Comparing the clinical and cost-effectiveness of remote (telehealth and online) cognitive behavioral therapy-based treatments for high-impact chronic pain relative to usual care: study protocol for the RESOLVE multisite randomized control trial

Chronic pain is one of the most common, disabling, and costly public health problems in the USA [1] and a primary reason that patients seek medical care. About 1 in 10 US adults experience high-impact chronic pain, defined as pain that has lasted 3 months or longer and is accompanied by at least 1 major activity restriction, such as being unable to work outside the home, go to school, or do household chores [1‐3]. Rural residency is associated with higher prevalence of high-impact chronic pain with complicating features such as depression and medical comorbidities [4, 5]. Rural residents with chronic pain report higher pain frequency and intensity and more pain-related disability and depression than urban residents with pain [6, 7]. Further, healthcare disparities between rural and urban areas are widely recognized with difficulties in availability, accessibility, and affordability of health services often disproportionately impacting rural residents [8]. These disparities are associated with higher risk of adverse outcomes and suboptimal pain management among rural patients with chronic pain.

Until relatively recently, opioids were the main, and often only, treatment provided for long-term chronic pain management despite limited evidence of effectiveness [9]. Opioid treatment-related addiction, overdose, and other harms resulting from widespread opioid use left an aftermath of adverse effects for patients, families, and communities [10, 11]. These consequences have been especially pronounced in rural communities where rates of non-medical prescription opioid use and overdose have been disproportionately higher than in urban areas [12, 13]. Consequently, primary care clinicians and their patients, especially in rural and medically underserved areas, urgently need increased access to viable non-opioid options and treatments for long-term chronic pain management.

Cognitive behavioral therapy (CBT) is the most widely accepted and effective non-pharmacotherapy treatment for chronic pain [1, 14, 15] and has been shown to benefit adults with low literacy in rural areas [16]. Cognitive behavioral therapy for chronic pain (CBT-CP) is based on the theory that patients’ beliefs, attitudes, behavior, and coping styles play central roles in mediating the impact of persistent pain on patients’ lives [17]. It focuses on helping patients develop and master skills to manage pain and the way pain affects their thoughts, feelings, and both physical and social activities in order to improve functioning and quality of life. Because CBT-CP focuses on learning, applying, and mastering coping skills, its effects potentially can be maintained long after treatment ends, without the negative side effects of opioids and other pain medications. The National Pain Strategy calls for wider implementation of CBT-CP self-management training [18], noting that despite evidence supporting its efficacy, CBT-CP implementation lags due to significant barriers including a paucity of trained providers and their concentration in higher socioeconomic status urban areas.

Outside Veterans Affairs (VA) healthcare systems [19], few clinicians are trained to deliver CBT-CP services in community practice. Despite the growing emphasis on standardized training and implementation methods, CBT-CP services often vary in content and quality [20]. In community settings, fidelity to best CBT-CP treatment practices is rarely assessed [21]. Frontline behavioral health providers offering CBT-CP generally have large caseloads and typically prioritize treatment for mental health disorders. These problems are especially critical in rural and medically underserved areas [6, 8, 22] where behavioral health and psychotherapy providers are scarce and few professionals are trained to deliver CBT-CP [23]. In addition, conventional CBT-CP programs can be difficult to access for patients with competing demands, limited time, and transportation or mobility barriers. Most CBT-CP programs require weekly in-person sessions of 50 min or more over 2 to 3 months, often in group formats with inflexible scheduling. Because of these and other barriers, patients referred for CBT-CP may not attend a sufficient number of sessions to receive an adequate treatment dose [24]. Further, the stigma associated with what are perceived to be “psychological” interventions can limit patient uptake [25, 26]. Providing CBT-CP by telephone, video visit, or an online program may help reduce access barriers, destigmatize its use, and encourage patients to view it as complementing conventional medical management of chronic pain. Lastly, primary care providers often lack familiarity with CBT-CP and may not have enough time to discuss CBT-CP with patients, lack ways to provide a compelling rationale for CBT-CP, or have difficulty explaining why a psychologically informed treatment may help manage a physical condition [27]. Moreover, few guidelines exist for determining which patients might benefit from CBT-CP [28‐30] and in which circumstances the various formats for delivery of CBT-CP-based interventions (e.g., led by trained interventionist vs. self-guided online format) may be preferable [31].

