Mindfulness-Oriented Recovery Enhancement for Veterans and Military Personnel on Long-Term Opioid Therapy for Chronic Pain: A Randomized Clinical Trial

This was a single-blind, parallel, randomized controlled superiority trial. The University of Utah institutional review board approved the protocol. From April 1, 2017, to October 1, 2021, participants were recruited from the Salt Lake City Veterans Affairs Medical Center, the Utah Army National Guard, and the region of the Salt Lake valley, Utah. Participants were recruited based on data extracted from electronic medical records (EMRs) and from physician referrals and advertisements. Following the onset of the COVID-19 pandemic, the trial shifted from an in-person format to a remote format. Eligible participants were U.S. military personnel or veterans age 18 or older with a physician-confirmed, chronic pain–related diagnosis, daily prescription opioid use for ≥3 months, and an average pain rating ≥3 on a 0–10 numerical rating scale. We excluded individuals receiving cancer treatment (because of potential confounding by treatment effects or disease progression), individuals experiencing elevated suicide risk, psychosis, and severe nonopioid substance use disorder (assessed with the Mini-International Neuropsychiatric Interview [11]), and individuals with previous exposure to mindfulness interventions (e.g., mindfulness-based stress reduction). After obtaining informed consent from the participants (which covered EMR data extraction), study staff collected demographic and outcome data, and the in-person cohorts completed a dot-probe task as a measure of opioid cue reactivity. Participants were compensated after each study visit.

A researcher who was not involved in the assessments or analysis used a computerized random number generator to determine treatment allocation to MORE or supportive psychotherapy with a blocked random assignment method (1:1 ratio, with block sizes of 4 to 8). Participants were not allocated by the coordinator until the day of the first treatment session to maintain allocation concealment and prevent bias. Assessments were conducted by staff blinded to group allocation (which remained concealed throughout the study). The allocation list was not accessible to staff involved in study treatments or assessments, and participants were prompted to keep their treatment assignment undisclosed before each assessment.

The study interventions were delivered in eight weekly 2-hour group therapy sessions with 6–12 participants. Sessions were delivered in person until the onset of the COVID-19 pandemic, at which point sessions were implemented through a HIPAA-compliant videoconferencing platform. To control for therapist effects, the same two licensed psychologists conducted an equal number of MORE and supportive psychotherapy sessions.

The manualized MORE intervention (12) provided training in mindfulness, reappraisal, and savoring techniques (N=69 in person; N=47 remote). Mindfulness training entailed mindful breathing and body scan meditations to attenuate pain and opioid craving, by reinterpreting these aversive sensations as innocuous sensory signals, and to self-regulate reactivity to opioid-related cues. Reappraisal training entailed reframing stress appraisals to reduce catastrophizing and negative emotional reactivity, while promoting meaning-making in the face of adversity. Savoring training entailed mindfully focusing attention on pleasant events and pleasurable sensations to boost positive emotions and reduce anhedonia. The psychoeducation component of the intervention addressed opioid misuse and chronic pain. Participants were instructed to complete 15-minute audio-guided mindfulness, reappraisal, and savoring practices each day. Also, before taking each daily opioid dose, participants were instructed to practice a 3-minute mindfulness technique designed to promote opioid sparing (i.e., reduced use of opioids) and help patients delay taking as-needed opioid doses by using mindful breathing to reduce pain and increase self-control over opioid craving and cue reactivity. We defined the minimum intervention dose of MORE (and supportive psychotherapy) as four or more treatment sessions, in accordance with treatment completion thresholds established in previous trials of mindfulness interventions (13, 14).

The active control condition in this trial consisted of supportive psychotherapy, in which therapist-led discussions elicited participants’ thoughts and emotions about coping with chronic pain, opioid misuse, and emotional distress (N=75 in person; N=39 remote). Clinicians encouraged expression of emotions via empathic responding and fostered social support between group members. No skill training or education on mindfulness was provided. To match the homework requirements of the MORE intervention, participants in the supportive psychotherapy group were instructed to journal about themes discussed at weekly therapy sessions for 15 minutes each day. We selected this control condition, which was designed emulate a widely available form of process-oriented, client-centered therapy (15), to control for nonspecific therapeutic factors (e.g., therapeutic relationship and social support). Previous trials of MORE and other mindfulness interventions have validated this control condition and found no significant difference in treatment credibility ratings between mindfulness interventions and supportive psychotherapy (16, 17).

