Background:

Although anxiety is more common than depression among older adults, research on the nature and treatment of anxiety and worry has lagged behind that of depression. Cognitive-behavioral therapy (CBT) and yoga have been shown to decrease worry and anxiety, but there are no comparative effectiveness trials of these modalities for treating worry in older adults.

Objectives:

The primary aim of this study was to compare the effects of CBT and yoga on worry (Penn State Worry Questionnaire-Abbreviated [PSWQ-A]) in older adults (≥60 years). The secondary aims of this study were to compare the effects of these interventions on anxiety (PROMIS® Anxiety scale) and sleep (Insomnia Severity Index [ISI]). The exploratory aims of this study were to determine participant preference for CBT vs yoga and to examine participant preference and selection effects on worry, anxiety, sleep, adherence to intervention, and attrition rates.

Methods:

We conducted a 2-stage randomized preference trial. Other research indicates that choosing one's treatment has an impact on outcomes, adherence, and attrition, and this design allowed us to examine intervention effects within the randomized study and preference and selection effects. Participants were adults aged ≥60 years with moderate to severe levels of self-reported worry (Penn State Worry Questionnaire-Abbreviated [PSWQ-A] score ≥26). The randomized preference trial included a traditional randomized trial and a preference trial. In the randomized trial, half of participants were randomly assigned to either CBT or yoga. In the preference trial, participants were able to choose their preferred intervention. CBT consisted of 10 weekly individual telephone sessions, and yoga consisted of 20 biweekly yoga classes in community settings. The primary outcome was worry (PSWQ-A) and the secondary outcomes were anxiety (PROMIS Anxiety) and sleep (ISI). Intervention effects were estimated immediately postintervention at week 11 using a constrained mixed-model repeated measures analysis with an unstructured covariance matrix.

Results:

We randomly assigned 500 older adults to either the randomized trial (n = 250; n = 125 in CBT and n = 125 in yoga) or the preference trial (n = 250; n = 120 chose CBT and n = 130 chose yoga).

Randomized Trial:

The intervention effect on week 11 follow-up PSWQ-A means for yoga compared with CBT was 1.6 (95% CI, −0.2 to 3.3; P = .08), suggesting that the effects of both interventions were not significantly different. There were significant reductions in the mean PSWQ-A scores in both arms of the randomized trial. The mean PSWQ-A score dropped from 31.2 to 22.4 among participants randomly assigned to CBT for a change of −8.8 (95% CI, −10.1 to −7.5). Among participants randomly assigned to yoga, the analogous change was −7.2 (95% CI, −8.5 to −6.0). The intervention effect on follow-up PROMIS Anxiety means was 0.3 (95% CI, −1.5 to 2.2; P = .71). At week 11, the reductions in means, relative to baseline values, were −7.5 (95% CI, −8.8 to −6.1) and −7.1 (95% CI, −8.5 to −5.8) for the CBT and yoga arms, respectively. There was a significant difference on the ISI by intervention. The intervention effect on follow-up ISI means was 2.4 (95% CI, 1.2-3.7; P = .0002). At week 11, the reductions in means, relative to their baseline values, were −5.4 (95% CI, −6.3 to −4.4) and −3.0 (95% CI, −3.9 to −2.0) for the CBT and yoga arms, respectively.

Preference Trial:

Preference and selection effects were estimated by combining the data observed in the randomized and preference trials. The preference and selection effects for PSWQ-A were −1.5 (95% CI, −5.3 to 2.3; P = .44) and −1.0 (95% CI, −4.7 to 2.8; P = .62), respectively. The preference and selection effects for PROMIS Anxiety were −0.2 (95% CI, −4.8 to 4.4; P = 0.93) and 0.4 (95% CI, −4.2 to 5.1; P = .85), respectively. The preference and selection effects for ISI were −0.9 (95% CI, −4.7 to 3.0; P = .66) and −0.9 (95% CI, −4.7 to 2.9; P = .65) respectively. The preference and selection effects for attrition from the study were −8.7% (95% CI, −20.0% to 2.7%; P = .13) and 2.9% (95% CI, −8.5% to 14.2%; P = .62), respectively.

Conclusions:

Both CBT and yoga produced declines in worry and anxiety symptoms, with no significant differences between the 2 interventions. CBT was superior to yoga in improving sleep disturbances. Approximately half of participants chose CBT and half chose yoga, and there were neither preference nor selection effects on outcomes. These findings suggest that both CBT and yoga may be useful approaches for worry in older adults and may be suggested by clinicians without a strong preference for one vs the other except for those with sleep problems, for whom CBT may show a greater improvement than yoga.

Limitations:

Limitations include that participants had to agree to be randomly assigned to either the preference trial or randomized trial, the differences in the structure of the interventions, and the homogeneous (primarily White, well-educated women) sample.

Impact of Late-Life Worry

Anxiety consists of physiological, cognitive, and behavioral symptoms, and worry is a cognitive symptom of anxiety. It is most commonly defined as an uncontrollable verbal process that consists of trying to solve a problem but assumes negative outcomes and is associated with negative affect.¹ Worry is common, with prevalence rates as high as 45%.² Among older adults, worry is associated with many negative outcomes, including anxiety, cognitive difficulties, depression, disability, increased health care use, coexistent medical problems, decreased quality of life (QOL), and poor sleep.^3-10

Rationale for Cognitive-Behavioral Therapy

Our rationale for choosing cognitive-behavioral therapy (CBT) as a comparator was based on feedback from participants in our previous randomized controlled trial (RCT), who reported they thought it should be included in future studies. CBT is the most efficacious nonpharmacological treatment for worry¹¹ and has the strongest evidence base for treating late-life worry and related symptoms.¹² We have demonstrated that CBT is superior to enhanced usual care for the treatment of late-life anxiety disorders.¹³ Before this study, we conducted an RCT comparing CBT with the active comparison condition of supportive therapy. We demonstrated that CBT was superior to supportive therapy in reducing worry, anxiety symptoms, depressive symptoms, and sleep problems; most improvements were maintained up to 1 year after completing treatment.^14,15