Technologies to deliver and assist treatment such as telephone-based and online treatment programs [32‐34] offer ways to increase access to evidence-based pain care, including CBT-CP and related self-management approaches [18, 35, 36]. Prior studies have demonstrated clinically meaningful benefits of telephone-based CBT-CP for pain-related outcomes in the context of multicomponent interventions [34, 37, 38]. Online CBT-CP treatment programs, which deliver training in a self-completed, interactive, web-based format and do not rely on or only sometimes include the involvement of a trained therapist, have demonstrated efficacy for improving pain and pain-related impairment as supported by multiple meta-analyses [36, 39, 40]. Although overall effect sizes are modest, these reviews suggest the potential impact of these treatment approaches with respect to lower costs and greater safety than pharmacologic pain treatments [36, 39, 40].

Additionally, remote services can reach large numbers of patients at lower costs per patient treated while overcoming system, patient, and clinician barriers [41]. Growing evidence suggests that remotely provided interventions can improve self-management and chronic disease management outcomes [42]. Due in part to the COVID-19 pandemic, telehealth services have rapidly expanded with a particular push towards video visits which best approximate traditional in-person visits, while provision of self-administered online services has also increased markedly due to lower costs and greater accessibility [43‐45].

The primary objective of the RESOLVE study is to determine the comparative effectiveness of 2, remotely delivered, CBT-based, interventions for chronic pain: (1) an 8-session health coach delivered telephonic/video conference one-on-one program and (2) an 8-session online self-completed program. Effectiveness will be assessed by comparing clinically meaningful improvements in pain severity, a composite measure of pain intensity and pain-related interference, among patients with high-impact chronic pain at 3 months post-allocation, relative to usual care and each other.

Secondary objectives of the study include examining whether the interventions have an enduring impact on pain severity at 6 and 12 months post-allocation as well as the interventions’ impact at 3, 6, and 12 months on pain intensity, pain-related interference, social role functioning, physical role functioning, and patient global impression of change. The cost and incremental cost-effectiveness of the 2 interventions compared to usual care and each other will also be assessed.

The RESOLVE study also includes qualitative interviews with participants, healthcare system leadership, and study staff. These data will be used to better understand the acceptability of CBT-CP-based interventions for patients and health systems, lessons learned during study implementation, and changes in usual care during the study period. Exploratory objectives also include assessing the impact of the interventions on long-term opioid use, comorbid symptomology (depression, anxiety, and sleep disturbance), and chronic pain grade.

The RESOLVE study is a multisite, prospective, comparative effectiveness, phase III randomized controlled trial (RCT). The study uses a parallel group design in which study participants are randomized in equal ratio to 1 of 3 study groups. One group receives 8, one-on-one, CBT-CP sessions with a health coach via telephone or video conference to be completed within approximately 12 weeks from randomization. A second group receives an 8-session, online CBT-CP-based program that delivers pain coping skills training (painTRAINER®) to be completed within approximately 12 weeks from randomization. The content of the health coach CBT-CP sessions and painTRAINER interventions is similar. The third group receives a copy of the 2020 edition of the American Chronic Pain Association Resource Guide to Chronic Pain Management [46]. Participants will be followed for 12 months from allocation (Fig. 1).

Participants are being recruited from the populations of 4 integrated healthcare systems which serve as the clinical sites: (1) Kaiser Permanente Georgia (KPGA) with a service area of northern Georgia, (2) Kaiser Permanente Northwest (KPNW) with a service area of Oregon and southwest Washington, (3) Kaiser Permanente Washington (KPWA) with a service area of Washington state, and (4) Essentia Health with services throughout areas of northern Minnesota, eastern North Dakota, and northern Wisconsin. The healthcare facilities in the 3 participating KP regions are located in urban and suburban areas; however, the KP healthcare systems also serve individuals residing in rural areas of their respective regions. Essentia primarily serves rural areas. The RESOLVE study is part of the National Institutes of Health Helping to End Addiction Long-term® (NIH HEAL) Initiative which is an aggressive, trans-NIH effort focused on improving prevention and treatment strategies for opioid misuse and addiction and enhancing pain management. RESOLVE is supported by the HEAL Pain Effectiveness Research Network which is administered by the National Center for Advancing Translational Science (NCATS) Trial Innovation Network [47].

This study employs a population-based recruitment approach within each of the participating healthcare systems in which the individuals who are invited to be screened for study participation are identified based on the following electronic health records-based criteria.

Electronic health records inclusion criteria:

Electronic health records exclusion criteria:

*The pain-related healthcare utilization inclusion criteria aim to identify individuals with chronic pain; a unique criterion is used for Essentia because of lower overall in-person utilization rates among the predominately rural population served by this healthcare system.

