This is a multicenter, randomized, quadruple-masked, placebo-controlled, parallel-arm pragmatic clinical trial to determine the effects of percutaneous PNS on postoperative analgesia and opioid requirements, as well as physical and emotional functioning, the development of chronic pain, and ongoing quality of life. The primary Specific Aim of the trial is to determine the effect of percutaneous PNS on postoperative opioid requirements and analgesia following moderate-to-severely-painful ambulatory surgery (under the usual conditions in which PNS will be applied, making this a "pragmatic trial"). Secondary Specific Aims are to determine the effect of percutaneous PNS on physical and emotional functioning, chronic pain, and quality of life following moderate-to-severely-painful ambulatory surgery.
Anthropomorphic and demographic characteristics as well as baseline end points will be recorded/measured. Surgical procedures will include rotator cuff repair, ankle arthrodesis, ankle arthroplasty, and hallux valgus correction ("bunionectomy").
Lead implantation. Preoperatively, participants will have a percutaneous lead (MicroLead™, SPR Therapeutics, Inc., Cleveland, OH) inserted to target the brachial plexus (shoulder) or sciatic nerve (foot/ankle) under ultrasound guidance. Patients will be positioned either supine (brachial plexus) or prone (sciatic) and have the lead site prepared with chlorhexidine gluconate/isopropyl alcohol solution and sterile drapes. An ultrasound and linear or curved array transducer within a sterile sleeve will be utilized for lead implantation.
The stimulating probe will be inserted into an introducer "sleeve" and then passed through a lidocaine skin wheal to approximately 2 cm from the epineurium of the target nerve. The probe will be connected to an external pulse generator or "stimulator" (SPRINT® PNS System®, SPR Therapeutics, Inc., Cleveland, OH) with a surface return electrode placed on an ipsilateral limb. Electric current will be delivered at 100 Hz with the intensity slowly increased from zero. The pulse generator intensity setting spans a range of 0 (no current) to 100 (maximum), indicating a combination of amplitude (0-30 mA) and pulse duration (10-133 µs). The optimal sensory changes will target the surgical area; and, if sensory changes occur in a different location or muscle contractions are induced, the stimulator will be switched off, and then the probe/introducer advanced or withdrawn and readvanced with a slightly different trajectory.
This process will be repeated until sensory changes (often described as a "pleasant massage") are perceived in the surgical area. The current will be decreased to zero and the stimulating probe withdrawn from the introducing sleeve, leaving the latter in situ. An introducing needle which is preloaded with the lead will be inserted through the sleeve. The introducing needle-sleeve combination will then be withdrawn, deploying the lead.
The lead will again be connected to the stimulator to ensure lead dislodgement did not occur during deployment (if so, a new lead will be inserted). Wound closure adhesive (2-Octyl 2-cyanoacrylate) will be applied to the exit point, a connector block attached to the lead approximately 2 cm from the skin entry point, the excess lead removed with a sterile scissors, and the lead entry site covered with a sterile dressing. The lead will be connected to the stimulator a final time and settings recorded. The stimulator will be removed leaving the lead in situ.
Immediately prior to surgery, participants will receive an ultrasound-guided single-injection interscalene (shoulder) or popliteal-sciatic (foot/ankle) nerve block with 20 mL of ropivacaine 0.5% or bupivacaine 0.5% (with epinephrine). For surgical anesthesia, participants will receive a general anesthetic with intravenous propofol or inhaled volatile anesthetic in nitrous oxide and oxygen. Intravenous fentanyl, hydromorphone and/or morphine will be administered intraoperatively, as needed.