Rationale for Yoga

We considered adding yoga as an intervention for worry because participants in our previous study were interested in this option. Yoga may be an attractive and popular option for addressing worry because it is nonpharmacological and has minimal adverse effects.^16,17 Research has shown that, in experienced yoga practitioners, γ-aminobutyric acid (GABA; a neurotransmitter that decreases sympathetic nervous system activity) levels in the brain increase after a yoga session; this finding suggests that the practice of yoga should be explored as a treatment for disorders with low GABA levels, such as anxiety disorders.¹⁸ Yoga is highly accessible in most communities, affordable, feasible to offer,¹⁹ and widely used by an increasing number of people in the United States.^20,21 Data from the 2012 National Health Interview Survey (N = 34 525) revealed that for US adults, lifetime and 12-month prevalence of yoga use were 13.2% and 8.9%, respectively. Translated into total numbers, approximately 31 million US adults have ever practiced yoga, and approximately 21 million have practiced it in the past 12 months. For adults aged ≥65 years, lifetime and 12-month prevalence of yoga use were also substantial at 9.3% and 7.2%, respectively. To our knowledge, prior studies of yoga have not focused specifically on possible effects on worry. Yoga reduces symptoms of anxiety (worry is a major component of anxiety),²² including reductions in self-reported stress and anxiety.^23-25 Several recent randomized studies have reported decreased anxiety for participants assigned to yoga compared with control groups; several of these studies also reported improvements in depressive symptoms and sleep as well.^26-28 One review found that >70% of studies reported a significant decrease in anxiety and stress symptoms when a yoga intervention was implemented.¹⁷ Another more recent review found beneficial effects of yoga on both anxiety (in those with subclinical levels of anxiety symptoms) and depression.²⁹ Further, adherence to yoga interventions was high, and the interventions were generally easy to practice and maintain.¹⁷ In summary, data suggest that yoga reduces anxiety¹⁷ and has beneficial effects on psychological and physiological measures of stress.³⁰ Thus, yoga has emerged as a promising modality for decreasing worry symptoms.

We gave careful consideration to the types of yoga that would be most appropriate for both older adults and people experiencing significant levels of worry/anxiety.¹⁶ For anxiety, gentle or restorative yoga classes have been recommended to help quiet the mind and relax the body by linking gentle physical movement to the rhythm of breathing.³¹ For the target population of worried older adults, we selected a gentle yoga class with a strong emphasis on breathing and relaxation.

Gaps in Evidence

Worry is the cardinal symptom of generalized anxiety disorder (GAD). Benzodiazepines and selective serotonin reuptake inhibitors (SSRIs) are the primary pharmacological treatments for GAD. However, both classes of medications are associated with serious adverse effects for older adults,^32-35 and older adults prefer psychotherapy over pharmacotherapy for the treatment of anxiety.³⁶ Alternatives to pharmacotherapy for the treatment of late-life worry (and anxiety) are needed. CBT is superior to enhanced usual care and supportive therapy for treating late-life GAD.^13,37 Yoga reduces anxiety^{17,22,24,25,38-43} and may be especially appealing to older adults because it does not carry the same potential stigma as psychological care. However, there have been no comparative effectiveness studies of CBT and yoga for improving worry, anxiety, or sleep in older adults.

Despite the strong emphasis on patient preferences and choice in health care and shared decision-making, it remains unclear whether promoting informed choice in health care also leads to improvements in patient health or QOL. RCTs are considered the gold standard of research studies as they provide strong control for threats to internal validity. However, randomization to treatment introduces threats to validity by ignoring patient preference.⁴⁴ Such threats include an enhancement of placebo effects, decreased motivation to engage in a less-preferred treatment leading to differential attrition, and response bias.⁴⁴ Preference effects may be stronger in unblinded studies, such as those testing behavioral interventions, where participants know which treatment they are receiving.⁴⁵

In addition to the potential impact on validity, participant preference is important in clinical trials because it is a key component of shared decision-making and best-practice standards in routine clinical care.⁴⁶ Further, in the treatment of anxiety and depression, multiple efficacious treatment options exist to reduce symptoms of anxiety and depression, including psychotherapy, medication, physical activity, and mindfulness-based practices. Thus, in clinical practice, patients may be presented with multiple evidence-based options for treatment, making it important to better understand how and why they indicate treatment preference. Understanding the factors associated with preference may help providers in their framing of treatment options.

Preference is related to treatment outcomes in many ways. First, receipt of preferred treatment has been associated with a small improvement in clinical outcomes,⁴⁷ particularly in trials with mental health outcomes.⁴⁸ It is also associated with decreased rates of attrition, increased rates of intervention session attendance, and higher patient satisfaction.^47-50 Finally, receipt of a nonpreferred treatment can lead to negative placebo-like effects and interfere with the estimation of true treatment effects.^48,51,52

Significance

Specific Aims

The primary aim of this study was to compare the effects of 2 interventions, CBT and yoga, on worry in older adults (≥60 years). The secondary aims of this study were to compare the effects of CBT and yoga on anxiety and sleep. The exploratory aims of this study were to (1) determine participant preference for CBT vs yoga; (2) examine participant preference effects on worry, anxiety, sleep, adherence to intervention, and attrition rates; and (3) examine selection effects on worry, anxiety, sleep, adherence to intervention, and attrition rates.

Study Overview

We implemented a 2-stage randomized preference trial⁵⁸ comparing CBT with yoga for the treatment of worry in a sample of older adults (≥60 years) (see Figure 1). Five hundred participants were randomly assigned to either the preference trial (participants chose the intervention; n = 250) or to the randomized trial (participants were randomly assigned to 1 of the 2 interventions; n = 250). After randomization, intervention preference was assessed only in participants randomly assigned to the preference trial. The randomized trial and the preference trial were identical in all other respects (Figure 1). Participants received 10 weeks of 1 of the 2 interventions (CBT or yoga). Assessments were conducted at baseline (week 0), midintervention (week 6), immediately on completing the intervention (week 11), and 6 months after completing the intervention (week 37). CBT sessions were conducted by telephone and lasted approximately 45 to 50 minutes (1×/week; 10 sessions total). Yoga consisted of 10 weeks of gentle yoga classes (2×/week; 20 classes total).