Sessions were audio-recorded, and treatment fidelity was scored with validated measures (18). Adherence and competence scores were excellent, indicating that both manualized protocols were implemented as intended with no treatment diffusion.

Primary and secondary outcomes were collected over an 8-month period, at baseline, after treatment, and then every 2 months for the next 6 months. Our prespecified primary chronic pain outcome was measured with the pain interference and pain severity subscales of the Brief Pain Inventory (BPI) (19). The primary opioid misuse outcome was the Current Opioid Misuse Measure (COMM), a self-reported measure of aberrant drug-related behaviors, including using opioids for reasons other than pain, taking more opioids than prescribed, obtaining opioids from sources other than a prescribing physician, exhibiting signs of intoxication and emotional volatility, and so on (20). We chose this continuous measure as our primary measure of opioid misuse severity, unlike the measurement approach used in our previous trial of MORE (14). In that study, all participants entered the trial with a positive score on a binary measure of opioid misuse, and opioid misuse outcomes were assessed with this binary measure. For the present study of patients on long-term opioid therapy where opioid misuse was not an inclusion criterion, we reasoned that changes in a continuous measure of aberrant drug-related behaviors were clinically meaningful. To triangulate self-reports of aberrant drug-related behaviors, we also performed a clinical assessment of opioid misuse with the Addiction Behaviors Checklist (21), a semistructured interview performed by clinical staff (i.e., psychologists, social workers, and nurses) blinded to treatment assignment. In addition, at each assessment point for the in-person cohort, we performed urine screens, and as an exploratory outcome, we extracted available random urine screen data from EMRs at the 12-month follow-up. Urine screens that were positive for illicit drugs (e.g., heroin, cocaine, methamphetamine) or nonprescribed opioid medications were classified as positive.

Changes in morphine equivalent daily opioid dose were computed in accordance with best practice guidelines (22) as assessed with the timeline followback method (23), and when participants missed follow-up assessments, opioid use was obtained from the EMR.

Other secondary outcome measures included scores on the Depression Anxiety Stress Scale–21 (24), the Posttraumatic Stress Disorder Checklist–Military Version (25), the pain catastrophizing subscale of the Coping Strategies Questionnaire (26), the Snaith-Hamilton Anhedonia and Pleasure Scale (27), and the positive affect subscale of the Positive and Negative Affect Schedule (28). Process measures included the attention to positive information subscale of the Attention to Positive and Negative Information Scale (29), the cognitive reappraisal subscale of the Emotion Regulation Questionnaire (30), the Momentary Savoring Scale (31), the Mindful Reappraisal of Pain Scale (32), and the nonreactivity subscale of the Five Facet Mindfulness Questionnaire (33), which was selected because of its previously demonstrated association with the pain-relieving effects of MORE (16). Opioid craving in daily life was assessed on a 0–10 scale by ecological momentary assessments delivered by smartphone at three random times each day during the 8-week study treatments.

Before the trial switched to a remote format at the onset of the COVID-19 pandemic, opioid cue reactivity was assessed in the laboratory with an opioid dot-probe task designed to measure attentional bias toward opioid-related cues (34). Each trial began with the presentation of a fixation cross (for 500 ms) followed by an opioid-related image and a neutral image, which appeared side by side for either 200 or 2,000 ms. Opioid-related cues included images of opioid pills and pill bottles, which had been validated in previous studies (34). Neutral images were matched to the opioid-related images by visual features, including color, figure-ground relationships, and the presence of human faces. Presentation duration and the left-right position of the images were randomized and counterbalanced within each block of 58 trials. After a 50-ms interstimulus interval, a target probe replaced one of the images. Participants indicated the location of the target by pressing a left or right button, and reaction times were recorded.

Based on our pilot data, a sample size of 200 (after 30% attrition) would provide power greater than 0.90 at an alpha of 0.05 to estimate small clinical effects (Cohen’s d=0.20) from baseline-adjusted treatment effects averaged over four postrandomization time points on the BPI, the COMM, and other continuous outcomes (Cohen’s d values in pilot trials of MORE ranged from 0.50 to 0.84) (16). We planned to enroll 260 patients to account for loss to follow-up; because of the COVID-19 pandemic, the actual number of patients enrolled was 230.