Individuals who choose to be screened for eligibility must meet the following inclusion and exclusion criteria in order to participate in the study.

Screening inclusion criteria:

Screening exclusion criteria:

Participants complete informed consent by phone with a research staff person or electronically via the study website. There are several recruitment and screening steps that precede the informed consent encounter.

Specifically, based on the electronic health records eligibility criteria described above, potentially eligible patients are identified via data query and then mailed a packet containing the study (1) recruitment letter, (2) brochure, and (3) one-page infographic describing the study design and activities. The letter includes instructions for contacting research staff, specific to the potential participants’ clinical site, by phone to address any questions and/or complete eligibility screening by phone. The letter also includes information for accessing the study website and instructions on completing the eligibility screening online, if preferred, including a unique access code for the screening survey. Potential participants who have an active email address and have opted in to research-related communications from their healthcare system (a subset of those mailed) are sent a recruitment email that has similar content to the letter and links to the study website approximately 1 week after the mailing. If a potentially eligible participant does not call the study staff or complete the screening survey within approximately 2 weeks of the mailing, research staff attempt to reach them by phone. The recruitment letter explains this potential outreach and how to opt out of the future contact, if preferred.

If a potential participant is determined to be eligible based on the screening survey, they can proceed with the informed consent process by phone or web during the same encounter, immediately following completion of the screening survey. Or, if the individual would prefer to conduct the informed consent process at a later time, they can schedule a time to complete it by phone with a study staff member or return to the website later to complete it electronically, using their unique code.

As part of the informed consent process, participants are asked to provide authorization for extraction and use of their healthcare utilization data from their healthcare system’s electronic health record (i.e., encounters with associated pain-related procedures, diagnosis codes, and prescriptions) for the 12 months prior to and following allocation/randomization. These data will be linked to the study-collected assessment data. Participants are also asked to consent to future use of their data as part of the de-identified database stored in the NIH HEAL data repository in accordance with the public data sharing procedures and regulations of the NIH. This trial does not involve collecting biological specimens.

The RESOLVE study includes 2 active intervention arms: (1) a health coach-led, 8-session CBT-CP program that is provided one-on-one via telephone or video encounters, and (2) an online, self-directed, 8-session, CBT-CP-based program. Both of these active interventions are compared to (3) an enhanced usual care arm in which participants receive an educational manual, the 2020 edition of the American Chronic Pain Association Resource Guide to Chronic Pain Management [46]. Inclusion of the enhanced usual care comparator enables us to address the critical question: What is the incremental benefit of the study interventions over what treatments patients are already able to access to help manage their pain? This is important to understand from a clinical and healthcare-implementation (cost) perspective. If both interventions perform favorably compared to enhanced usual care, then 2 evidence-based, CBT-CP-based options would be available, providing options for remote care that can be accessed based on factors such as patient preference and healthcare system needs.

This study will also include a comparison of the 2 active, remote interventions. Given the importance of patient motivation and engagement to achieve CBT-CP benefits, we posit that those working with a live therapist via telephone or video may be better able to overcome barriers to routine practice of important skills. This may be particularly important for patients with higher levels of depression or anxiety symptoms (common chronic pain comorbidities) for whom de-activation and/or avoidance may create barriers to implementing effective pain coping skills. Limited data exist on the relative benefits of telephonic/video health coach format versus online delivery format for CBT-CP-based interventions, making this comparison of clinical and cost-effectiveness relative to usual care along with findings from the qualitative evaluation timely and important.

Both of the 8-session CBT-CP-based interventions being evaluated in the RESOLVE trial are based on and adapted from the programs developed and refined by Dr. Keefe and colleagues at Duke University over the past three decades [53‐58]. In addition, the health coach manual and participant workbook for the RESOLVE health coach-led intervention are based on the PPACT intervention, which was tested in a large pragmatic trial [59, 60]. Table 1 provides an overview of the core content for both of the RESOLVE CBT-CP-based interventions by session. The content and sequencing of the two interventions is consistent and begins with a focus on understanding the neuroscience of pain and the associated rationale for the potential impact of CBT. Sessions focus on learning / mastering the following evidence-based skills: relaxation and body awareness techniques, activity-rest cycling, pleasant activity scheduling, cognitive restructuring, guided imagery, problem solving, and maintenance planning. The RESOLVE interventions are guided by social cognitive theory (e.g., social modeling, vicarious learning) [61, 62], adult learning theory (e.g., tying skills to personal goals and experiences) [63, 64], and behavior change theory [65]. Additionally, the health coach intervention utilizes motivational interviewing techniques to clarify patient values, elicit change talk, and match session focus to patient readiness for change [66] and painTRAINER utilizes the principles of multimedia instruction (interactive exercises, graphics to reinforce explanations) [67]. Participants are considered to have received a full dose of the interventions if at least 75% or any 6 of the 8 sessions are completed.

