support are mixed in the literature, we will first conduct a direct replication testing the hypothesis that on days in which examinees report receiving support, they report more stress (H1). Next, we seek to examine the hypothesized effect of partner support provision that was nonsignificant in Bolger et al.’s (2000) study. That is, on days in which partners report providing support, examinees report less stress (H2). Next, we will attempt to replicate Bolger et al.’s finding that the negative effect of support receipt is heightened during the stress phase (H3). Finally, we will test the hypothesis that the positive effect of support provision is heightened during the stress phase (H4).

In the second set of power analyses, we will expand Bolger et al.’s research to an explicitly dyadic design and test the reciprocal effects of support receipt and provision on both examinees and their partners. Our hypotheses for this study are the same as the previous (examinee-only) study; however, we expect the effects for partners to be somewhat weaker (since they are not under prolonged stress). In conducting power analyses, we will determine the number of individuals and time points needed to have a strong likelihood of observing statistically significant support for our hypotheses for both examinees and partners (assuming the effects exist in the population). In addition, we will assess other methodological factors besides individuals and time points that can increase our chance of success, particularly in cases in which initial sample-size-based power analyses indicate that we do not have sufficient resources to reliably observe an effect of interest.

Power for between-subject designs

We first review the basic concept of power and the factors that affect it using a basic unstandardized single-level regression model. Equation (1) depicts such a population model for a between-subjects version of the Bolger et al. (2000) social support model.

Y_{i} = b_{0} + b_{1} X_{i} + e_{i}

Here, Y_i is a continuous dependent variable (e.g., stress) that is modeled as a function of some continuous predictor variable, X_i , where i indexes individuals (e.g., support received from one’s partner). Also in the model are parameters b ₀, which indicates the average level of Y, and b ₁, which is the association between X and Y. The error term, e_i , is the deviation of individual i in their actual Y value compared to what would be expected given their value of X. In most cases, our parameter of interest is b ₁, the association between support receipt and stress.

Power, formally defined, is the probability of correctly rejecting a false null hypothesis. That is, it is the likelihood of declaring that one has found a significant hypothesized effect (e.g., α ≤ .05) in a sample given that there is an effect in the population. A power analysis involves determining the sample size necessary to ensure some predetermined probability (e.g., 80%) of rejecting the null hypothesis given a hypothesized effect size. Power is a function of the Type I error rate (i.e., α, which is generally fixed a priori), the effect size (unstandardized or standardized), and the standard error (Cohen, 1988).

In conducting a power analysis, we explicitly acknowledge uncertainty due to variability in our estimate of the effect size if we were to run the same study repeatedly across multiple samples. The standard error of an effect is the statistical approximation of that uncertainty for an effect from a single study. We use the standard error in conjunction with the estimated effect size to construct test statistics that are then evaluated for statistical significance. Our goal is to determine the minimum sample size necessary in order to have a high probability of concluding, in our single study, that we can be reasonably certain that our hypothesized effect size differs from zero in the population (i.e., that the association between support receipt and stress is statistically significant in our study).

The standard error is itself made up of three factors: the sample size, the variance in X (e.g., the degree to which some individuals receive more support than do others), and the error variance (e.g., the amount of variability in stress that is not due to differences in support receipt; see Table 1). Table 1 shows that increasing the sample size, N, will decrease the standard error (and increase power). Similarly, increasing the amount of variance in X (support receipt, $σ_{X}^{2}$ ) will increase power. However, increasing amounts of unexplained variance (i.e., error/residual, $σ_{e}^{2})$ will serve to decrease power.

Table 1.

Single level regression model and factors that affect power.

Regression model	Slope standard error
$Y_{i} = b_{0} + b_{1} X_{i} + e_{i}$	$σ_{b_{1}} = \sqrt{\frac{σ_{e}^{2}}{N σ_{X}^{2}}}$
Variables
Y_i	Dependent variable
X_i	Independent variable
e_i	Error (i.e., residual)
i	Indexes each individual
Parameters		Effect on power
b₀	Intercept estimate	↑
b₁	Slope estimate	↑
$σ_{b_{1}}$	Standard error of the slope	↓
$σ_{e}^{2}$	Error variance	↓
$σ_{X}^{2}$	Variance of independent variable	↑
N	Sample size (i.e., number of individuals, i)	↑

Note. ↑ = increasing the magnitude of the parameter increases power for the corresponding fixed effect; ↓ = increasing the magnitude of the parameter decreases power for the corresponding fixed effect.

Although we discuss at the end of this article strategies for increasing the effect size, or reducing the standard error by other means than increasing sample size, for the most part, the focus of a power analysis is to examine the likely impact on statistical significance of the number of observations at each level of analysis.² Next, we extend our discussion to the within-subject (multilevel) case, which is the primary focus of this article.

Power for within-subject (multilevel) designs

For demonstrating the factors that affect power in multilevel designs, we begin by extending the population model given in Equation (1) to that given in Equation (3) (cf., Raudenbush & Bryk, 2002).