Treatment group assignment. After confirmation of successful lead implantation, participants will be randomly allocated to one of two possible treatments: receiving either electric current (experimental group) or not (sham/control group). Randomization will be stratified by institution and anatomic lead location in a 1:1 ratio and in randomly chosen block sizes using computer-generated lists by the informatics group of the Department of Outcomes Research at the Cleveland Clinic. Treatment group assignment will be conveyed to the enrolling sites via the same secure web-based system used to collect and collate all post-intervention outcomes (Research Electronic Data Capture, Cleveland Clinic, Cleveland, Ohio). The pulse generators (SPRINT® PNS System®, SPR Therapeutics, Inc., Cleveland, OH) are capable of being programmed to either (1) pass electrical current; or (2) not pass electrical current. Importantly, these 2 modes (active and sham) are indistinguishable in appearance, and therefore investigators, participants, and all clinical staff will be masked to treatment group assignment, with the only exception being the unmasked individual who programed the stimulator and was not involved in subsequent patient assessments. The unmasked personnel who programmed the pulse generator will provide the programmed unit in the off position to the individual interacting with the subject.
Intraoperative course. The primary surgical anesthetic will be a general anesthetic, spinal anesthetic or exclusively the preoperative single-injection peripheral nerve block(s). Anesthetics that are also analgesics such as ketamine will not be used: the only permitted analgesic will be intravenous fentanyl, which is anticipated to be minimal since all subjects will receive a single-injection peripheral nerve block immediately prior to surgery.
Postoperative course. Within the recovery room following surgery, the stimulators will be attached to the leads and activated. Operating and recovery room pharmacologic analgesic requirements will be recorded. Subjects will be informed that during postoperative active treatment with electrical current patients do not always have the sensations experienced during preoperative lead placement and once proper placement is confirmed with comfortable sensations, therapeutic levels of stimulation may be delivered sub-threshold (below the intensity required for sensation and still provide relief, which is factual/accurate). This protocol will ensure a randomized, double/quadruple-masked, sham/placebo-controlled trial. Unmasking will not occur until statistical analysis and manuscript preparation are complete (termed "quadruple masked").
Prior to discharge, subjects and their caretakers will be provided with verbal and written instructions, the DVPRS scale (pain scale 0-10), and the telephone and pager numbers of a local investigator available at all times during the first two weeks of treatment. Subjects will be discharged home with their leads in situ. Subjects will be also be discharged with a prescription for immediate-release oral opioid, preferably oxycodone 5 mg tablets, taken for breakthrough pain.
We will attempt to contact subjects the evening of POD 0 to review stimulator instructions, although it is not always possible due to logistical reasons such as a late recovery room discharge. Subjects will be contacted by telephone for end point collection beginning on POD 1. Lead removal will occur on postoperative day 14 (+/- 3 days) by healthcare providers. This procedure encompasses simply removing the occlusive dressing and gently pulling on the lead. For resistance during lead withdrawal, lidocaine 1-2% (1-10 mL) may be infiltrated around the lead to relax the peri-lead muscle. Following study completion, the results will be mailed electronically or by the United States Postal Service to all enrolled subjects in written form using non-technical language.
Outcome measurements (end points). We have selected outcome measures that have established reliability and validity, with minimal inter-rater discordance, and are recommended for pain-related clinical trials by the World Health Organization and the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) consensus statement. Importantly, nearly all outcome measures are common data elements from the National Institute of Neurological Disorders and Stroke (NINDS). End points will be evaluated on postoperative days 0, 1, 2, 3, 4, 7, 11, and 18 as well as months 1, 4 and 12.
Demographic and medical history. Subjects will have demographic and anthropomorphic data collected including age, sex, height, weight, educational level, employment status, marital status, and U.S. military service (e.g., none, discharged, active). In addition, the medical history will be collected. Since post-traumatic stress disorder (PTSD) may be associated with the severity of pain, at baseline we will apply the PTSD Checklist (PCL-C), a 20-item self-report measure reflecting symptoms of PTSD validated in military, Veteran, and civilian populations.
Postoperatively, surgical endpoints will be recorded such as surgical duration, tourniquet duration (if applicable), analgesic administration, anesthetic administered, and any sedative agents provided. In addition, subjects will have baseline end points measured including a pain score at the surgical site using the Numeric Rating Scale (NRS, 0-10).