Any adverse events associated with the active study interventions are expected to be minor, and there are no planned criteria for discontinuing or modifying allocated interventions. There may be rare instances in which an individual decompensates (or is threatening to study staff) and is consequentially unable to continue to actively participate in a behavioral intervention of the type administered in this trial. In this event, the reason for discontinuation will be documented and an attempt to connect the participant to relevant behavioral health resources/support in their healthcare system will be made. If a participant informs the study staff that they will discontinue participation in the intervention, staff will assess their reasons for discontinuation and determine whether the participant wants to continue with the other study activities or withdraw from the study entirely.

Eligibility screening criteria exclude from participation individuals who are currently receiving, are planning to receive in the next month, or have received in past 6 months CBT for pain or a similar psychoeducational skill-based training for pain. However, once enrolled, participants in all study groups can receive any pharmacologic or nonpharmacologic treatments available to them without restriction. At each follow-up study assessment (T₁, T₂, T₃), participants’ use of CBT for pain or a similar psychoeducational skill-based training for pain (in-person, by phone or via online or App-based programs) will be assessed. Receipt of opioids in a manner consistent with long-term opioid treatment is also tracked via electronic health records data.

Post-trial care will not be provided. There is no anticipated harm for trial participation and therefore no compensation for anticipated harm.

Table 2 provides information on primary and secondary study objectives and outcomes. The RESOLVE study employs the NIH HEAL Common Data Elements [68] and additional select outcomes.

The RESOLVE study includes a mixed-method evaluation to understand (1) patient experiences of the interventions, including how they relate to treatment response, clinical site, and rural/medically underserved residency status; and (2) healthcare system issues, including adaptations and contextual factors at the site and external levels, barriers and facilitators to intervention success, and potential for adoption, sustainability, and dissemination. As part of the mixed-method evaluation, interview data will be collected at a range of timepoints and reflective of multiple perspectives, including active intervention participants, participants that drop out or disengage from the interventions; health coaches, staff involved in onboarding participants to the online program; and healthcare system leaders at each site who are involved in managing services for chronic pain patients. Table 5 summarizes the interviews to be conducted.

Active intervention participants will be interviewed twice after completion of the 8-session intervention, with the first interview occurring post-treatment (approximately 3 months post-allocation; T₁) and the second interview occurring 9 months post-treatment (approximately 12 months post-allocation; T₃). We will explore barriers to and facilitators of engaging in the two interventions and learning and practicing the skills, as well as willingness and ability to utilize and maintain the skills over time. We will also assess perceived benefits and/or negative consequences on pain, pain management, and other possible outcomes (e.g., improved sleep). We aim to interview 70–80 participants, balanced by intervention group, site, age, rural/urban residency, pain severity score at T₁, and representative of race/ethnicity. This number of interviews is sufficient for meeting saturation for content analysis and identifying themes [94]. Additionally, we will interview 20 participants who disengage from the interventions early on to assess barriers to participation.

All interview data will be managed by an experienced and trained qualitative team led by a doctoral trained medical anthropologist (Carmit McMullen, Co-Investigator). Interviews will be conducted by phone, recorded on password-protected devices, and professionally transcribed to aid in content analysis. An inductive, constant comparative approach [95] will be used to summarize interview data. Mixed method data management and coding/analysis of interview data will be aided by the qualitative software program NVivo R1.6 [96].