{Y_{i}}_{t} = (b_{0} + b_{0 i}) + (b_{1} + b_{1 i}) * {X_{i}}_{t} + e_{i t}

In this example, we can imagine that individuals (i) were measured in terms of their levels of support receipt (X) and stress (Y) not just once but t times. Thus, Y_it is the value of stress for individual i on measurement t, and X_it is the value of support receipt for individual i on measurement t. The error term, e_it , is the measurement-specific deviation from the model prediction for each individual observation. Most important are the coefficients b _0i and b _1i. These are random variables that represent individual-specific intercepts and slopes, respectively, in addition to the sample average intercept (b ₀) and slope (b ₁). In other words, because individuals were assessed multiple times, we can estimate and statistically test if individual i reported a higher average level of stress across the diary period than the sample average level of stress (b ₀), as well as whether individual i had a lower association between support receipt and stress than the average association across the sample (b ₁). In a multilevel framework, we assume that b _0i and b _1i are normally distributed with a population mean and variance represented by ${\bar{b}}_{0}$ and $σ_{b_{0}}^{2}$ , and ${\bar{b}}_{1}$ and $σ_{b_{1}}^{2}$ , respectively. That is, we expect individuals to have some sample average level of anxiety, and some sample average association between support receipt and anxiety, but we also anticipate variability between individuals on both average stress (the intercept) and the association between support receipt and stress (the slope).

As before, if we ran a study in which we sampled a group of individuals and measured support receipt (X) and stress (Y) a total of t times for each individual, we can show that the power to detect the average within-subject effect of ${\bar{b}}_{1}$ (the slope) can be characterized as a function of Type I error rate, effect size, and the standard error (Table 2).³ The Type I error rate is defined as in the between-subjects case. The effect size, ${\bar{b}}_{1}$ , is analogous to b₁ in Equation (1). However, measuring individuals repeatedly over time results in two new components to the standard error not found in the between-subject example. These are n, the number of repeated assessments, and $σ_{b_{1}}^{2}$ , the variance of the random slope. Each is added to the equation for the sampling variance of the effect of X on Y from Equation (2) and is shown in Table 2 (cf., Snijders, 2005).

Table 2.

Multilevel regression model and factors that affect power.

Regression model	Slope standard error
$Y_{i t} = (b_{0} + b_{0 i}) + (b_{1} + b_{1 i}) * X_{i t} + e_{i t}$	$σ_{{\bar{b}}_{1}} = \sqrt{\frac{σ_{e}^{2}}{N n σ_{X}^{2}} + \frac{σ_{b_{1}}^{2}}{N}}$
Variables
Y_it	Dependent variable
X_it	Independent variable
e_it	Error (i.e., residual)
i	Indexes each individual
t	Indexes each repeated assessment
Parameters		Effect on power
b ₀	Intercept estimate	↑
b _0i	Individual-specific intercept	↑
b ₁	Slope estimate	↑
b _1i	Individual-specific slope	↑
$σ_{{\bar{b}}_{1}}$	Standard error of the average (between-person) slope	↓
$σ_{e}^{2}$	Error variance	↓
$σ_{X}^{2}$	Variance of independent variable	↑
$σ_{b_{1}}^{2}$	Variance of the individual slopes (multilevel)	↓
N	Sample size (i.e., number of individuals, i)	↑
n	Cluster size (i.e., number of repeated assessments, t)	↑

The multilevel sampling variance now consists of two components. The ratio to the left of the “+” sign (the within-subject component) is largely familiar, but now includes n in the denominator, which indicates that as the number of repeated measurements increases so will power. Our observation of repeated measurements now also allows us to identify individual differences, and thus there is an additional piece to the sampling variability to the right of the “+” sign (the between-subject component) that includes the variance of the individual slopes divided by N, the number of individuals.⁴

Available tools for power analysis

Having reviewed the components that influence power in a multilevel model, we now turn to available tools for estimating it. Until recently, there were relatively few resources available to conduct power analyses for multilevel models. Those that are available fall into two broad categories: formula based and simulation. Formula-based approaches can often be found in books specializing in multilevel modeling and longitudinal design (Ahn, Heo, & Zhang, 2015; Fitzmaurice, Laird, & Ware, 2012; Gelman & Hill, 2006; Hox, 2010; Liu & Liang, 1997; Moerbeek & Teerenstra, 2016; Moerbeek, Van Breukelen, & Berger, 2008; Snijders & Bosker, 1993, 1999). Such approaches are able to provide exact estimates of power for various sets of models where the standard errors for certain parameters have been explicitly derived. However, given the considerable effort required to derive such formulae for the countless possible models researchers could be interested in, many available formulae are restricted to more basic multilevel models (e.g., Moerbeek & Teerenstra, 2016).

The approach that we typically prefer is the use of simulation methods (Bolger & Laurenceau, 2013; Gelman & Hill, 2006). This approach is supported by many of the statistical software packages psychologists use, including Mplus (Muthén & Muthén, 1998–2012), R (R Development Core Team, 2015), SAS (SAS Institute, 2013; Zhang & Wang, 2009), and SPSS (IBM, Inc., 2013) and has myriad uses in scientific research beyond power applications (cf., Paxton, Curran, Bollen, Kirby, & Chen, 2001). The rationale behind power estimation by simulation is to use the hypothesized population model and parameters to generate data for a hypothetical study. We can then analyze the data from this study using our hypothesized statistical model and record the significance of the effects of interest. Since the data are randomly generated using the population model, there will be sampling variability in the estimates of the individual effects and their standard errors, and we will not exactly recover the parameters of the population model. This can be done thousands of times, simulating thousands of hypothetical studies, and for each we record the significance of the hypothesized effects. The proportion of times each individual effect is significant across all of the simulations is the power of that effect—quite literally, the expected number of times you would observe a significant effect if an alternative hypothesis was true in the population.⁵