Data collection. Much of the surgical data from the day of surgery will be extracted from electronic health records to leverage data collection that occurs in health care delivery rather than requiring independent research data collection. Subject demographic, surgical and percutaneous PNS administration data will be uploaded from each enrolling center via the Internet to a secure, password-protected, encrypted central server (RedCap, Department of Outcomes Research, Cleveland Clinic, Cleveland, Ohio). All data collection following the day of enrollment (postoperative day 0)-regardless of enrolling center-will be collected by telephone from the University of California San Diego. Staff masked to treatment group assignment will perform all assessments.
Statistical Plan and Data Analysis. Randomized groups will be compared for balance on baseline characteristics using descriptive statistics and the standardized difference (i.e., difference in means or proportions divided by pooled standard deviation). Absolute standardized differences larger than 0.10 will be considered imbalanced and the corresponding variables considered for adjustment in all analyses. Primary analyses will be modified intent-to-treat, such that all randomized patients who receive at least some of the study intervention will be included in the analyses. All patients will be analyzed in the group to which they were randomized.
Primary Aim. For Specific Aim 1 we will estimate the treatment effect of PNS versus usual and customary care on pain and opioid consumption using a joint hypothesis testing framework. Specifically, we will conclude PNS is more effective than usual and customary analgesia if it is found to be superior on at least one of pain score or opioid consumption and not worse, i.e., noninferior, on both.
Noninferiority Testing. We will first test for noninferiority of PNS to usual care on each of the two outcomes using 1-tailed tests. The noninferiority deltas will be 1 point (worse) in pain score and 20% higher in opioid consumption. Noninferiority will be assessed at the overall (1-tailed) 0.025 significance level with no adjustment to the significance criterion for testing two outcomes since noninferiority is required on both outcomes - i.e., an intersection-union test. A noninferiority delta of 1 point in pain score is appropriate for between-group comparisons because it is about half the difference that would be considered clinically relevant for intra-subject changes: receiver operating characteristic curve analysis has demonstrated that changes from baseline of at least 1.7 along a 10-point NRS accurately identified patients who rated improvements as "much improved" or more, compared with those who perceived no change or worsening following analgesic interventions.
We will assess noninferiority on pain score using a 1-tailed t-test which incorporates the noninferiority delta of 1 point. The estimated treatment effect for pain score will be derived from a linear mixed effects model with the outcome of patient's "average" pain score for each day (1,2,3,4,7), with fixed effects for intervention (PNS vs usual care), time (days 1 through 7) and baseline average pain score, and assuming an autoregressive (AR(1)) correlation structure among the measurements on the same patient over time. We will then test for noninferiority with a 1-tailed t-test in which the numerator is the estimated treatment effect from the model minus the noninferiority delta (1), and the denominator is the standard error of the estimated treatment effect. This method will yield results similar to comparing groups on the patient mean across these seven days but is more flexible since it allows for missing data and also directly accounts for the correlation within patient. The model further allows assessing the treatment-by-time interaction, but this will be only of secondary clinical interest. As a sensitivity analysis we will relax the normality assumption and assess the treatment effect (plus test for noninferiority) on pain score over time using a mixed effects quantile regression model 1 in which we consider patient as a random effect, report the treatment effect as the difference in median pain scores, and use the same noninferiority delta of 1.