The process evaluation is informed by 2 frameworks which guide data collection and analysis. First is the RE-AIM model [97, 98], which has 4 components: Reach, Effectiveness, Adoption, Implementation, and Maintenance. Electronic health records, interview, participant tracking and survey data will contribute to understanding RE-AIM components. Reach reflects the percentage and characteristics of persons who receive or are affected by a program. The project will use electronic health records and study tracking data to examine (1) the percentage of patients excluded from the trial and the rationale for exclusion, and (2) the percentage of patients who participate in the program based on the denominator of all patients who were approached for participation in each healthcare system, as well as all potentially eligible patients in the healthcare system regardless of whether or not they were approached for participation. Effectiveness measures the impact of the intervention on primary and secondary outcomes. Trial outcomes and participant interview data will be used to assess and explain effectiveness. Adoption is less relevant to the current study as the telehealth programs can and will be made available to patients completely outside the ambulatory care setting, thereby reducing or eliminating routine barriers for adoption of healthcare treatments. However, health system leader interviews will provide insight about potential for future adoption. Implementation will be assessed by examining participant completion of the 2 interventions (data recorded by the health coaches and automated data collected from the painTRAINER platform). Interview data will identify barriers and facilitators to engagement and completion of intervention activities. Finally, maintenance of skills learned will be assessed through interviews with participants immediately following and 9 months after intervention completion. In addition to RE-AIM, the Theoretical Framework of Acceptability (TFA) will be used to explore various aspects of acceptability, from both participant and healthcare system perspectives [99]. The TFA is a multifaceted construct that reflects the extent to which people delivering or receiving a healthcare intervention consider it to be appropriate. The TFA is complimentary to constructs in RE-AIM and further examines issues of acceptability, particularly for patients. The TFA consists of 8 primary domains that have temporal aspects (e.g., before, during, and after an intervention) and consider both anticipated reactions to an intervention as well as cognitive and emotional responses experienced with an intervention. The domains include affective attitude, burden, ethicality, intervention coherence, opportunity costs, perceived effectiveness, and self-efficacy.

See Fig. 2 for a schedule of participant activities.

For the primary study outcome, MCID in pain severity from T₀ to T₁, sample size requirements were calculated for a two-sided comparison of independent proportions with 90% power using Fisher’s least significant difference method to account for three-way comparisons (specifically conduct Omnibus Wald test for any difference between three groups and then conduct pairwise comparisons given an overall difference is statistically significant at the 0.05 alpha level). Sample size calculations assumed a usual care outcome rate of 15% who achieve the MCID of ≥ 30% reduction in pain severity from T₀ to T₁. The 15% usual care rate was chosen because it was observed among participants in the usual care arm of the study principal investigator’s recently completed PPACT trial [24]. The necessary analytic sample size of 1863 (621 per arm) was calculated to detect a difference of 7.5% between a given intervention group relative to usual care in the proportion of individuals who attain a clinically meaningful change in pain severity. A retention rate of 80% is estimated. Thus, to achieve this final analytic sample size, at least 2331 individuals will be randomized, approximately 777 per intervention arm. A 7.5% detectable difference corresponds to 22.5% (relative change of 150%) of individuals in an intervention arm attaining a MCID in pain severity.

Power for secondary, subgroup analyses was also estimated (Table 6). Sample size requirements for these secondary analyses were calculated using the same assumptions described above (i.e., a two-sided comparison of independent proportions using Fisher’s least significant difference approach to account for three-way comparisons, with sample size calculations assuming an improvement rate of 15% in the usual care arm). The subgroup sample size was projected to range between 20 and 40% of the original 1863 sample size since this should cover the range of the subgroup sample sizes of interest.

There is 80% power to detect a 10.8% difference (relative change of 172%) between each intervention group and usual care if subgroup sample size is 40% of the overall study population and 16.0% difference (relative change of 206.7%) if the subgroup sample size is 20% of the overall study population. Note that in previous studies of this study team, sex and comorbid mental health conditions (depression, anxiety) were not less than 40% of the population suggesting there is high power for the primary subgroups of interest. Further, the study is aiming to have at least 20% of rural/medically underserved residency and therefore there is good power for this subgroup. Individuals with negative social determinants of health comprise an exploratory subgroup since it is not clear how many people in this population a priori will have this indication.

Each of the 4 sites is responsible for recruiting and enrolling approximately 600 patients per site in order to reach the overall study target for number randomized within the study timeline (N = 2331). On a monthly basis during the approximately 24-month recruitment period, each site queries their electronic health records data warehouses to identify a random sample of patients who meet the electronic health record-based inclusion criteria. The sample of patients is stratified by urban vs. rural or medically underserved residence, based on the individuals’ resident Census Tract/geocoded data [85, 86].

As described previously in the section related to informed consent, individuals in the random sample are mailed a recruitment letter and brochure which includes a description of the study, instructions for how to call a research staff person to complete the screening survey by phone or complete it online, and select elements of informed consent, including a clear statement of the ability to opt out of further contact by calling the site-specific study telephone number. Finally, the letter states that patients might be contacted by phone in the following weeks to participate in the study if they have not called to opt out of further contact or gone online to complete the screening survey. Each site, as feasible/allowable, will also send a recruitment email in follow-up to the mailing to patients in the sample who have an active email address.