In an effort to make formulae or simulation-based procedures easier to apply and power analysis for such designs more widely accessible, a number of specialized software programs have been developed, including RMASS2 (Hedeker, Gibbons, & Waternaux, 1999), Optimal Design (Raudenbush et al., 2011), PinT (Bosker, Snijders, & Guldemond, 2007), and ML-DEs (Cools, Van den Noortgate, & Onghena, 2008). These programs generally provide the user with a limited set of models to choose from, and once chosen present a list of the various parameters the user must specify in order to conduct the analysis. Although these software vary in their degree of user-friendliness, they can be fast and convenient when researchers know the specific model they wish to estimate, that model is accommodated by the software, and they can generate reasonable estimates for the model parameters. However, as with the formula-based approach, the array of supported models across software programs can be limited, and there are few guidelines for generating parameter estimates when the model specifications are not well defined by previous research. Moreover, generating sample size estimates from software that cannot fully accommodate a predicted model comes with the risk of producing invalid power estimates via model misspecification.

We present here a syntax-based procedure for conducting power analysis using simulation. While the learning curve can be steep, investing in the process will pay considerable dividends in fully understanding the model one wants to estimate, identifying all of the factors that can affect hypothesized statistical tests, and providing an exact template of the desired analysis once the data have been collected. Furthermore, the simulation approach can be extended to a virtually unlimited variety of models in order to accommodate researchers’ idiosyncratic needs.

Longitudinal random effects model example (support receipt and anxiety)

In this section, we provide an example of how to conduct a power analysis using simulation in Mplus (Muthén & Muthén, 1998–2012). We chose Mplus because it requires the least amount of formal programming knowledge and has the ability to accommodate a wide variety of statistical models without changing the analysis framework. In both examples, we will attempt to fully describe each element of the syntax and how it relates back to the information we gathered to conduct the power analysis. We present the analogous syntax for R (R Development Core Team, 2015), SAS (SAS Institute, 2013; Zhang & Wang, 2009), and SPSS (IBM, Inc., 2013) in the Online Supplement to this article.

We describe a power analysis in which we gather information from that provided by Bolger et al. (2000) and link it to syntax generated in Mplus. Our first example represents a particularly complete reporting of the information necessary to conduct a power analysis. We use it partially as an exemplar of how to report such analyses in the interest of facilitating power analyses aimed at promoting future research and replication. Later we describe methods for estimating parameters when the model is less well defined.

The information needed broadly consists of four components:

The statistical model

The measurement scale for each variable

Expected patterns of missingness

All means, variances, and parameter estimates (i.e., covariances) for variables defined by the model

Bolger et al. (2000, p. 956) explicitly define their statistical model, which we restate in Equation (3). They operationalized stress using reports of anxiety and depression in separate analyses; for the current example, we focus their analysis using anxiety as the dependent variable. We recommend writing out the hypothesized statistical model as a first step in any power analysis, both to help identify the information needed and to prepare for syntax generation (which will require this model to be explicitly stated)

\begin{matrix} {Anx}_{i t} = (b_{0} + b_{0 i}) + (b_{1} + b_{1 i}) * {LagAnx}_{i t} + b_{2} * {Phase}_{i t} \\ + (b_{3} + b_{3 i}) * {Provision}_{i t} + (b_{4} + b_{4 i}) * {Receipt}_{i t} \\ + b_{5} * {Provision}_{i t} * {Phase}_{i t} + b_{6} * {Receipt}_{i t} * {Phase}_{i t} + e_{i t} \end{matrix}

Several components of this model are consistent with Equation (2). Specifically, the outcome, examinees’ anxiety (Anx _it ) is a function of a fixed and random intercept (b ₀ and b _0i) and support receipt (b ₄ and b _4i). This basic model is expanded by Bolger et al. (2000) to also account for the previous measurement’s anxiety ((b ₁ + b _1i)*LagAnx _it ; cf., Castro-Schilo & Grimm, this issue), whether or not it was the week before the exam (b₂ *Phase _it ), and if the examinees’ partner reported providing support ((b ₃ + b _3i)*Provision _it ). The authors also estimated two two-way interactions, between provision and phase and between receipt and phase (b ₅ *Provision _it *Phase _it , b ₆*Receipt _it *Phase _it ).

Now that we have defined our model (Step 1), we must determine the scale on which all of the variables are measured (Step 2), which is in this case easily determined from the Measures section of the original manuscript (Bolger, Zuckerman, & Kessler, 2000, p. 955): Examinee anxiety is a continuous variable and support and phase are binary variables. The authors indicate that their final sample was composed of 68 couples, each of whom provided 32 days of data (Bolger et al., 2000, p. 955). However, they also note that approximately 2% of the data were missing (Step 3).

Finally, we must acquire estimates for all means, variances, and parameters (Step 4). We begin by determining the parameter estimates for all of the fixed effects. Fortunately, Bolger et al. (2000, p. 957) provide the unstandardized fixed effects parameter estimates, which we reproduce in Table 3. In the original study, we see that both support receipt and its interaction with phase were statistically significant, while both support provision and its interaction with phase were not. Next, we determine the parameter estimates for the random effects. The random effects are not reported in the main body of Bolger et al. (2000) but rather in their Footnote 6 (p. 956). They report standard deviations for the random effects of the intercept, lagged anxiety, and support receipt to be .306, .147, and .229, respectively. For the power analysis, we square these values to estimate the variances for those random effects (Table 2). The authors were unable to estimate a random effect for support provision, suggesting that it was very small in actuality, and therefore constrained it to 0.0 in the final model. We estimated this random effect but assigned it a very small variance ( $σ_{b_{3}}^{2}$ = .001).