Figure 1

Study Design.

The primary aim was to compare the effects of CBT and yoga on worry in older adults (as assessed by the Penn State Worry Questionnaire-Abbreviated [PSWQ-A] measured postintervention, week 11). Secondary aims were to compare the effects of these interventions on anxiety and sleep measured postintervention (as assessed by the PROMIS® Anxiety and Insomnia Severity Index [ISI] at week 11). Exploratory aims were to determine participant preference for CBT vs yoga, and to examine participant preference effects and selection effects on worry, anxiety, sleep, adherence to intervention, and attrition rates. This study design allowed for the estimation of traditional intervention effects (differences in outcomes between participants randomly assigned to CBT or yoga), preference effects, and selection effects. Preference and selection effects are described in detail below.

Study Design

A randomized preference trial was chosen to determine the relative efficacy of CBT and yoga on worry in older adults and the effects of intervention preference on outcomes and how preference may affect attrition. To understand the effect of choice on intervention outcomes, we needed to disentangle the direct effect of intervention from the preference and selection effects. The preference effect can be thought of as the average effect for those who received their preferred intervention (regardless of whether it was CBT or yoga) minus the average for those who did not receive their preferred intervention (regardless of the intervention). For those who did not receive their preferred intervention, the average effect is estimated in the randomized trial. The selection effect addresses the question of whether there is a benefit to getting to select one intervention over the other, and it measures the effect on outcomes of self-selection to a specific intervention (see formulas below). The traditional RCT design does not provide a way to estimate these effects; they are masked in the overall intervention effect.

These effects are not separated in choice trials either, and the intervention may affect the estimation of preference and selection effects. The 2-stage randomized trial design is best suited for providing separate estimates of intervention, preference, and selection effects. In the first stage, participants are randomly assigned to either a randomized trial or a preference trial. In the randomized trial, participants are randomly assigned to one or the other intervention, whereas in the preference trial, participants can choose their preferred intervention. Intervention effects are estimated in the randomized trial as is customary for RCTs. The preference and selection effects are estimated by combining the data collected in the preference and randomized trials.^59,60 Walter et al⁵⁸ showed that unbiased estimates of the selection and preference effect sizes are given by $\widehat{SE}=\frac{m_1({\widehat{\mu }}_{11}-{\widehat{\mu }}_1)-m_2({\widehat{\mu }}_{22}-{\widehat{\mu }}_2)}{2\widehat{\phi }(1-\widehat{\phi })m}$ and $\widehat{PE}=\frac{m_1({\widehat{\mu }}_{11}-{\widehat{\mu }}_1)+m_2({\widehat{\mu }}_{22}-{\widehat{\mu }}_2)}{2\widehat{\phi }(1-\widehat{\phi })m}$, respectively, where ${\widehat{\mu }}_{11}$ and ${\widehat{\mu }}_{22}$ represent the estimated means of the outcome (eg, PSWQ-A) of the yoga and CBT intervention groups in the preference trial; ${\widehat{\mu }}_1$ and ${\widehat{\mu }}_2$, the estimated mean of each intervention group in the random group; m₁, the number of participants in the preference group who select 1 intervention (eg, yoga); m₂, the number of participants in this arm who select the other intervention; and m=m₁+m₂ is the total number of participants randomly assigned to the preference group. The estimated preference rate ($\widehat{\phi }$) for a specific intervention is estimated in the preference group as $\widehat{\phi }=\frac{m_1}{m_1+m_2}$.

In the special case where m₁ = m₂ (in our design, m₁ = 130 and m₂ = 120), $\widehat{SE}=({\widehat{\mu }}_{11}-{\widehat{\mu }}_1)-({\widehat{\mu }}_{22}-{\widehat{\mu }}_2)=({\widehat{\mu }}_{11}-{\widehat{\mu }}_{22})-({\widehat{\mu }}_1-{\widehat{\mu }}_2)$ and $\widehat{PE}=({\widehat{\mu }}_{11}-{\widehat{\mu }}_1)+({\widehat{\mu }}_{22}-{\widehat{\mu }}_2)=({\widehat{\mu }}_{11}+{\widehat{\mu }}_{22})-({\widehat{\mu }}_1+{\widehat{\mu }}_2)$. From these equations, it can be seen that the selection effect can be rewritten as the difference between preference means, subtracting the analogous difference observed under randomization, with the whole quantity representing the effect of self-selection to a particular intervention. In contrast, the preference effect compares the means in the preference study with those observed in the randomized study, representing a contrast between those who chose their intervention and those who were randomly assigned.

Study Setting

Participants

As the primary aim of this study was to compare the effects of CBT and yoga on worry in older adults, participants consisted of worried older adults. Recruitment was conducted through our collaborative partners at WFBH (clinics detailed under “Recruitment Sites”) to yield a heterogeneous sample. For recruitment at non-WFBH sites, we developed recruitment flyers and brochures with stakeholder input. These materials were posted and distributed throughout the community. We attended community events to distribute flyers, advertised in the Volunteers in Touch with an Active Lifestyle newsletter (a twice yearly newsletter sent to almost 10 000 older adults interested in research participation), ran articles in local magazines and the local newspaper, and distributed postcards via voter registration lists in 2 counties for adults aged ≥60 years.

Interventions and Comparators or Controls

CBT Intervention

CBT consisted of 10 individual weekly 45- to 50-minute psychotherapy sessions conducted by telephone with 1 of 2 study therapists (referred to after this point as a study coach) and an accompanying workbook given to participants. We have used this intervention in 2 previous RCTs (NIH/NIMH R01 MH083664 and K23MH065281, Dr Brenes, principal investigator). The 10-chapter workbook focuses on techniques that have demonstrated efficacy in treating adults with GAD⁶² and older adults with GAD.^13,14,63-65 Chapter 1 describes the intervention and presents a cognitive-behavioral model of worry. The remaining chapters address a specific worry-management technique or a specific problem that may be comorbid with worry, as well as relapse prevention (see Table 1 for a description of the workbook contents). This workbook, which was previously adapted for use with older adults, includes techniques that have been shown to be beneficial for older adults.^24,25,58-60 Techniques that are more applicable to younger or middle-aged adults (such as assertiveness and time management) were replaced with chapters that are more applicable to older adults (such as pain and sleep management). Further, each chapter contains multiple examples of specific situations that an older adult might experience and is followed by a homework exercise. The study coach discussed experiences with the homework exercises during each subsequent session. Both study coaches were licensed clinical social workers. Our study coaches who provided the CBT intervention were an African American woman and a White woman, adding diversity to the delivery of the intervention.

