The OPTIMIZE Study is a multisite comparative effectiveness trial using SMART (sequential multiple assessment randomized trial) design , with recruitment sites in 2 U.S. cities. SMART design allows for the assessment of adaptive interventions using prespecified decision rules to tailor treatment strategies to individual patients . Figure 1 illustrates the study design. After informed consent and baseline assessment, participants will be randomized to receive 8 weekly sessions of phase-1 treatment with either PT or CBT. These treatments were selected on the basis of their common use [17, 18], supporting evidence , and lack of a previous head-to-head comparison in patients with chronic low back pain.
Approximately 10 weeks after enrollment, participants who have not experienced adequate treatment response (i.e., 50% reduction in pain-related disability) to their assigned treatment will be randomly assigned to receive 8 weekly sessions of a new phase-2 treatment: 1) crossing over to the alternate phase-1 treatment (PT to CBT or CBT to PT) or 2) initiating Mindfulness-Oriented Recovery Enhancement (MORE). The rationale for the choice of phase-2 treatment options was based on a growing but less well developed evidence base and the existence of a provider workforce trained in mindfulness interventions in chronic low back pain. Switching treatments allows evaluation of the sequencing effects of PT and CBT. Participants who respond to phase-1 treatment are permitted up to 2 additional sessions during phase 2 to facilitate their transition to self-management. Outcome assessments are conducted at 10, 26, and 52 weeks after initial randomization. We scored the design of the OPTIMIZE Study using the 9 domains of the PRECIS-2 (pragmatic-explanatory continuum indicator summary-2)  on a scale of 1 to 5 and rated the study as more pragmatic than explanatory (Fig. 2 and Table 1).
The study design addresses 3 major deficits of previous investigations. First, given that many previous trials have shown small or equivocal effect sizes in terms of disability and pain, especially when averaged across study populations, our large sample size allows detection of smaller average treatment effects across the study population. Second, because of its large sample size, our study will have the statistical power to indicate whether particular treatment strategies are beneficial within subgroups based on specific patient characteristics. Third, the use of SMART design allows for the evaluation of sequences of treatments for participants who do not respond to the initial treatment.
Ethical review and approval were received from a local institutional review board (IRB), acting as the single IRB for this multisite study. Recruitment and local considerations were ceded to the individual site IRBs. Written consent was documented at 2 participating institutions and waived in lieu of verbal consent at 1 institution. Documentation of consent was obtained from all participants before study enrollment.
The study comprises 3 broad objectives that each include a cluster of interrelated specific objectives.
At week 10, we will compare the effectiveness of phase-1 treatments (PT vs. CBT)
At 1 year, we will compare the effectiveness of phase-2 treatments (MORE vs. the alternate phase-1 treatment [herein, “switching”]) among nonresponders to phase-1 treatments in terms of
At 1 year, we will compare the effectiveness of phase-1 treatments (PT vs. CBT)
Eligibility criteria were designed to recruit a representative sample of patients with nonspecific chronic low back pain who recently sought healthcare for their condition. Reasons for ineligibility or nonparticipation will be monitored and recorded.
Eligibility criteria are as follows:
Chronic low back pain will be operationalized using the National Institutes of Health Task Force criteria based on 2 questions: 1) “How long has low back pain been an ongoing problem for you?” and 2) “How often has low back pain been an ongoing problem for you over the past 6 months?” Responses of “greater than 3 months” to question 1 and “at least half the days in the past 6 months” to question 2 will be required. Participant eligibility will be based on pain intensity scores of > 4 on the NRS and disability of ≥24% on the ODI.
Patients will be excluded from the study for the following reasons:
OPTIMIZE will be conducted at 3 healthcare systems in the U.S.
Across study sites, potential participants will be informed of the study during healthcare visits with primary care providers. Alternatively, we will search the electronic health record (EHR) monthly to identify individuals with International Classification of Diseases, Tenth Revision codes indicating nonspecific low back pain (codes M47.817, M51.26, M51.27, M51.36, M51.37, M54.16, M54.17, M54.3, M54.4, M54.5, M54.89, M54.9, M99.03, M99.04, S23.9XXA, S33.5XXA, or S33.6XXA). Potential participants identified through the EHR will be sent an invitation letter via electronic or postal mail describing the study and providing instructions on how to opt out of additional contact or to opt in by contacting study personnel. Study personnel will attempt to contact by telephone those individuals who neither opt in nor opt out after 5 days.