Table 3.

Parameter estimates and power results for Bolger et al. (2000).

				Power
Parameter	Mplus parameter	Estimate	p	N = 68	N = 110	N = 310
Main effects
Intercept	BTW – Means ANX	.140	.002	.863	.972	1.000
Lag anxiety	BTW – Means SLOPE1	−.500	.000	1.000	1.000	1.000
Phase	WTH – ANX ON PHASE	.400	.000	1.000	1.000	1.000
Supp. provision	BTW – Means SLOPE2	−.040	.350	.234	.343	.798
Supp. receipt	BTW – Means SLOPE3	.120	.025	.844	.963	1.000
Provision × Phase	WTH – ANX ON PHPROV	−.030	.748	.065	.083	.141
Receipt × Phase	WTH – ANX ON PHREC	.170	.047	.555	.792	.995
Random effects
Intercept	BTW – Variances ANX	.094	<.050	1.000	1.000	1.000
Lag anxiety	BTW – Variances SLOPE1	.022	<.050	.794	.959	1.000
Supp. provision	BTW – Variances SLOPE2	.001	>.050	.010	.010	.022
Supp. receipt	BTW – Variances SLOPE3	.052	<.050	.943	.997	1.000
Error/residual variance	WTH – Residual Variances ANX	.420^a	<.010^a	1.000	1.000	1.000
Means
Lag anxiety	WTH – Means LANX	.000
Phase	WTH – Means PHASE	.220
Supp. provision	WTH – Means PROV	.580
Supp. Receipt	WTH – Means REC	.560
Provision × Phase	WTH – Means PHPROV	.000
Receipt × Phase	WTH – Means PHREC	.000
Variances
Lag anxiety	WTH – Variances LANX	.500
Phase	WTH – Variances PHASE	.170
Supp. provision	WTH – Variances PROV	.240
Supp. receipt	WTH – Variances REC	.250
Provision × Phase	WTH – Variances PHPROV	.041
Receipt × Phase	WTH – Variances PHREC	.033
Covariances
Cov(Provision, Receipt)	WTH – PROV WITH REC	.051

Note. N corresponds to the number of subjects in the power analysis. The number of assessments (n) is fixed at 32. BTW—between-level results. WTH—within-level results.

^aResidual variance and p-value estimated from Shrout et al. (2006).

Lastly, we estimate the means and variances for each of the variables in the model. Means and variances of the phase and support variables are not directly provided by the authors, but they can be easily derived. The authors note that of the 32 days that individuals completed diaries, 7 belonged to the week prior to the exam.⁶ A dichotomized variable was created in which 22% (7/32) of the entries belonged to the stressed phase and the other 78% belonged to the nonstressed phase. We can then multiply these values to create an estimate of the variance for the phase variable (i.e., p(1−p)). Therefore, phase has a mean of .22 and a variance of .17. The authors also present the proportions of support provision and support receipt days across the study (p. 956). From this, we can estimate that partners reported support provision on 58% of days and examinees reported support receipt on 56% of days. As with the phase variable, we can use these values to estimate each support variable’s variance to be .24 and .25, respectively. The authors do not report a mean or variance for the lagged anxiety predictor; however, this is not a major concern as its primary use was as a covariate, for which the other parameter estimates are already adjusted. We use an estimated mean of 0.0 and a variance of .5 in the simulation. Lastly, we require an estimate of the error variance. Unfortunately, the authors do not report this nor do they provide a direct means for estimating it. However, another published article using the same data does provide us with a useful estimate of the error variance. Shrout, Herman, and Bolger (2006) reanalyzed the data from this study using different statistical models and examining different moods with the same hypotheses in mind. They report error variances for their models, which, although not exact due to the different modeled parameters, provide reasonable estimates for the error variance used here.

Figure 1 provides the input syntax to conduct a Monte Carlo simulation study in Mplus using the population values just described and the statistical model from Equation (3). Individual lines are commented using exclamation points (!) and include heading identifiers that correspond to the following explanations:

Figure 1.

Mplus syntax for power analysis of Bolger et al. (2000).

A list of variables in the model: anxiety (anx), lagged anxiety (lanx), phase (phase), support provision (prov), support receipt (rec), phase by provision interaction (pprov), phase by receipt interaction (prec)

Total number of observations: N multiplied by n (2,176)

Number of individuals (68) and repeated measurements (32)

Arbitrary value for the random number generator (20160215) so that one can rerun the simulation and get the same results

Number of simulated studies⁷ (1,000)

Generate patterns of missingness (missing completely at random): In this case, 1 pattern (p = 1.0) where anx is missing on 2% of cases

Predictors that only vary at the within-subjects level (lanx, phase, prov, rec, pprov, prec)

Predictors that only vary on the between-subjects level (none in current example)

Type of model: a two-level random effects model

Specify the generating population model

Specification for the within-subjects effects (see Figure 1 for details)

Specification for the between-subjects effects (see Figure 1 for details)

Specify the model to be estimated: It is the same and the population model syntax should be copied into this section

The results of the power analysis using the specifications from the original model reported by Bolger et al. (2000) are shown in Table 3 and Supplementary Material (for additional examples of annotated Mplus output see Bolger & Laurenceau, 2013; Bolger, Stadler, & Laurenceau, 2012). From these results, we can see that a replication would be acceptably powered to test H1 (the main effect of support receipt) but underpowered to test the other hypotheses (e.g., support provision, both support by phase interactions).