This population-based recruitment process is the primary method for identifying potentially eligible patients for this trial. A secondary method is self-referral. Individuals who learn about the study on their own (not through the targeted mailing) can contact their site. Study staff will obtain their permission to access their electronic health record, and then the site analyst will execute a pre-developed program to evaluate eligibility. If the person does not meet the electronic health record inclusion criteria, the study staff person will follow-up with the patient by phone or mailed letter to explain this. If the person does meet the electronic health record inclusion criteria, they will be mailed recruitment materials and follow the same process as described above for those identified through the monthly queries.

After completion of the baseline assessment, participants are individually randomized in equal ratio to one of the three study groups: (1) telephonic/video conference program, (2) online program, or (3) usual care plus manual. Randomization is stratified on sex as documented in the electronic health record (male vs. female or other); pain severity score on 11-item modified BPI-SF from baseline assessment (< 7 vs. ≥ 7); clinical recruitment site (KPGA, KPNW, KPWA, Essentia Health); and residency in a rural or medically underserved area based on residency geocode for Census Tract from electronic health record (yes vs. no). A random permutated block design is used with random variable block sizes of 3, 6, or 9 to ensure approximately equal accrual over time into the three study groups.

Participants are randomized within the study’s secure, web-based, electronic data capture system immediately after participant completion of the baseline assessment. The lead biostatistician at the NIH HEAL Johns Hopkins University Trial Innovation Center Biostatistics Core, in collaboration with the study biostatistician (Andrea Cook), developed the randomization scheme. The Utah Data Coordinating Center developed the randomization tables for integration into the electronic data capture system.

Following randomization within the electronic data capture system (EDC), participants appear on cohort management lists and sections of the EDC that are applicable to intervention delivery for logging intervention contacts and session completion and are accessible only by unblinded staff (i.e., research support staff who mail intervention materials, health coaches). Information on the allocation group will remain concealed to study outcome assessment staff. Participants receive a mailing within approximately 1 week of allocation that indicates the study group to which they have been assigned and includes any relevant materials related to their group.

The outcome assessors are blinded to group allocation. During assessments, participants are instructed to not communicate with the assessors about the intervention received.

In addition, all study team investigators will remain blinded and not have access to outcome data or results until the completion of the final 12 months outcome assessments in which the datasets will be locked. After the 3-month outcome data collection is complete, the independent Data Coordinating Center at the University of Utah, independent Biostatistical Core at John Hopkins University, and the study team’s collaborative biostatistician will have access to outcome data without treatment allocation for programming purposes. The study biostatistician Dr. Cook, will not have access to data or see any results, remaining blinded until after the 12-month outcome assessments are complete and final datasets are locked. The statistical analyses will be conducted blind to actual randomization assignment until final.

The outcome assessors will not be unblinded during the trial. There are no planned interim analyses so unblinding of statisticians is not anticipated prior to the data lock unless requested by the independent Data Safety and Monitoring Board.

Assessments will be completed via questionnaires administered at baseline (T₀), 3 months post-randomization (T₁; post-treatment), 6 months post-randomization (T₂), and 12 months post-randomization (T₃). The research team will keep careful track of assessment completion and will contact participants (by phone, email, mail) if measures have not been completed according to a protocol to encourage completion of assessments at all timepoints.

The following strategies will be used to maximize follow-up assessment completion rates: (1) allow participants to complete assessments using the mode they prefer (online, by telephone, or a mailed survey) given reasonable comparability expected across modalities of administration [100, 101]; (2) confirm and update participant contact information (phone, address, email) at each contact; (3) use healthcare system administrative records to identify any address changes that are not communicated by the participant; and (4) provide incentives that adequately compensate subjects for the time spent completing assessments.

Follow-up assessment data are stored on a HIPAA-compliant secure server hosted, managed, and monitored by the University of Utah Data Coordinating Center (DCC), with daily backups, and will be de-identified at the earliest possible opportunity. The DCC oversees data management for the trial and details on their processes and procedures are specified in the Data Management Plan which is available from the corresponding author on request.

Subject confidentiality is strictly held in trust by the investigators, study staff, and the study sponsor(s) and their agents. This confidentiality is extended to any study information relating to participants. The study protocol, documentation, data, and all other information generated will be held in strict confidence. No information concerning the study or data will be released to any unauthorized third party without prior written approval of the study sponsor. The U.S. Department of Health and Human Services (HHS) has issued a Certificate of Confidentiality and, as a recipient of NIH funding for human subjects research, this study complies with the requirements for protection of identifiable research information from forced disclosure per the terms of the NIH Policy. As a recipient conducting NIH-supported research covered by this Policy, the study team has established and maintains internal policies and procedures to ensure management in compliance with Federal statutes, regulations, and the terms and conditions of the award.