Table 1

Content of the CBT Workbook.

Study Outcomes

Table 2 contains a description of the primary outcome measures, secondary outcome measures, exploratory outcome measures and process measures accompanied by the collection schedule, a description of the measures, and references to psychometric properties. The outcomes we collected are common problems reported to be bothersome by older adults. All outcomes are based on self-report measures. Worry is associated with significant impairment and distress, and our previous research has demonstrated improvements in functioning after CBT. Among older adults, worry is associated with anxiety, depression, disability, and poorer sleep.^4,5,7,10 Thus, measures were included to assess these outcomes as well. All outcomes were assessed at baseline (week 0), postintervention (week 11), and 6-month follow-up (week 37). Primary and secondary outcomes were also assessed at midintervention (week 6).

Table 2

Description and Timing of Study Measures.

Further, older adults may experience anxiety differently than younger adults,⁸² and traditional diagnostic classifications do not reflect these differences.^83,84 This difference results in many older adults with moderate to severe worry not meeting full criteria for DSM diagnoses. A minimally important difference (MID) with respect to worry has been defined as a 5.5-point reduction in the PSWQ-A (range, 8-40).^85-87 To our knowledge, no MID is available for between-group comparisons.

Sample Size Calculations and Power

In this intention-to-treat (ITT) design, all individuals in the randomized trial were included in the primary analyses. In addition to the intervention effect, the proposed 2-stage randomized design allows for the estimation of the preference and selection effects. As described below, a contrast within the framework of a constrained mixed model for randomized trials was used to test the primary null hypothesis of no intervention effect at the postintervention assessment visit at week 11. This analysis was performed in the subset of participants who were randomly assigned to the randomized trial. The detectable effect size was calculated for the test of equality of PSWQ-A means at the postintervention assessment visit (week 11) using the 2-sample t test power formula appropriate for analysis of covariance (ANCOVA). As explained below, use of the midintervention week (week 6) measurement within the constrained mixed model will help to account for missing outcomes at the postrandomization visit. The power formula for ANCOVA uses the variance of the outcome, conditioned on the baseline value. This conditional variance is a function of (1 − r²), where r is the correlation between the baseline and follow-up measurement. Sample size and detectable effect sizes were estimated over a range of possible correlations between the baseline and follow-up PSWQ-A measurements and assuming an SD of 5.6 based on our prior data. Preliminary data that informed the calculations came from various sources, including data from our previous studies and published reports of intervention effect sizes from similar studies conducted with change in overall PSWQ-A score as the outcome in aging populations.^13,37,85 We allowed the correlation between baseline and the week 11 follow-up standardized effect size measurement to vary between 0.30 and 0.55 and explored power for effect sizes between 0.20 and 0.40 SDs. Table 3 shows the achievable power depending on the intervention effect size for each level of correlation between the baseline and follow-up PSWQ-A assessments, assuming a 2-sided significance level of α = .05.

Table 3

Achievable Power Relative to Detectable Effect Size and Longitudinal Correlation, With n = 250 (125 Per Arm) Individuals Randomly Assigned to the Random Group.

Per Table 3, assuming a significance level of α = .05 and a correlation between baseline and follow-up scores of 0.5, the study was designed to have approximately 90% power to detect intervention effect sizes of 0.35σ, which corresponds to a PSWQ-A score difference of 2.0 between individuals who were randomly assigned to the CBT and yoga arms. Equivalently, because the 2 arms of the randomized trial should have equal means at baseline, the proposed comparison would have close to 90% power to detect a difference of 2.0 in change from baseline to the postintervention measure (week 11). In our prior RCT of late-life GAD,¹⁴ the observed correlation estimate between the baseline and follow-up PSWQ-A score was 0.51 at 16 weeks postrandomization and 0.45 after a follow-up of 12 months. These estimates suggested that that the correlation between the baseline and week 11 measurement would likely be >0.5, which would result in stronger statistical power. Therefore, under the original assumptions, the study would be adequately powered to detect medium standardized effect sizes that, according to Cohen,⁸⁸ can range between 0.20 and 0.50. We also note that much larger effect sizes have been reported in the literature. For example, in a study conducted among older adults with a similar sample size, Stanley et al⁸⁵ reported an effect size of 0.85σ at the 3-month follow-up visit with changes in PSWQ (full measure of the PSWQ-A) worry scores of −7.7 in their CBT arm vs −3.2 in the enhanced usual care arm. The sample size of 250 participants in the randomized trial would maintain at least 80% power to detect the same effect size, 0.35σ, for dropout rates as high as 20%.

As mentioned previously, the 2-stage trial design allows for the estimation of the preference and selection effects (see the “Exploratory Aims: Preference and Selection Effects” section). The additional 250 participants in the preference trial provide the data necessary for estimating those effects. The estimation of the statistical power to detect these effects assumed a total sample size of 500 individuals (250 in the preference trial and 250 in the randomized trial). The randomized trial contributes in the estimation of these effects through the randomization performed in the first stage (preference vs randomized trials),⁵⁸ and the expected equal distribution of preferences in the 2 arms of the randomized trial. Based on the power estimation approach described in Turner et al,⁸⁹ Table 4 shows the achievable power for various combinations of selection and preference effect sizes.

Table 4

Achievable Power and Detectable Preference and Selection Effect Sizes, With N = 500 Individuals Assuming an Equal Preference for Intervention (ϕ = 0.5).