To ensure that a future study is well powered to detect all hypothesized effects, we can vary the number of individuals (N) and/or repeated assessments (n) we wish to collect. In this case, holding the number of assessments fixed at 32, we wish to see the number of individuals required so that the effect of the support receipt by phase interaction is powered to 80% (H3). Table 1 shows that this will be accomplished by recruiting a sample of 110 individuals. We note that this is approximately double the original sample, despite the original sample producing a statistically significant result. This is because the initial study obtained a p-value for the effect of .047, which is close to the critical value (α = .05) where power is 50% (Cohen, 1988). As such, considerably more individuals would be necessary to observe the same effect at greater than chance probability. Given that Bolger et al. (2000) also hypothesized (but did not find) that the provision of support would be associated with a decrease in examinees’ anxiety, we may wish to see the sample required to power the support provision effect (b = −.04, p = .350) to 80% (H2). Rerunning the power analysis, we see that this would be accomplished by recruiting a sample of 310 individuals. Consistent with this power analysis, a replication of Bolger et al. (2000) conducted by Shrout et al. (2010) using a sample of 312 examinees and 310 of their partners over the course of 35 days did observe significant effects for both support receipt and support provision. However, we note that even in a sample of 310 individuals, we are still heavily underpowered to detect a significant provision by phase interaction. Given the current model and parameter estimates, we would require 3,000 individuals to have 80% power to detect such an effect. This highlights that researchers may find that the sample size required to test their hypothesis may go far beyond their available resources. In such situations, they might reconsider whether the effect, even if it does exist in the population, is sufficiently large to be of substantive importance.

Dyadic longitudinal random effects/actor–partner interdependence model example (coupled support receipt and anxiety)

Our second example departs from the previous model in two important ways. First, although Bolger et al. (2000) collected couples data, only the examinees’ outcome was estimated. In our second example, we demonstrate a model in which we simultaneously predict stress for both the examinees and their partners. We model the data together in a dyadic data analysis using the actor–partner interdependence model (Kashy & Kenny, 1999; Kenny, 1996; see Iida, Seidman, & Shrout, current issue; Rogers, Wood, & Furr, current issue; and Stern & West, current issue, for further details and potential alternatives). In doing so, we can fit a multivariate version of Equation (3) in which each partner is modeled simultaneously (Laurenceau & Bolger, 2005; Raudenbush, Brennan, & Barnett, 1995; Raudenbush & Bryk, 2002). This model is presented as follows:

\begin{matrix} {Anx}_{i t d} = E_{d} * [(b_{0 E} + b_{0 E i}) + (b_{1 E} + b_{1 E i}) * {LagAnx}_{i t d} + b_{2 E} * {Phase}_{i t d} \\ + (b_{3 E} + b_{3 E i}) * {Provision}_{i t d} + (b_{4 E} + b_{4 E i}) * {Receipt}_{i t d} \\ + b_{5 E} * {Provision}_{i t d} * {Phase}_{i t d} + b_{6 E} * {Receipt}_{i t d} * {Phase}_{i t d}] \\ + \\ P_{d} * [(b_{0 P} + b_{0 P i}) + (b_{1 P} + b_{1 P i}) * {LagAnx}_{i t d} + b_{2 P} * {Phase}_{i t d} \\ + (b_{3 P} + b_{3 P i}) * {Provision}_{i t d} + (b_{4 P} + b_{4 P i}) * {Receipt}_{i t d} \\ + b_{5 P} * {Provision}_{i t d} * {Phase}_{i t d} + b_{6 P} * {Receipt}_{i t d} * {Phase}_{i t d}] \\ + e_{i t d} \end{matrix}

This model allows for the estimation of parallel effects for each of the dyad members, d, while also allowing for each dyad member to have unique random variation that correlates with that of their partner. Indicators E_d and P_d signify which partner each line of data comes from so that separate examinee and partner components of the model can be estimated. Determining parameter estimates in our first example was largely straightforward, as we were conducting a hypothetical direct replication. In many real-world research scenarios, however, precise estimates of our hypothesized parameters are not available. In our second example, we demonstrate a power analysis in which we adjust findings from a similar model to offer best guesses of our proposed effects. Later, we discuss strategies for making such guesses when the models are even more weakly predefined.

Bolger et al. (2000) hypothesized that when examinees acknowledged support receipt from their partners they would feel more distressed and that this effect would be particularly exaggerated the week prior to their stressful examination (i.e., phase). The authors also collected, but did not analyze, similar data on the partners of examinees. By their logic, we might hypothesize that partners also feel more distressed after acknowledging support provision, but since they are not preparing for a difficult examination and not under systematic prolonged stress, the effects may be weaker.

Table 3 presents parameter estimates for a simulation study in which both examinees and partners report on their anxiety, if they provided support, and if they received support as the examinees’ exam approached. Many of the estimates are the same as those presented in Table 2, just repeated twice, once for each dyad member. We may expect many of the individual-level parameter estimates to be the same across dyad members, and so we retain the examinee estimates in many cases. This includes assuming 2% missing data for partners.