Individuals interested in participation will be screened for eligibility using a telephone screener. Eligible individuals interested in participation will provide informed consent verbally or through a consent cover letter provided through Research Electronic Data Capture (REDCap), a Health Insurance Portability and Accountability Act–compliant, secure, electronic data capture system . After provision of consent, participants will complete the baseline assessment through REDCap, supplemented by telephone assessment conducted by study personnel.
The OPTIMIZE Study uses a SMART design involving 2 randomizations: one occurring after the baseline assessment and, for nonresponders, one occurring after the week-10 assessment. For each randomization, a computer-generated scheme will be used to randomize participants in a 1:1 ratio in blocks of random sizes stratified by enrollment site. Randomization will be administered centrally through the REDCap system .
It is impossible to mask treatment assignment from participants, healthcare providers, and study coordinators; however, study personnel who are responsible for baseline and follow-up assessments conducted through REDCap will be blinded to initial randomization assignment and re-randomization assignment, when applicable.
Assessments will be conducted at baseline (before randomization) and at weeks 10, 26, and 52 after enrollment (Fig. 1 and Table 2). The week-10 assessment corresponds to the end of phase-1 treatment, at which time, patients who did not respond to phase-1 treatment will be re-randomized. The week-26 assessment corresponds to the completion of phase-2 treatment. The 1-year assessment will permit evaluation of long-term treatment effects.
Our 2 co-primary outcome measures are low back pain–related disability and pain intensity.
The ODI is a 10-item measure of low back pain–related disability that assesses the current effects of a patient’s low back pain on various aspects of daily living. ODI scores range from 0 to 100, with higher scores indicating greater disability .
Pain intensity will be assessed using an 11-item NRS ranging from 0 (“no pain”) to 10 (“worst imaginable pain”). Separate ratings will be recorded for current, best, and worst pain intensity during the previous 24 h .
The change in ODI value from baseline will be used to define a treatment responder. We previously evaluated ODI responder thresholds and found that patients who achieve at least 50% improvement are highly likely to consider themselves “a great deal” or “a very great deal better” . We consider 50% or greater improvement in ODI from baseline to represent response to treatment.
We will use the PROMIS to assess physical, mental, and social health using the PROMIS-29 short form. The health domains assessed will be pain interference, physical function, fatigue, anxiety, depression, sleep disturbance, and ability to participate in social roles and activities (herein, “social roles and activities”) .
We will ask participants to self-report opioid use at each assessment if they have used opioids for their low back pain during the past 90 days. For those responding “yes,” we will ask whether the patient has used opioids for their low back pain “daily or near daily in the past 90 days.” Daily or near daily use of opioids for at least 120 days is considered long-term opioid use .
We will ask participants to self-report healthcare utilization at each assessment, including provider visits (e.g., primary care, complementary providers, emergency department, or surgical consults for low back pain), imaging (e.g., radiographs, magnetic resonance imaging), and procedures (e.g., injections, surgery).
To characterize our participant sample, we will collect detailed demographic and clinical data at baseline (before randomization). Demographic data will consist of participant age, sex, race/ethnicity, employment status, and tobacco use and will be assessed through participant self-report. Clinical data will consist of general medical and low back pain history (e.g., previous back treatments and use of opioid medication). Demographic variables will be used to create patient subgroups and to determine possible confounding variables that may affect prognosis.
We will collect information about physical adverse effects (e.g., increased pain, stiffness) and psychological adverse effects (e.g., increased depression, anxiety) that participants report during week-10 and week-26 assessments. A questionnaire will ask participants whether they experienced any adverse effects and the extent to which they believe these adverse effects are related to study treatment (ranging from “not at all” to “extremely”) [27, 28].
We will assess each patient’s risk for poor outcome at baseline (before randomization) on the basis of psychological and physical risk factors using the STarTBack Screening Tool [29, 30] to characterize participants as having high, medium, or low risk for poor outcomes. Screening results from the STarTBack tool will be evaluated as a potential subgrouping variable.