This power estimation also assumed a significance level of α = .05. The first number in each cell of Table 4 represents the achievable power for detecting the corresponding preference effect size; the second number shows the power for the selection effect. The preference and selection effect sizes have been standardized (ie, estimates are provided assuming a standard error of 1); therefore, the first cell suggested that we would have 71% and 83% power, respectively, to detect a preference and a selection effect size of 0.2 SD, assuming the proportion of study participants who prefer CBT to yoga was around 50%. Overall, Table 4 shows that we would have at least 80% power to detect a preference effect size of at least 0.35σ and a selection effect size of at least 0.40σ. The power to detect preference effect sizes of 0.3σ and higher is always >90%, independent of the detectable selection effect size. In summary, the power analyses showed that the originally proposed sample size of 500 individuals (125 in each of the 4 arms) would provide approximately 90% power to detect an overall intervention effect of 0.35σ, at least 90% power to detect preference effect sizes of 0.35σ and higher, and at least 80% to detect selection effect sizes of 0.4σ and higher.

Data Collection and Sources

Analytical and Statistical Approaches

Analyses of the primary outcome began by examining descriptive statistics (means; SDs; minima; quartiles 1, 2, and 3; and maxima) and plots of the data (histograms for data measured only once and changes in variables that were measured twice) to become familiar with the data and to examine it for outliers as well as for the necessity of data transformation. Simple associations between variables were estimated using the Spearman rank correlation coefficient. The primary analysis approach was prespecified before unblinding the statisticians to intervention groups. Diagnostic methods were used to ensure that model assumptions were met. The intervention effect for the primary aim was estimated by comparing mean PSWQ-A scores between CBT and yoga groups in the random group (N = 250, with 125 per group) using constrained mixed-model repeated measures ANCOVA with an unstructured covariance matrix to account for the fact that the multiple measurements at baseline (week 0), midintervention (week 6), and postintervention (week 11) from participants were not independent. The model contained terms for baseline psychotropic medication use (yes/no; used to stratify randomization), sex and race (race dichotomized to White vs other), and intervention effects that were specific to each follow-up time. Because this was a randomized trial, we constrained the prerandomization intervention-specific outcome means to be the same.^90,91 For randomized trials, constrained mixed models can provide more efficient estimates of postrandomization intervention differences when either baseline or postrandomization measures are missing. A statistical contrast was used to test the primary hypothesis at the postintervention (week 11) time point using a 2-sided α = .05 significance level. For this model, estimation of an intervention effect using a contrast to compare intervention means at week 11 provides the same estimate as is obtained by taking a difference of changes in means from baseline. In the primary analysis, all randomly assigned participants were included in their original study group for analysis regardless of the final mode of intervention or the extent of compliance with the study protocol; that is, the primary analysis followed an ITT philosophy. As descriptive information, the proportion of participants achieving minimally important changes was calculated within intervention groups, and CIs for binomial proportions were used to place 95% CIs on both the within-intervention group percentage achieving the MID and the difference between these proportions.

The 2 secondary end points (PROMIS Anxiety, ISI) were analyzed with the same forms of mixed models that we used for the primary end point, whereas attrition rates at week 11 were analyzed using logistic regression. Many articles have addressed the appropriate use of secondary outcomes and analyses in clinical trials. Experts do not agree on the type I error level, or even whether secondary end points should be tested when the primary end point is not statistically significant.^92-95 Similarly, there is no consensus on reporting of subgroup analyses from randomized trials. One recommendation by Wang et al⁹⁶ is to calculate and report the overall probability of type I error given the number of subgroups that have been tested. Given that we view our subgroup analyses as providing additional evidence for understanding primary outcome results, we followed the recommendations of Wang et al⁹⁶ and calculated/reported the probability of type I error given the number of subgroups tested.

As mentioned previously, estimation of preference and selection effects (exploratory aims) was based on the complete sample using data collected in both arms (preference and random) of the trial. Therefore, these analyses were based on a sample size of 500 individuals. The mixed-model repeated measures framework was used to estimate the selection and preference effects. Dummy variables were created to identify participants' membership in the random and preference groups, intervention assignment in the random group, and intervention preference in the preference group. The adjusted means and variance-covariance matrix needed to compute these effects and their standard error were estimated from the fitted model. The standard error associated with the preference and selection effects was derived using formulas provided by Walter et al⁹⁷ (see equations 4 and 12 in that article).

Almost all biomedical research must deal with issues related to missing observations. For participants lost to follow-up, we used all available information until the loss to follow-up. If loss to follow-up is related to the level of the unobserved missing outcome (often termed missing not at random [MNAR]), results can be somewhat biased. Our primary analytical models described previously used maximum likelihood estimation within the framework of a constrained mixed model, which provided a valid approach for handling missing data if they were considered to be missing at random (MAR).^98,99 Under the MAR assumption, the likelihood of a missing outcome may depend on observed covariates or other outcomes, but not on unobserved outcomes. Following the recommendations of Little and Rubin,¹⁰⁰ we performed a sensitivity analysis that included as predictors those variables determined to predict loss to follow-up in this study to determine the robustness of the models that assume outcomes are MAR, as MAR is a nonverifiable assumption. To explore the possible effect of deviations from MAR, one must assume that informative censoring has occurred. For example, biased estimates can result if participants with adverse experiences are more likely to withdraw (or, conversely, tend to be relatively less likely to withdraw), while those participants are also at higher risk for the noneffectiveness of the interventions. A growing body of literature describes approaches that explicitly model the censoring mechanisms^101-103 and pattern-mixture models.¹⁰⁴ We analyzed the data incorporating varying assumptions about the missing observations. This provided useful information about limitations in the ability to interpret results in the presence of informative censoring.

The investigation of the effect of missing data on the results was considered a secondary “sensitivity” analysis, with the primary analysis being the mixed-model repeated measures ANCOVA (an approach that accommodated a MAR assumption and was consistent with ITT¹⁰⁵). Sensitivity analyses to missing outcome data were performed for the primary (PSWQ-A) and secondary (PROMIS Anxiety T-score, ISI) outcomes. In addition, all subgroup analyses for the PSWQ-A were run on multiply imputed data sets. Two approaches (models 1 and 2, described below) were used for multiple imputation (MI), and 10 imputed data sets were used for each.