This trial will not involve the collection of biological specimens.

We will use modified Poisson regression [102] fit using generalized estimating equations (GEE) to model the binary primary outcome, MCID in pain severity (30% reduction from baseline), 3 months (T₁; primary timepoint) and 6 and 12 months (T₂ and T₃; secondary timepoints). We are employing modified Poisson (i.e., Poisson family with log link, but use robust standard errors to correct for mis-specified outcome variance) instead of logistic regression since the binary outcome is not rare and the estimate of interest is the relative risk. We will use a working independence correlation matrix and will calculate standard errors using the robust sandwich estimator to account for within-person and within-health coach correlation [103] and account for the mis-specified mean–variance structure when using Poisson regression for a binary outcome [102, 104]. We will include interactions between each intervention and indicators of time (T₂ and T₃) to estimate time-specific intervention effects; the primary comparisons will be between the interventions and usual care at 3 months (i.e., primary effectiveness will test the size of the intervention coefficient at the 3-month timepoint). We will adjust for baseline levels of pain severity, other stratification variables (sex, clinical site, and rural/medically underserved residency), and a priori variables predictive of outcome (multisite pain and co-occurring mental health condition). Specifically, we will fit the following mean model where usual care and 3 months are the reference groups:where \({\mathrm{Y}}_{\mathrm{ij}}\) is the binary MCID outcome for participant i (i = 1,…,n) and timepoint j (j = 1,2,3), \({\mathrm{Int}1}_{\mathrm{i}}\) is 1 if the participant i is randomized to the first intervention group and 0 otherwise, \({\mathrm{Int}2}_{\mathrm{i}}\) is 1 if participant i is randomized to the second intervention group and 0 otherwise, \({\mathrm{T}1}_{\mathrm{ij}}\) is 1 if outcome is measured for participant i at 6 months (j = 2) and 0 otherwise, \({\mathrm{T}2}_{\mathrm{ij}}\) is 1 if outcome is measured for participant i at 12 months (j = 3) and 0 otherwise and \({\mathrm{Z}}_{\mathrm{i}}\) is a vector of baseline adjustment covariates.

Interim analyses will not be conducted as no potentially serious outcomes are expected.

Subgroup analyses will be conducted to determine the impact of the active interventions on specific populations and explore for potential heterogeneity of treatment effects by sex, age, race/ethnicity, rural/medically underserved residency, multiple pain conditions, mental health disorders, and negative social determinants of health. Analyses will follow the same general approach as for the primary outcome but will be focused on assessing heterogeneity of treatment effects (subgroups). We will assess heterogeneous treatment effects by each potential moderator separately. For each moderator, a main effect for the moderator and an interaction between the moderator, intervention, and follow-up time, to estimate time-specific intervention effects within each subgroup defined by the potential moderator. The primary comparison will be of the interaction terms associated with each intervention arm at the 3-month follow-up time. The longitudinal nature of data collection will allow us to qualitatively assess if the treatment effectiveness pattern is different over time in each of the intervention groups at the different levels of each of the moderators.

Mediation analyses will also be conducted to assess and quantify the effect of theory-based mediators (pain catastrophizing, pain self-efficacy, perceived support). Mediators represent a causal pathway between the intervention and outcome. Mediation occurs when the intervention influences a variable (the mediator) that in turn subsequently influences the outcome variable. Controlling for a mediator variable causes the strength of relationship between intervention and outcome to be meaningfully reduced. Consistent with recommendations, we will conduct mediation analyses only for interventions that have significant impacts on the outcomes under consideration at 6 months. Primary mediation analyses will assess the effect of the potential mediators on the primary outcome at 6 months, MCID in pain severity, while explanatory secondary analyses will investigate mediator impacts on secondary outcomes at 6 months. We will conduct mediation analyses using the framework recommended by Baron and Kenney [112] but using more recent statistical methods developed to better quantify and decompose different aspects of the mediation effect [113]. We will run a separate set of mediator analyses for each intervention compared to usual care. We will illustrate our approach for the binary outcome, achieving MCID in pain severity at 6 months.

As the primary analysis, all effectiveness outcome measures are analyzed under intention-to-treat (ITT). A per-protocol sample may be constructed if there is crossover among greater than 10% of participants randomized to usual care (i.e., > 10% of usual care group receives CBT-CP) in which treatment-as-received is analyzed.