To control for random baseline imbalance between study treatment arms, we used a constrained longitudinal data analysis (cLDA) model in SAS, version 9.4, and Mplus, version 8.10. The cLDA model (for additional details, see the online supplement) provides results similar to the classic analysis of covariance (ANCOVA) approach when there is minimal missing data (35, 36). Yet, unlike ANCOVA, cLDA is a full information maximum likelihood (FIML) procedure that retains every observation and is hence more efficient and less prone to missing data biases. The baseline assessment and four postbaseline assessments (at 2, 4, 6, and 8 months of follow-up) are described above. Baseline measurements were taken before randomization to supportive psychotherapy or MORE conditions, so the treatment group means are assumed equal at baseline in the cLDA model but allowed to differ at follow-up assessments. As detailed above, COVID-19-related restrictions, which were instituted midway through the study, necessitated a change in format. Therapy sessions were initially conducted in person but were subsequently implemented remotely to comply with requirements. Because this format change could not be randomized, we treated delivery method as an observational stratification variable. Therefore, population means for the treatment groups were randomized and necessarily equal within the in-person and remote conditions, but the effects of these two conditions were uncontrolled, and their baseline means were unconstrained. Effects were averaged across the in-person and remote conditions to compute the principal estimate of overall treatment impact. Serial dependence was modeled by normally distributed random intercepts, along with normally distributed random error. To control for multiple comparisons, we first conducted three independent structural equation models to perform a multivariate omnibus test of no treatment impact on primary, secondary, and process outcomes. These omnibus tests, which control for multiple comparisons, are likelihood ratio tests of the null hypothesis (no difference between groups) with four degrees of freedom between the unrestricted model and the constrained model. Examination of individual outcomes was pursued if and only if the omnibus test was rejected at an alpha of 0.05. Opioid dose was square root transformed to reduce skew before using cLDA.

If the omnibus multivariate test was significant, we examined the univariate treatment effects on each outcome using the cLDA approach under a mixed-effects model likelihood framework. For each outcome, the null hypothesis posited equal baseline-adjusted mean differences between treatment arms over the four postbaseline time points, while assuming equal baseline means across treatment arms, with a compound symmetry covariance structure. The single degree-of-freedom estimates and tests were implemented using SAS “estimate” coefficients and evaluated against the null at alpha=0.05 (two-sided, with conservative Kenward-Roger degrees of freedom). Time was treated as a categorical factor with four postbaseline levels. The overall estimate of the between-group treatment effect is reported in unstandardized response variable metrics. No additional covariates were considered in these primary analyses.

Ecological momentary assessment of craving was analyzed with a mixed model that included fixed effects of time, treatment, and the treatment-by-time interaction, as well as a random intercept and a first-order autoregressive covariance structure. In this analysis, the treatment-by-time interaction (difference in craving trajectory across the possible 180 assessments per subject) was the primary fixed effect of interest. Similarly specified mixed models were also used to assess treatment effects on opioid attentional bias scores, with the treatment-by-time interaction being the effect of interest. Attentional bias scores were computed separately for reaction times (RTs) following presentation of the 200- and 2,000-ms cues using the canonical approach (RT_neutral−RT_opioid), with higher values indicating a greater attentional bias toward opioids (34).

We followed an intent-to-treat approach and sought to obtain follow-up data on all participants. Study discontinuation rates did not differ significantly across treatment arms and were similar to rates observed in trials of psychosocial treatments for opioid use disorder (37). No missing data were imputed, because FIML methods are theoretically accurate even when dropout rates are substantial and when predictors of dropout, such as treatment assignment and prior observations, are modeled as observed variables (38). Sensitivity to missingness at random was evaluated in FIML multivariate analyses that introduced a larger set of auxiliary demographic and clinical variables expected to correlate with missingness—an alternative to multiple imputation that often produces more accurate and precise parameter estimates (38).