In the setting of this pragmatic effectiveness trial, we will document barriers to implementation of study interventions to inform future implementation efforts. We will record barriers encountered across study sites using the Consolidated Framework for Implementation Research . The Consolidated Framework for Implementation Research categorizes barriers into the following 5 domains: 1) characteristics of the intervention (e.g., aspects of the treatment); 2) outer setting (e.g., factors outside of the clinic and individual health systems); 3) inner setting (e.g., clinic environment); 4) providers (e.g., characteristics of the clinicians); and 5) process of intervention implementation. In addition to identifying and characterizing the barriers to implementation, we will record whether each barrier is ongoing or resolved and any actions taken to remedy the barrier.
All treatments will be provided by licensed providers who have at least 1 year of experience working with patients with chronic pain and who have been trained in study-related procedures by the investigators.
The initial treatment session will be provided within 30 days of randomization (to phase-1 or phase-2 treatment). All treatments will be provided during individualized weekly sessions over an 8-week period. To accommodate participants’ schedules, we will allow up to 2 sessions to be provided during the same week, but no more than 8 sessions will be received during the 8-week treatment period in phase 1 or phase 2. At the week-10 assessment, participants who are determined to have responded to phase-1 treatment may schedule 1 or 2 additional treatment sessions to finalize a self-management plan and discuss relapse prevention or other pertinent topics. The treatment approaches in this study are designed to be pragmatic, focusing on provision of evidence-based care but allowing tailored application of this care according to each patient’s needs.
Physical therapists will provide evidence-based PT for chronic low back pain consisting of patient education, exercise instruction, and manual therapy (Table 3) [9, 32]. Education will focus on reassurance, positive recovery expectations, addressing maladaptive pain perceptions, and the importance of physical activity  and may be tailored to individual patients’ needs based on the STarTBack Screening Tool . Exercises will address general conditioning and physical activity, as well as deficits in strength, flexibility, and postural control tailored to the clinical presentation and needs of individual patients. Manual therapy may include various hands-on techniques tailored to the spinal mobility deficits of individual patients.
CBT will be provided by behavioral health providers, including psychologists, advanced practice nurses, social workers, or other licensed providers with behavioral health training. The CBT protocol is adopted primarily from that of Thorn , as well as studies by Cherkin et al.  and Lamb et al. , showing effectiveness of CBT in patients with chronic low back pain. Patients will receive 8 sessions focused on key components of effective CBT (Table 4): 1) education about the biopsychosocial model of pain and its association with thoughts, feelings, and behavior 2) identifying and reframing maladaptive cognitions, 3) developing pain coping strategies (e.g., relaxation and positive coping statements), 4) setting and working toward behavioral goals using activity pacing, and 5) developing skills for self-management and relapse prevention [36, 37]. Depending on the judgment of the behavioral health provider, 2 additional CBT sessions may be offered to the patient to further address self-management and relapse prevention. Each course of CBT will begin with a psychosocial assessment (e.g., pain catastrophizing, fear of movement) and clinical interview. Patients will be instructed about activities to perform on their own between sessions and for ongoing self-management.
MORE will also be provided by licensed behavioral health providers. The MORE program used in this study is designed specifically to address symptoms and underlying cognitive-affective mechanisms of chronic pain (Table 5) . MORE will be provided in 8 individual sessions emphasizing 3 core therapeutic approaches:
Each course of MORE will begin with a psychosocial assessment and clinical interview. Patients will be instructed about activities to perform on their own between sessions and for ongoing self-management.
The study team has developed several mechanisms to enhance treatment fidelity for these study interventions. Mechanisms include provider training, structured intervention manuals and resources, and ongoing monitoring through the use of fidelity checklists embedded in the EHR.
Study investigators develop a rigorous training schedule and materials for those who are providing the study interventions. Providers receive 12 h of training in study procedures and are provided manuals and online resources outlining core components for each treatment group. Initial training is conducted during an 8-h in-person workshop emphasizing demonstration and practice. PT and behavioral health providers will receive ongoing training through quarterly 1-h telephone calls led by an intervention leadership team to review protocols, reinforce skills, and discuss clinical issues. The calls will be discipline specific (i.e., a separate series of calls for PT and for behavioral health).