MI model 1 used Markov chain Monte Carlo (MCMC) imputation in SAS PROC MI to initially create monotone missing data (ie, impute for intermittent missing outcomes among those not lost to follow-up) and then subsequently used monotone regression-based imputation to handle missing data due to loss to follow-up. The imputation model performed imputation within intervention groups separately. Subsequently, constrained mixed models were fit to each MI data set. SAS PROC MIANALYZE was used to obtain the overall intervention effect (and associated 95% CI and P values) across imputed data sets. In addition to prior measures of the outcome, the following baseline variables were used as predictors: sex, race, age, baseline psychotropic medication use, depressive symptoms, college or higher education, and current employment. This imputation approach would be classified as accounting for a MAR mechanism because it depends only on observed information (either covariates or previously observed outcomes).

MI model 2 imputed all follow-up missing observations using only baseline information and subsequently offset the mean of imputed variables to be approximately equal to the baseline mean of the outcome variable. All imputation was performed in SAS PROC MI using monotone regression, with the baseline measure of the outcome and the following baseline variables used as predictors: sex, race, age, baseline psychotropic medication use, depressive symptoms, college or higher education, and current employment. Constrained mixed models were fit to each MI data set and SAS PROC MIANALYZE was used to obtain the overall intervention effect (and associated 95% CI and P values) across imputed data sets. This imputation approach would be classified as accounting for an MNAR mechanism (ie, the mechanism that governs missing outcomes depends on unobserved observations) and assumes that individuals with missing outcomes revert to baseline outcome levels.

Based on site demographics, we expected that the sample would be mostly female (65.7%), and that 20.6% of the sample would be racial/ethnic minorities. Therefore, it was informative to describe the intervention effect in these subgroups. The prespecified subgroups used in the analysis were defined by age (≤80 years, >80 years), use of psychotropic medications, and self-reported depression diagnosis (yes/no). Because of sparsity of participants in the >80-years-old group, a post hoc grouping was formed for age (≤70 years, >70 years). Formally, differences in intervention effects between subgroups were tested using a series of models in which we tested for interaction between intervention and subgroup within the randomized study. We added the subgroup and the subgroup-by-intervention interaction terms at each time point to the prespecified model for the primary outcome, and then we used a contrast to test the interaction at that time point. This approach determined whether there were differences in the intervention's efficacy among subgroups, and it provided the tools to describe it adequately.

Participant Information and Recruitment

Figure 2 displays participant flow from screening through study follow-up. Table 5 displays the baseline characteristics of the 500 randomized participants. Ascertainment of reasons for ineligibility was completed by phone and through baseline PSWQ-A questionnaires. Reasons for ineligibility are shown in Figure 2. The majority of participants were female (86.6%) and White (78.8%) with an average (SD) age of 66.5 (5.2) years and were highly educated (54.6% had completed a Bachelor's degree or higher). Most participants were either married or living with a partner (52.8%) and living in a household with 2 individuals (50.8%). Participants were more likely to have never smoked (57.8%), and 43.8% of them were taking at least 1 psychotropic medication. Participant characteristics were, by design, not different between the preference and randomized trials, nor between CBT and yoga within the randomized trial. Within the preference trial, those who chose yoga tended to be younger than those who selected CBT, with mean (SD) ages of 65.6 (4.3) and 67.4 (5.7) years, respectively (P = .004). About 52% of participants in the preference trial chose yoga; with 250 participants randomly assigned to the preference trial, this proportion was not significantly different from 50% (P = .53; exploratory aim 1).

Figure 2

CONSORT Diagram.

Table 5

Baseline Characteristics of Randomly Assigned Participants.

The baseline distributions of the primary, secondary, and exploratory outcomes and process measures are shown in Tables 6a, 6b, and 6c. The study included only participants with a PSWQ-A score ≥26, resulting in baseline outcome scores that were high in both trials: mean PSWQ-A was 32 (4.3); mean PROMIS Anxiety T-score was 65.2 (6.2); and mean ISI score was 13.4 (6.4). The distributions of these outcomes were comparable between the 2 trials. Reasons for missing outcomes are included in Table 7. The number of primary outcomes at week 11 within the randomized trial was 207 (101 within CBT and 106 within yoga) and within the preference trial was 220 (104 within CBT and 116 within yoga; see Figure 2).

Table 6a

Baseline Primary and Secondary Outcomes.

Table 6b

Baseline Exploratory Outcomes.

Table 6c

Process Measures.

Table 7

Reasons for Withdrawal/Missing Data Before Week 11.

Primary Outcome

The randomized trial included 250 participants (125 in CBT, 125 in yoga). The primary outcome was the PSWQ-A measured at week 11. In the randomized trial, outcome assessment was performed at weeks 6, 11, and 37, and, relative to the baseline scores, significant reductions in the primary outcome (Table 8a) were observed in both arms of this trial at each time point. After adjustment for baseline psychotropic medication use, sex, and race, at week 11 a change of −8.8 (95% CI, −10.1 to −7.5) was observed among participants randomly assigned to CBT, compared with a change of −7.2 (95% CI, −8.5 to −6.0) among participants randomly assigned to yoga. From this model, the intervention effect on follow-up PSWQ-A means of yoga compared with CBT at week 11 was 1.6 (95% CI, −0.2 to 3.3; P = .08), indicating that the 2 interventions were not statistically different (primary aim). A MID for the PSWQ-A has been defined as a 5.5-point decrease in the score.^85-87 Participants randomly assigned to CBT had a 68.5% chance of achieving this MID (95% CI, 59.4%-77.7%), whereas participants randomly assigned to yoga had a 56.5% chance of achieving this MID (95% CI, 46.9%-66.0%), for an intervention effect of 12.1% (95% CI, −1.2% to 25.4%). Results were similar at week 37, with greater reduction from the baseline scores observed in the later assessments in both arms of this trial. The mean PSWQ-A score dropped from 31.2 at baseline to 18.7 and 18.8 at week 37 among participants randomly assigned to CBT and yoga, respectively. The adjusted intervention effect on follow-up means was 0.1 (95% CI, −1.7 to 2.0; P = .90).

Table 8a

Primary and Secondary Outcomes—Results from the Randomized Trial.