Because partners are not preparing for a difficult examination and are not under systematic prolonged stress, overall we expect them to report less anxiety. Therefore, we estimated the intercept to be .07 instead of .14. We also expect a smaller main effect of phase (.20 instead of .40), a smaller effect of support receipt on anxiety (.06 instead of .12), and a smaller interaction between support receipt and phase (.04 instead of .17). Lastly, since partners’ reports are likely to be correlated, we specified that partners’ random intercepts, slopes, and residual variances correlated at a moderate level (r ≈ .30; Kenny, Kashy, & Cook, 2006). This was accomplished by using the formula for calculating the correlation between two variables, in which we know the approximate correlation (Kenny et al., 2006) and the variances of partners’ parameters (Bolger et al., 2000), and so can estimate the shared covariance between each pair (see Table 4).⁸ Figure 2 presents the Mplus syntax for this model.

Table 4.

Power results for dyadic example.

			Power
Parameter	Mplus parameter	Estimate	N = 68	N = 310
Main effects
Intercept (E)	BTW – Means EANX	.140	.872	1.000
Intercept (P)	BTW – Means PANX	.070	.326	.921
Lag anxiety (E)	BTW – Means ESLOPE1	−.500	1.000	1.000
Lag anxiety (P)	BTW – Means PSLOPE1	−.500	1.000	1.000
Phase (E)	WTH – EANX ON EPHASE	.400	1.000	1.000
Phase (P)	WTH – PANX ON PPHASE	.200	1.000	1.000
Supp. provision (E)	BTW – Means ESLOPE2	−.040	.276	.831
Supp. provision (P)	BTW – Means PSLOPE2	−.040	.259	.838
Supp. receipt (E)	BTW – Means ESLOPE3	.120	.854	1.000
Supp. receipt (P)	BTW – Means PSLOPE3	.060	.347	.893
Prov. × Phase (E)	WTH – EANX ON EPHPROV	−.030	.086	.148
Prov. × Phase (P)	WTH – PANX ON PPHPROV	−.030	.076	.163
Receipt × Phase (E)	WTH – EANX ON EPHREC	.170	.565	.998
Receipt × Phase (P)	WTH – PANX ON PPHREC	.040	.097	.167
Random effects
Intercept (E)	BTW – Variances EANX	.094	.999	1.000
Intercept (P)	BTW – Variances PANX	.094	1.000	1.000
Lag anxiety (E)	BTW – Variances ESLOPE1	.022	.826	1.000
Lag anxiety (P)	BTW – Variances PSLOPE1	.022	.811	1.000
Supp. provision (E)	BTW – Variances ESLOPE2	.001	.012	.026
Supp. provision (P)	BTW – Variances PSLOPE2	.001	.011	.031
Supp. receipt (E)	BTW – Variances ESLOPE3	.052	.946	1.000
Supp. receipt (P)	BTW – Variances PSLOPE3	.052	.944	1.000
Random effect covariances
Intercept (E-P)	BTW – EANX WITH PANX	.030	.526	.993
Lag anxiety (E-P)	BTW – ESLOPE1 WITH PSLOPE1	.007	.214	.695
Supp. prov. (E-P)	BTW – ESLOPE2 WITH PSLOPE2	.000	.000	.002
Supp. receipt (E-P)	BTW – ESLOPE3 WITH PSLOPE3	.017	.253	.844
Residual (E-P)	WTH – EANX WITH PANX	.100	1.000	1.000

Note. N corresponds to the number of subjects in the power analysis. The number of assessments (n) is fixed at 32. Means and variances are the same for both partners as in Table 3 and so are excluded. (E)—Examinee. (P)—Partner. BTW—between-level results. WTH—within-level results.

Figure 2.

Mplus syntax for dyadic power analysis.

Table 4 presents results from the power simulation of the hypothetical dyadic model using the original sample size and number of repeated assessments reported by Bolger et al. (2000). As expected, the hypothesized smaller support receipt effect for partners would be underpowered (34.7%; H1). However, using the sample size from Shrout et al. (2010), replication of this study offers good power for the main effect of partner support receipt (89.3%), as well as partner support provision (83.8%; H2). Alternatively, with the exception of the examinee support receipt by phase interaction, the interaction effects are still heavily underpowered in the event that the researchers expect them to differ from zero in the population (H3 and H4).

Sensitivity analysis and factors that affect power

In Example 1, we demonstrated a power analysis in a case in which the model parameters were generally well defined, and the main source of uncertainty was merely due to sampling variability. Such methods are particularly useful in instances where the researcher is seeking to conduct a direct replication and has a large amount of resources. However, in most cases, there is also uncertainty surrounding the predicted values of model parameters themselves. This may be due to novel hypotheses regarding effect sizes that have not been previously established in the literature, as well as limited information regarding the expected magnitudes or structure of the variance or residual covariance components. Researchers may also conduct a power analysis and discover that they do not have the resources available to have a high likelihood of observing particular hypothesized effects.

To address these issues, in this section, we briefly discuss sensitivity analysis. Sensitivity analyses are iterative analyses that systematically assess the impact on power of various model parameters. Sensitively analyses can fulfill two related objectives: First, they can identify lower limits of expected power across a range of parameter values and combinations when there is limited preexisting information about the likely magnitude of the effects. For instance, a researcher may be unsure of the size of a dyad-level random slope effect but can use sensitivity analyses to ensure that a study is sufficiently powered even in the event that the random effect is quite large. Second, sensitivity analyses can examine trade-offs when resources are limited. For instance, the researcher can assess the impact of increasing number of participants versus number of measurements when funding for participant remuneration is fixed or can help researchers identify which moderators or mediators of interest are most likely to be fruitful to assess given a fixed amount of survey time. In all cases, we recommend that researchers create tables or plots of multiple specifications to examine the sensitivity of their model design to various exogenous or endogenous factors and optimize their design to maximize study success. Below we provide some examples for doing so using the support provision examples described above and offer guidance for anticipating the impact of some common design decisions on power.