Of the 331 patients assessed for eligibility, we enrolled 230 (Figure 1). Of this sample, 83% were male and 91% were veterans, with the remainder being active-duty military personnel. Participants had a mean age of 57.5 years (SD=11.7), mean BPI pain severity score of 5.6 (SD=1.5), mean COMM score of 13.4 (SD=7.8), and a mean morphine equivalent daily opioid dose of 105.3 mg (SD=204.6; interquartile range, 12.0–90.0 mg). More than half of the participants (55%) reported having oxycodone or hydrocodone prescriptions. Participants reported having pain for a mean duration of 19.3 years (SD=12.6), and pain was most commonly reported to be in the lower back (81%). Major depressive disorder was prevalent in the sample (60%), but a substantial proportion of participants also met clinical criteria for opioid use disorder (34%) or posttraumatic stress disorder (PTSD) (19%), based on the Mini-International Neuropsychiatric Interview at baseline, with no between-group differences. Participants in the MORE and supportive psychotherapy conditions attended a mean of 5.5 and 5.7 sessions, respectively. Data for one or more outcome variables from the 8-month follow-up were available for 81% of participants. Demographic and baseline clinical characteristics were similar between the two groups (Table 1).

Treatment effects of MORE and supportive psychotherapy on primary outcomes, secondary outcomes, and process variables are presented in Table 2. For pain and opioid use outcomes through the 8-month follow-up, the omnibus multivariate likelihood ratio test was significant (χ²=13.09, df=4, p=0.011), indicating the superiority of MORE over supportive psychotherapy. Compared with supportive psychotherapy, MORE produced significantly greater reductions in pain interference (B=0.47, 95% CI=0.10–0.84, p=0.011) and pain severity (B=0.27, 95% CI=0.00–0.54, p=0.048). Although aberrant drug-related behaviors decreased significantly in both groups over time (B=0.50, 95% CI=0.08–0.92, p=0.019) with no significant between-group differences (p=0.43), MORE reduced aberrant drug-related behaviors to a significantly greater extent than supportive psychotherapy in the in-person cohorts (B=0.48, 95% CI=0.01–0.96, p=0.047). No between-group differences were observed in the clinical interview of opioid misuse or in urine drug screen measures, except at an exploratory 12-month follow-up point extracted from EMRs; at this time point, among the patients who completed random urine drug screens (N=38), a smaller percentage of those in the MORE condition (13.3%, N=2) had a positive urine screen compared with those in the supportive psychotherapy condition (43.5%, N=13) (likelihood ratio, χ²=4.13, df=1, p=0.042). With regard to opioid use, MORE reduced daily opioid dose (square root transformed values) to a significantly greater extent than supportive psychotherapy (B=0.65, 95% CI=0.07–1.23, p=0.029); there was a 20.7% reduction in the mean opioid dose (18.88 mg, SD=8.40 mg) in the MORE condition compared with a 3.9% reduction (3.19 mg, SD=4.38 mg) in the supportive psychotherapy condition. Sensitivity analyses controlling for auxiliary variables associated with missingness also found that MORE outperformed supportive psychotherapy in reducing pain interference (p=0.010), pain severity (p=0.025), and opioid dose (p=0.025).

For secondary outcomes through the 8-month follow-up, the omnibus multivariate likelihood ratio test was highly significant (χ²=32.51, df=5, p<0.00001). No significant between-group differences were observed for emotional distress (p=0.102) or PTSD symptoms (p=0.175); participants in both treatment conditions improved over time. However, MORE reduced anhedonia (B=2.27, 95% CI=1.11–3.42, p<0.001) and pain catastrophizing (B=2.54, 95% CI=1.19–3.98, p<0.001) and improved positive affect (B=1.50, 95% CI=0.15–2.85, p=0.029) to a significantly greater extent than supportive psychotherapy.

For the process variables, the omnibus multivariate likelihood ratio test was highly significant (χ²=32.79, df=5, p<0.00001). MORE produced greater increases than supportive psychotherapy for all process variables, including mindful reinterpretation of pain sensations (p<0.001), nonreactivity to distressing thoughts and emotions (p=0.030), cognitive reappraisal (p=0.011), savoring (p=0.036), and attention to positive information (p=0.001).

Regarding ecological momentary assessment of opioid craving, craving ratings decreased over the course of treatment by 0.67 points more in the MORE condition than in the supportive psychotherapy condition (95% CI=0.001–0.007, p=0.019). Finally, participants assigned to MORE exhibited significantly greater decreases in the 200-ms opioid attentional bias measure than participants in supportive psychotherapy (B=29.89 ms; 95% CI=3.77–56.01; p=0.025). No significant group differences were observed with the 2,000-ms attentional bias measure.