Secondary Outcomes

Secondary outcomes (Table 8a) were assessed at weeks 11 and 37 postrandomization. After adjustment for baseline psychotropic medication use, sex, and race, the standardized PROMIS Anxiety T-scores were improved in both intervention groups, with reductions at week 11 of −7.5 (95% CI, −8.8 to −6.1) and −7.1 (95% CI, −8.5 to −5.8) for CBT and yoga, respectively, yielding an intervention effect on follow-up means of 0.3 (95% CI, −1.5 to 2.2; P = .71). Further changes from the baseline mean score were observed at week 37, −9.9 (95% CI, −11.5 to −8.3) for CBT, relative to −11.1 (95% CI, −12.6 to −9.6) for yoga. The intervention effect on week 37 means was −1.2 (95% CI, −3.3 to 1.0). These results suggest that the 2 interventions were not statistically different. However, participants randomly assigned to CBT did experience a greater reduction in ISI at week 11, but the effects dissipated by week 37. Week 11 changes from baseline mean ISI scores were −5.4 (95% CI, −6.3 to −4.4) for CBT participants vs −3.0 (95% CI, −3.9 to −2.0) for yoga participants, for an intervention effect on follow-up means of 2.4 (95% CI, 1.2-3.7; P < .01), with those randomly assigned to CBT showing the largest reduction in the score. At week 37, the intervention effect on follow-up means dropped to 0.9 (95% CI, −0.5 to 2.2; P = .21).

A MID for PROMIS Anxiety has been defined as a 3-point decrease in the score.¹⁰⁶ Participants randomly assigned to CBT and yoga had a 73.3% chance (95% CI, 64.5%-82.2%) and a 70.8% chance (95% CI, 61.9%-79.6%) of achieving this MID, respectively, for an intervention effect of 2.6% (95% CI, −10.0% to 15.2%). For the ISI, a MID has been defined as a 6-point increase in this score.¹⁰⁷ Participants randomly assigned to CBT and yoga had a 49.6% chance (95% CI, 39.5%-59.7%) and a 26.7% chance (95% CI, 18.0%-35.3%) of achieving this MID, respectively, for an intervention effect of 22.9% (95% CI, 9.7%-36.2%).

Exploratory Outcomes

Exploratory outcomes (Table 8b) were assessed at weeks 11 and 37 postrandomization. Participants randomly assigned to CBT experienced a greater reduction in PROMIS Sleep Disturbance, Pain Interference, and Pain Intensity scores at week 11, with differences between interventions becoming nonsignificant at week 37. Mean week 11 changes from baseline for Sleep Disturbance scores were −6.5 (95% CI, −7.7 to −5.2) for CBT vs 3.9 (95% CI, −5.1 to −2.7) for yoga participants, for an intervention effect on follow-up means of 2.6 (95% CI, 0.9-4.3; P < .01), with those randomly assigned to CBT showing the largest reduction in the score. At week 37, the intervention effect on follow-up means dropped to 0.5 (95% CI, −1.2 to 2.2; P = .58). For pain interference, week 11 changes in means from baseline were −2.6 (95% CI, −4.1 to −1.0) for CBT participants, compared with −0.1 (95% CI, −1.6 to 1.5) for yoga participants, for a week 11 adjusted intervention effect of 2.5 (95% CI, 0.5-4.6; P = .016), which dropped to 1.6 (95% CI, −0.6 to 3.8; P = .14) at week 37. Similar results were observed with pain intensity, where the adjusted intervention effect on follow-up means was 0.7 (95% CI, 0.2-1.3; P < .01) at week 11, but the effect was no longer significant at week 37.

Table 8b

Exploratory Outcomes—Results from the Randomized Trial.

Process Measures

Results for the process measures are presented in Table 8c. There was a statistically significant difference in the adherence to the intervention between those randomly assigned to CBT and those randomly assigned to yoga. Among CBT participants, the adherence rate was 76.4% (95% CI, 70.2%-82.6%) compared with 60.4% (95% CI, 53.3%-67.4%) among those randomly assigned to yoga, for an intervention effect of −16.0% (95% CI, −25.4% to −6.7%; P < 0.01). Attrition rates were not statistically different in the 2 arms of the randomized trial. At week 11, the attrition rate (percentage of participants who did not complete either of the week 6 or week 11 assessment) was 16% (95% CI, 9.5%-22.5%) among participants randomly assigned to CBT, compared with 12.0% (95% CI, 6.2%-17.8%) among those randomly assigned to yoga. The intervention effect on attrition was −4.0% (95% CI, −12.6% to 4.7%; P = .36).

Table 8c

Process Measures—Results from the Randomized Trial.

Exploratory Aims: Preference and Selection Effects

In the preference trial, the preference rate for yoga was 0.52 (95% CI, 0.46-0.58; exploratory aim 1). This rate was not statistically different than 0.5; the 95% CI for the difference ranged from −0.04 to 0.08, P = .6, which suggests that there was no preference for one intervention over the other. Preference and selection effects (exploratory aims 2 and 3) were estimated by combining the data observed in the randomized and preference trials (Table 9). The week 11 preference and selection effects for PSWQ-A were −1.5 (95% CI, −5.3 to 2.3; P = .44) and −1.0 (95% CI, −4.7 to 2.8; P = .62). There were no statistically significant preference and selection effects for either of the secondary outcomes. The preference and selection effects for adherence were 10.4% (95% CI, −2.1% to 22.9%; P = .10) and −6.5% (95% CI, −19.0% to 6.1%; P = .31), respectively. These results suggest a trend toward better adherence among participants who chose their preferred intervention; however, the preference effect was not statistically significant. The attrition preference and selection effects were −8.7% (95% CI, −20.0% to 2.7%; P = .13) and 2.9% (95% CI, −8.5% to 14.2%; P = .62), respectively.

Table 9

Preference and Selection Effects for the Primary and Secondary Outcomes.