Assuming that we hold the Type I error rate constant, the remaining factors that influence power are the effect size and standard error. So far, we have restricted our conversation to the influence of the number of participants, but the researcher also has direct control over the number of repeated assessments. From a practical standpoint, researchers conducting studies that involve repeated assessments are often faced with the issue of balancing the number of repeated assessments and the number of individuals recruited. Increasing participants can be time-consuming and costly. Increasing the number of assessments can be associated with participant fatigue, leading to increased dropout and decreased quality of data. Relatively, it may ultimately be easier to increase the number of assessments compared to recruiting more participants, but from the viewpoint of statistical power, is it worth it (see also Rast & Hofer, 2014)?

To provide perspective in attempting to answer this question, we conducted a series of power analyses using the model from Table 3. We focus on the interaction effect between support receipt and phase, which in the original example with 68 couples and 32 assessments had 55.5% power. Assuming that the total number of measurements that a researcher was able to collect was fixed, in Figure 3 we show the relative increase in power for this effect as either the number of individuals or the number of assessments is increased. As is suggested by Table 2, increasing the number of participants increases power more than increasing the number of assessments. This is because increasing the number of participants decreases both the within-subject and between-subject components of the standard error, whereas increasing the number of assessments only decreases the within-subject component (Snijders & Bosker, 1999). In this example, it is critical to note that increasing the number of assessments while holding the number of participants constant will never reach 80% power. This is an important point more broadly, as in certain designs, such as diary studies, it is often less expensive to have participants complete more assessments than it is to recruit more participants. Figure 3 demonstrates that even a few extra participants may be more impactful for testing a hypothesis than hundreds of additional measurements. However, a researcher might also require a minimum number of assessments to assure variability in variables of interest. For example, interpersonal conflict might be rare compared to support receipt. Thus, while increased subjects may gain a researcher more power than increased assessments holding all other parameters equal, this may come with a trade-off of realistically also reducing predictor variance, which will undermine power.

Figure 3.

Sensitivity analysis of the effect of adding participants versus adding assessments on the estimated power of the phase by support receipt interaction in Bolger et al. (2000).

Beyond the number of participants and assessments, Table 2 shows that other study elements can affect the probability that a hypothesized effect will be significant. These are less directly under the researcher’s control, but the researcher can make efforts to mitigate them. For example, researchers might also measure constructs they believe are associated with their dependent variable and include them in their analyses as covariates in order to decrease error variance ( $σ_{e}^{2}$ ). This will have the effect of increasing power. Experimental techniques like matching or blocking participants or engaging methodological strategies for reducing measurement noise can also decrease error variance and increase power. Researchers may also attempt to maximize the variance in their predictor by assigning participants equally to groups if the predictor is categorical or sampling subpopulations with more variability on X or from the extremes of the distribution if the predictor is continuous ( $σ_{X}^{2}$ ), which also would increase power.

One factor that affects power that is probably the least under researchers’ control is the random variation of an effect across subjects ( $σ_{b_{1}}^{2}$ ). These are the random effects in a multilevel model, and as their variance increases, power for the associated fixed effect decreases. Given that researchers generally have less control over how much a hypothesized effect will vary across subjects, and they may not even have an expectation as to how much an effect varies across subjects to begin with, it is useful to investigate how much different levels of variation in a random effect can impact the power of the associated fixed effect. To do this, we again use the Bolger et al. (2000) example and, in this case, focus on the main effect of support receipt. They reported that this effect had an associated random effect with variance .052. That is, the fixed effect of support receipt on stress of .12 could vary across participants, with some participants being quite negatively impacted by support receipt while others showed a very small or negligible negative effect. However, such a random effect might be very difficult to estimate in the absence of prior research. It may also be difficult to estimate empirically and requires a researcher to estimate such an effect as fixed (Barr, Levy, Scheepers, & Tily, 2013). Therefore, we can conduct a sensitivity analysis to assess the impact of this random effect on our overall power. We have plotted this effect in reference to three other factors that affect power in order to illustrate its influence.

First we show how increasing the number of participants (Figure 4(a)) can mitigate the impact of an increasingly large random effect. In the first power analysis, we saw that the power of the support receipt main effect in Bolger et al. (2000) was 84.4%. Assuming the same number of participants, we can see that as the random effect of support receipt increases power decreases steadily. However, increasing the number of participants mitigates this effect, importantly in a nonlinear way. As the number of participants increases, the slope of the power curve decreases, initially sharply, but less so with each increment. This indicates that increasing the number of participants can protect against large random effects, but after a certain number of additional participants, it is unnecessary. We next illustrate the same effect for increasing the number of assessments (Figure 4(b)). In contrast to Figure 4(a), adding more assessments is not as protective as adding participants. These two examples represent direct ways in which researchers can hedge themselves against uncertainty with regard to the size of random effects. Lastly, we illustrate the impact of increasingly large random effects on the power of the fixed effect as the size of the fixed effect changes (Figure 4(c)). A researcher might be interested in how robust their hypothesized effect is to the random between-subject variation observed within their sample. Importantly, Figure 4(c) shows that smaller effects are disproportionately affected by random slope variation. Larger effects are more resilient, and random slope variation is not as much of a concern.

Figure 4.