For each of the 3 study interventions, the study team has developed structured intervention manuals that follow the 8-session format. The manuals offer guidance to healthcare providers and include informational handouts and worksheets for participants.
Providers complete checklists built into the electronic medical record to document treatment sessions, providing a pragmatic assessment of treatment fidelity . We will use these checklists to determine whether core components of each study intervention are provided to participants. After each treatment session, the provider will complete fidelity checklists through the EHR.
All analyses will follow intention-to-treat principles, with participants evaluated on the basis of randomization assignment, regardless of compliance. Personnel at a biostatistics center at one of the enrollment sites will perform statistical analyses.
Our primary objectives are to compare the effectiveness of the phase-1 treatments and of the phase-2 treatments among phase-1 nonresponders. Our main secondary objective is to compare the effectiveness of each phase-1 treatment when followed by MORE or when followed by switching to the alternative phase-1 treatment. As exploratory objectives, we seek to identify which two-stage embedded treatment regime provides the best average outcome across the four 2-stage treatment strategies and to evaluate the primary and secondary treatment comparisons in prespecified patient subgroups.
Separate longitudinal linear models will be used to relate repeated assessments of our co-primary outcomes of disability and pain to phase-1 treatment (PT versus CBT), while controlling for baseline outcome score. Model parameters will be estimated using normality restricted maximum likelihood estimation . With this approach, treatment effect estimates will remain consistent and unbiased if missing data follow a missing-at-random pattern. Mean differences in ODI values and NRS scores at week 10 will be our primary assessment. Secondary comparisons of PT and CBT at weeks 26 and 52 will evaluate long-term effects of phase-1 treatment in the context in which nonresponders are assigned to a phase-2 treatment with equal probability.
A similar analytic framework will be used to compare the effects of phase-1 treatments (PT versus CBT) on secondary outcomes (physical function, anxiety, depression, fatigue, sleep disturbance, and social roles and activities). Weighted generalized estimating equations will be used to compare participant opioid use during the 1-year follow-up period between those who underwent PT vs CBT as phase-1 treatment . Differences at week 10 will again represent our primary assessment, with subsequent comparisons in the context of phase-2 treatment for nonresponders.
Subgroup analyses for phase-1 treatments will be performed by repeating the longitudinal analyses within each prespecified group and by adding interactions between phase-1 treatments and subgroup factors comprising age (< 50 or ≥ 50 years), gender, long-term opioid use (yes/no), and high risk according to the STarTBack screening tool.
To determine which treatment to use when phase-1 treatments do not provide adequate response, we will compare the effectiveness of switching to MORE versus CBT for phase-1 nonresponders to PT, and, in a separate analysis, we will compare the effectiveness of switching to MORE versus PT for phase-1 nonresponders to CBT. We plan separate analyses for the nonresponders to PT and CBT because the characteristics of these nonresponders may differ. These comparisons will be performed in the 2 sets of nonresponders using separate longitudinal linear models for our co-primary outcomes at weeks 26 and 52, with the phase-1 treatment and week-10 outcome scores used as covariates to account for the phase-1 treatment and its initial effects before implementing the phase-2 treatment.
Similar analysis will be conducted to determine the effectiveness in terms of secondary outcomes of phase-2 treatments among phase-1 nonresponders.
A preplanned secondary analysis will pool the estimates of the effects of phase-2 treatments across the 2 groups of phase-1 nonresponders. This analysis will receive particular emphasis if the overall study encounters a shortfall of recruitment or if treatment adherence is low, which would limit the statistical power of the primary comparisons performed separately in the nonresponders to PT and CBT.
We will compare the effectiveness of the 2 phase-1 treatments when followed by MORE in analyses that include all responders to the phase-1 treatments, as well as nonresponders who are randomized to MORE. By using weighted generalized estimating equations, we will compare disability and pain at weeks 10, 26, and 52 between the 2 phase-1 treatments. Inverse probability weights will account for nonresponders being re-randomized into 2 groups (switching vs. MORE) and, therefore, being underrepresented relative to responders to phase-1 treatment. Similar methods will be used to determine the effectiveness of phase-1 treatments followed by MORE in terms of secondary outcomes and within prespecified subgroups.