Subgroup Analyses

Subgroup analyses (Figure 3) revealed greater reduction in the PSWQ-A scores in individuals with a self-reported diagnosis of depression (relative to those with no such diagnosis) who were randomly assigned to CBT compared with those who received yoga. At week 11, among participants randomly assigned to yoga, the mean PSWQ-A score was 23.1 (95% CI, 20.9-25.2) for those with no depression diagnosis and 24.9 for those with a depression diagnosis (95% CI, 22.6-27.2); these means were 23.1 (95% CI, 20.9-25.4) and 20.8 (95% CI, 18.5-24.7), respectively, among participants randomly assigned to CBT. The adjusted intervention effects (yoga minus CBT) on week 11 follow-up means were −0.1 (95% CI, −2.4 to 2.3) for those with no depression diagnosis and 4.1 (95% CI, 1.6-6.6) for those with a depression diagnosis, with an interaction effect P = .02. Additional subgroup analyses by age group (post hoc using 60-69 years vs ≥70 years due to low recruitment in the prespecified subgroup of ≥80 years), psychotropic medication use (yes vs no), sex (male vs female), and race (White vs other racial/ethnic groups) did not show statistically significant differential effects. Given that there were 5 subgroups tested each at the α = .05 level, the type I error for subgroup analyses, assuming independence between measurements, would be 0.226.

Figure 3

Subgroup Outcomes for the Week 11 PSWQ-A Scores From the RCT.

Sensitivity Analyses

In a post hoc sensitivity analysis, we implemented the covariate adjustment procedure of Cochran¹⁰⁸ described in Marcus et al¹⁰⁹ to estimate the causal effect of randomization vs preference. Limiting ourselves to those covariates that we tested between preference and randomization groups at baseline, this approach amounted to adding a covariate for baseline age (the only covariate that was different in the preference trial between those who preferred CBT and those who preferred yoga) to the prespecified covariates when estimating the preference and selection effects. Table 10 provides these results and illustrates little difference between the unadjusted and adjusted results, providing some evidence that conclusions from unadjusted analyses held up even after adjusting for age differences between those who preferred CBT vs yoga.

Table 10

Causal Inference for the Selection and Preference Effects on the Primary and Secondary Outcomes.

As described previously, sensitivity analyses for missing outcome data were performed using MI. Table 11 contains estimated intervention effects on week 11 follow-up means (and 95% CIs) for the primary and secondary outcomes, using imputed values for missing ones. For comparison purposes, we have once again included the estimates obtained on observed data (see Tables 8a, 8b, and 8c) for each outcome. In comparison with conclusions based on the observed data, we reached similar conclusions under both imputation models. Similarly, Table 12 contains a comparison of subgroup results for the PSWQ-A for the observed data and under both imputation models. Conclusions for subgroup analyses were generally consistent under all approaches, with a slight exception for depression diagnosis where the nominal P value for the interaction increased to P = .06.

Table 11

Comparison of Results for Primary/Secondary Outcomes Under 2 MI Models.

Table 12

Comparison of Subgroup Results for PSWQ-A Under 2 MI Models.

Safety

A total of 52 adverse events were reported throughout the study, as shown in Table 13. Two of these events were possibly related to the intervention, neither of which was a serious adverse event. Both were from participants in the RCT. One CBT participant reported a spontaneous panic attack of mild severity, and 1 yoga participant reported a joint injury of moderate severity at an outcomes assessment.

Table 13

AE Summary.

Subgroup Analyses

Subgroup analyses were conducted to determine whether there were differences in outcomes based on self-reported depression diagnosis (yes vs no), age of ≥70 years (relative to 60-69 years of age), baseline psychotropic medication use (yes vs no), sex (male vs female), and race (White vs other racial/ethnic groups). Participants who had a depression diagnosis and were randomly assigned to CBT, on average, experienced a greater decline in worry severity than participants randomly assigned to yoga. No other subgroup differences were significant.

Study Strengths

This study has many significant strengths. Most notable is the unique randomized preference trial design that allows researchers to compare interventions using a traditional randomized trial design and to examine the effects of participant preference on outcomes of worry. Further, this trial is the largest study to date of both CBT and yoga. Additional strengths include the systematic measurement of intervention adherence and fidelity, adaptation of interventions specifically for older adults, and significant stakeholder involvement.

Study Limitations

Our findings are tempered by some study limitations. Because we had a community-based sample, we may have had a sample biased toward a population that is actively seeking help or wanting to be involved in research efforts. Despite the inclusion of a preference trial, participants still had to be willing to be randomly assigned to the preference trial or the randomized trial, knowing that those assigned to the randomized trial would be told which intervention they would receive. Although we tried to make the structure of interventions as similar as possible, it was important to balance that effort with how the interventions are delivered in the real world. CBT is usually provided once a week, while yoga is often recommended more frequently. Also, yoga was delivered in person, while CBT was delivered by telephone. Because yoga was delivered in group sessions (compared with individually delivered CBT sessions), there could be some cluster effects that were unaccounted for in the analyses. Because only 1 intervention could be considered a cluster design, any effects due to clustering could not be accounted for statistically. That said, the yoga participants in the randomized trial took separate classes from those in the preference trial (to have a clean study design and prevent bias and cross-talk between those who chose to take yoga classes and those who were randomly assigned to them). There may have been intervention-specific barriers. While CBT was offered by telephone to overcome transportation issues, yoga was conducted in person. Yoga offered via telemedicine platforms has recently started to become available but was not offered in this trial.¹¹⁷ Although the locations for the yoga intervention were limited and may not have been convenient to participants, locations were changed throughout the course of the study, and participants could be rescreened for eligibility if a different location was deemed more convenient. Participants could always participate at either of the 2 available locations that fit their time and location needs. That said, we tried to move our availability to different parts of our geographic area to match the zip codes within which we were recruiting at any given time. Because we did not have a no-intervention comparison group, we cannot rule out the possibility of environmental factors impacting outcomes. Finally, the sample consisted largely of well-educated, White women, which may limit the generalizability of findings to other populations. Future research might further examine various yoga approaches to determine whether the type of yoga affects levels of worry (along with anxiety, depression, and sleep). Additionally, future work could compare internet-delivered CBT for worry in older adults with therapist-delivered CBT to determine whether we could make the intervention even more scalable/sustainable.