Our primary approach to handle missing data is through baseline adjustment which assumes that missing data to be missing at random (MAR) given the adjustment of the baseline covariates. If we observe > 15% missing primary outcome at 3 months, or differential missingness by group (> 10% difference between arms), we will conduct missing data sensitivity analyses. We will address missing data in 2 ways. Our first approach will apply a pattern mixture imputation missing data approach that relaxes the MAR assumption conditioning on the patterns of missing data over time [114]. The second approach will be used as a sensitivity analysis assuming a worst-case, best-case approach. Specifically, for those with missing outcome data in the intervention groups, we will assume they did not achieve the MCID in pain severity at each missing time point (worst-case). For those randomized to the usual care, we will assume all achieved the MCID in pain severity at each missing time point (best-case). This sensitivity analysis will provide the extreme case in how small the intervention effect could be relative to usual care due to missing outcome data.

The full protocol will be accessible on ClinicalTrials.gov at the time the study results are posted. All data collection forms are available from the corresponding author on request. A database for underlying primary data for publications will be made publicly available on the NIH HEAL Initiative central data repository. The database will be de-identified in accordance with the definitions provided in the HIPAA and will be accompanied by a data dictionary that provides a concise definition of every data element included in the database. The policies for release of and access to this database are in accordance with the HEAL Data Sharing policy as determined by the NIH. The statistical code for primary study analyses will be available from HEAL Pain Effectiveness Research Network Trial Innovation Center (TIC) at Johns Hopkins University which serves as the Biostatistics Core for the study.

Study monitoring is conducted by Trial Innovation Centers (TICs) of the NCATS Trial Innovation Network. Specifically, the Duke University TIC serves as Clinical Coordinating Center (CCC) and the University of Utah TIC serves as the Data Coordinating Center (DCC). Clinical and remote site monitoring is conducted to ensure that the rights of human subjects are protected, that the study is implemented in accordance with the protocol and/or other operating procedures, and that the quality and integrity of study data and data collection methods are maintained.

Study oversight is under the direction of a Data and Safety Monitoring Board (DSMB) comprised of experts from chronic pain treatment, behavioral interventions, and statistics. Specifically, the DSMB members include David A. Williams, PhD (Chair), Steven Dobscha, MD, and Keith Goldfeld, DrPH. The DSMB met before study enrollment began to approve the study protocol prior to implementation and meets biannually until the study ends to assess safety and effectiveness data, monitor accrual of study participants, and assess study progress and data integrity for the study. If safety concerns arise, ad hoc meetings and more frequent standing meetings of the DSMB may be held. The DSMB operates under the rules of a charter that was approved at the initial meeting. The Johns Hopkins University TIC serves as the DSMB Unit for the RESOLVE study, supporting the DSMB members, as an independent entity, in the organization and implementation of successful DSMB meetings and is composed of a DSMB unit director, safety officer, DSMB coordinator, biostatistician, and an independent analyst. The DSMB will provide recommendations to the funding agency, the National Institute on Aging (NIA), regarding proceeding with the study as planned, proceeding with modifications, or terminating the study, as noted in the DSMB Charter.

Adverse events (AEs) are identified by participant self-report, and select serious adverse events (SAEs), inpatient hospitalizations and deaths, are systematically assessed based on electronic health records and healthcare system administrative data. Every 6 months, each clinical site queries active participants’ electronic health records data (in alignment with the DSMB meeting schedule) to identify any hospitalizations or deaths throughout the interval of active participant enrollment in the trial. An independent physician within each healthcare system conducts a chart review for each death to assess its potential relatedness to study procedures and interventions. The summary of SAEs and findings of these reviews are submitted to the DCC for reporting to the DSMB.

Monitoring is performed by the Duke CCC of the NIH HEAL Pain ERN in collaboration with the Utah DCC. Data are reviewed twice a month throughout the active study period for completeness; timeliness with completing data entry, per responsibilities of the site; ensuring participant visits occur within the appropriate time frame for scheduled study activities; and logical data (i.e., no “unbelievable” values).

A remote “for cause” monitoring visit may be triggered if there are serious issues of concern, which may include serious or persistent non-compliance with the protocol, study requirements, and/or applicable regulations and guidelines.

Approval for any study protocol amendments will be obtained from the Vanderbilt University Medical Center Institutional Review Board (IRB) which serves as the single IRB for the study. If warranted by the amendment, participant consent materials and information sheets will be updated accordingly and any changes to the published protocol will be reported in full in any future publications.

The results from this clinical trial will be fully disclosed by means of publications in international peer-reviewed journals and by oral/poster presentations at national and international scientific meetings. Both positive and negative findings will be disclosed.