We will compare the effectiveness of the 2 sequences of the phase-1 treatments (i.e., CBT followed by PT vs. PT followed by CBT) by using analyses analogous to those described above for the comparison of the phase-1 treatments when followed by MORE. Analyses will include responders to the phase-1 treatments and nonresponders who were randomized to the alternate phase-1 treatment in phase 2.
Analyses addressing objectives 1 and 3 will use 2-sided α levels of 0.04 for the ODI and 0.01 for the NRS to assure a study-wide type-I error ≤ 0.05 across the 2 co-primary outcomes. Because the comparisons for objective 2 will be applied separately among phase-1 nonresponders to CBT and PT, we will use 2-sided α levels of 0.02 for the ODI and 0.005 for the NRS. This will ensure that the total type-I error for the objective 2 comparisons will not exceed α = 0.05 = 0.02 (for the ODI in CBT nonresponders) + 0.02 (for the ODI in PT nonresponders) + 0.005 (for the NRS in CBT nonresponders) + 0.005 (for the NRS in PT nonresponders). We will use different α levels for the 2 co-primary outcomes because the minimum clinically important difference for the NRS is larger in relation to its variability than it is for the ODI. (i.e., NRS scores are less variable because we expect to observe a larger difference in relation to its underlying variability than the difference we expect to observe in ODI values.)
Treatment will be assigned randomly at the participant level and provided by trained physical therapists, psychologists, and social workers. Although the statistical analyses described above will be performed at the participant level, we realize that there may be an effect of provider on treatment effect. To account for this, we will conduct planned sensitivity analyses within each broad objective to test for effects of clustering. First, we will evaluate whether treatment effects vary across sites. We will use a random effects model to test treatment effects in our primary and secondary objectives that include main effect for site and interaction effects between site and treatment group. Second, we will evaluate whether treatment effects vary across providers. Using a random effects model, we will add random effect terms for the participants’ index providers, recognizing that each participant may have more than 1 intervention provider.
Statistical power was evaluated under the assumption of an estimated 85% participant retention during the 1-year follow-up period. We have designated ODI value and NRS score as our co-primary outcomes and assume standard deviations of 12.5 and 2.2, respectively. We assume serial correlations of 0.13 and 0.23 for the ODI and NRS, respectively, between baseline and follow-up according to a previous study . The computations assume phase-1 responder rates of 30% to 45% [24, 45] and account for the type-I error rates described above. Each study intervention is an active treatment hypothesized to be beneficial; therefore, we base our power calculations on minimal clinically important differences in ODI (6 points) and NRS (2 points) [45, 46] instead of directional hypotheses for comparisons against control groups. Under the indicated assumptions, 945 randomized participants provide at least 99% power for the objective-1 and objective-3 comparisons and at least 89% power for the objective-2 comparisons when performed in the full randomized cohort. All of these comparisons have sufficient power to determine whether one treatment is clinically superior to the other or whether the mean difference between treatments is sufficiently small that the treatments can be considered clinically equivalent. The objective-1 and objective-3 comparisons retain at least 83% power when performed in subgroups that include at least one-third of the randomized participants.
The risks of the interventions are minimal because PT, CBT, and MORE are standard treatments used in everyday clinical practice. Through our study eligibility criteria (e.g., excluding those with serious pathology as cause of low back pain) and other procedures (e.g., requiring licensed providers to deliver interventions), we have attempted to minimize risks to participants. All investigators and research staff complete online tutorials and in-person training approved by their institutional review boards to comply with all regulations of the Office of Human Research Subjects Protection. A data and safety monitoring board composed of individuals with relevant expertise from outside the participating institutions will provide external safety monitoring for the OPTIMIZE Study.
Participant safety and confidentiality will be monitored continuously. Treatment providers, through training and ongoing conference calls, will report any potential adverse events to the site study coordinators. In addition, adverse events will be solicited at every assessment and, if they occur, will be recorded and reported in accordance with standard reporting guidelines of our respective institutional review boards and PCORI and our data and safety monitoring plan. The relatedness, expectedness, and severity of adverse events are adjudicated by the study investigators and data and safety monitoring board.