Sensitivity analyses for Bolger et al. (2000) of the effect of random slope variance on power at varying levels of (a) participants, (b) assessments, and (c) effect sizes.

Determining parameter estimates

Although we recommend sensitivity analyses regardless of the certainty a researcher may have in the parameters of their proposed model, it can still be hard to know where to start. Certainly, it is unfeasible (and unhelpful) to conduct power analyses on an infinite combination of parameter values. In this section, therefore, we provide some initial (and incomplete) pointers for obtaining starting values for your power sensitivity analyses.

Echoing decades of other scholars who have written on methodological and design issues in relationship research, our strongest recommendation is to pilot, pilot, pilot! Having concrete data on which to base multilevel power analyses, however small or unrepresentative the sample, can result in considerably less effort in estimating the various parameters for the hypothesized population model and less uncertainty regarding the parameter specifications in the model. Pilot data are particularly useful for the estimation of random effects in power analyses, as these are infrequently reported in published research. While pilot study estimates may themselves be imprecise and subject to sampling variability, they at least provide a starting point from which to conduct sensitivity analyses.

Drawing on previously conducted studies using similar measures or employing similar designs can also be extremely useful, although researchers may have to contact the authors of the original study to obtain the necessary parameter estimates. For instance, an existing study of support receipt on stress may be a useful starting point for estimating parameters modeling the effect of support receipt on intimacy; or a study of relationship satisfaction approaching and following marriage may provide some clues for a new study examining weight fluctuation approaching and following marriage. Researchers may also turn (cautiously) to between-person estimates as proxies for proposed within-person processes. Most importantly, the researcher should become familiar with their literature. Many patterns, such as residual autocorrelation structures or self- versus other effect sizes are largely consistent even across quite varied studies. In sum, although the values of many parameter estimates may not be intuitive, the existing literature may provide useful initial approximations for a wide variety of parameters, which, combined with sensitivity analyses, may offer considerable insight into the resources needed to maximize successful studies and minimize failed ones.

Conclusion

We detailed above a method for conducting power analyses for designs commonly used in relationships research, including all of those reviewed in this special issue (Castro-Schilo & Grimm, this issue; Iida, Seidman, & Shrout, this issue; Rogers et al., this issue; Stern & West, this issue). Although it requires effort, we believe that this method can be used by relationships researchers in planning future studies and in writing grant applications. To recapitulate, conducting a power analysis involves answering the following questions:

Q1: What information do I need to conduct a power analysis for a proposed study involving multiple individuals in dyads or families, at single or multiple time points?

A1: Researchers will need to know in advance their hypothesized statistical model, including estimates for all parameters. This includes means, variances, and coefficients (i.e., covariances/correlations) for the effects at each level of analysis.

Q2: How do I conduct a power analysis once I have collected the necessary information?

A2: Several formulae and software programs exist for conducting power analyses for a subset of common models. We offer tools for conducting power analyses using simulation, an approach that can accommodate virtually any model.

Q3: What factors are likely to have the strongest effect on power?

A3: The factors that influence power are the Type I error rate (usually set a priori to α = .05), effect size, and standard error (which comprises the sample size at each level of analysis and variance components). Of primary interest to most researchers are the within-subject (n) and between-subject (N) sample sizes. Increasing both increases power, but as Figure 3 illustrates, increasing the between-subjects sample size boosts power more than increasing the number of within-subjects assessments. We draw special attention to the variance of the random within-subject slope ( $σ_{b_{1}}^{2}$ ): The greater its variance, the lower the power to detect within-subject effects.

Q4: What if I do not have all of the information that I need?

A4: It is unlikely that researchers will have precise estimates of all parameters unless they are conducting a direct replication. We strongly recommend collecting pilot data or drawing on prior research using similar measures and designs. However, when even imprecise estimates are difficult to locate, we encourage anchoring on the conservative end of the distribution.

In closing, we hope that the procedures detailed here will help relationships researchers plan informative studies that make the best use of financial resources. For additional examples of power simulations using models that are relevant to relationships researchers, see Bolger & Laurenceau (2013) and Bolger, Stadler and Laurenceau (2012).

Supplemental material

Supplementary_material - Power struggles: Estimating sample size for multilevel relationships research

Supplementary_material for Power struggles: Estimating sample size for multilevel relationships research by Melissa A. Curran, Lara K. Kammrath, J.-P. Laurenceau, Sean P. Lane, and Erin P. Hennes in Journal of Social and Personal Relationships

Supplemental material

Supplemental Material, Additional_supplemental_files_to_add_for_lane_hennes_2018_JM - Power struggles: Estimating sample size for multilevel relationships research

Supplemental Material, Additional_supplemental_files_to_add_for_lane_hennes_2018_JM for Power struggles: Estimating sample size for multilevel relationships research by Melissa A. Curran, Lara K. Kammrath, J.-P. Laurenceau, Sean P. Lane, and Erin P. Hennes in Journal of Social and Personal Relationships

Footnotes

Acknowledgments

The authors would like to especially thank Niall Bolger and Patrick E. Shrout for their advisory roles in developing and guiding the work that formed the basis of this manuscript. The authors would also like to thank them, the Columbia University and New York University Couples Labs, and three anonymous reviewers for their helpful feedback on earlier versions of this article.

Funding

The author(s) disclosed receipt of the following financial support for the research, authorship, and/or publication of this article: This research was supported by the National Institutes of Health grant T32 AA013526.

Supplemental material

Supplementary material is available for this article online.

Notes

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