Cumulative opioid consumption is not typically normally distributed, and usually approximates a log-normal distribution, as in the pilot trial. We therefore plan to assess the treatment effect of PNS versus usual care on the log-transformed cumulative consumption through POD 7 using a linear regression model in which we adjust for any imbalanced baseline variables. The estimated treatment effect (i.e., difference between groups) will then be used in a noninferiority test with null and alternative hypotheses as: H0: µ1 - µ2 ≥ log(1.2) = 0.263 versus HA: µ1 - µ2 < log(1.2) = 0.263, where µ1 and µ2 are the means of log-transformed opioid consumption for PNS and usual care, respectively, and µ1 - µ2 is estimated by the coefficient (i.e., beta) for PNS versus usual care in the regression model. The estimated treatment effect in the model will also be an estimate of the ratio of geometric means for the two groups, assuming data for each group is log-normal with similar coefficient of variation between groups.
Superiority Testing. If noninferiority is found on both pain and opioid consumption we will test for superiority on each outcome using 1-tailed tests in the same direction. For superiority testing, since superiority on either outcome would be sufficient to reject the joint null hypothesis (i.e., a union-intersection test), we will control the type I error at 0.025 across the 2 outcomes by using a Bonferroni correction and using 0.025/2=0.0125 as the significance criterion.
Secondary Outcomes. We will use a linear mixed effects model to assess the treatment effect over time for additional outcomes measured at days POD 1-7 (1, 2, 3, 4, 7), as in the primary analysis, including worst pain and the Defense and Veterans Pain Rating Scale; similarly we will assess the treatment effect on total severity score and total interference score at days 3 and 7. As sensitivity analyses we will also use a generalized ordinal regression model for each of these outcomes. For outcomes analyzed at a single time point (days 11, 18; months 1, 4, 12) we will use 2-sample t-test or Wilcoxon rank sum test for physical and functioning as measured by the Brief Pain Inventory (Hypothesis 3), chi-square analyses and t-test of Wilcoxon rank sum test for incidence and intensity of chronic pain, respectively (Hypothesis 4), and Wilcoxon rank sum test for quality of life measure by the World Health Organization Quality of Life-BREF Instrument. Analogous regression models would be used, as needed, to adjust for baseline imbalance.
Study-wide Type I error control. We will use a parallel gatekeeping procedure to control the study-wide type I error at 0.05. For this procedure we a priori prioritize the study outcomes into 10 ordered sets, as follows:
Set Outcome(s) Measurement Timing ^
- Primary outcomes POD 1-7 [Average pain, opioid consumption]
- Worst pain score POD 1-7 DVPRS POD 1-7
- BPI interference subscale POD3, POD7
- Worst pain POD 1-11 DVPRS " Average pain "
- Worst pain Months 4 and 12
- Worst pain POD 18 DVPRS " Average pain "
- Worst pain Month 1 DVPRS " Average pain "
- Worst pain Month 4 DVPRS " Average pain "
BPI interference subscale Months 1, 4, and 12 WHO-DAS "
- Additional outcome measures and time points, such as least and current pain levels (from the BPI) will be considered exploratory and not compared statistically ^ throughout, POD 1 refers to POD 0 after PACU through POD1
Analysis will proceed in that order, and testing will proceed through each "gate" to the next set if and only if at least one outcome in the current set reaches significance. The significance level for each set will be 0.025 [for each direction of interest; primary outcomes being 1-sided and all others 2-sided] times a cumulative penalty for non-significant results in previous sets (i.e., a "rejection gain factor" equal to the cumulative product of the proportion of significant tests across the preceding sets). Within a set, a multiple comparison procedure (Bonferroni or Holm-Bonferroni correction) will be used as appropriate to control the type I error at the appropriate level.
Assessment of treatment effect heterogeneity. There is little relevant prior experience with the study intervention in the patient population of the proposed investigation, so it is not known whether either sex would interact with the treatment effect. Therefore, in accordance with the Human Subjects recommendations, we will assess the treatment effect of PNS on the primary outcomes of interest (pain score, opioid consumption) within levels of sex, and asses the interaction. In addition, we will assess treatment effect heterogeneity across within anatomical locations across the various lead insertion sites, across types of surgical procedures, and across levels of other baseline characteristics as listed below. We will assess the treatment-by-covariate interaction in the appropriate statistical model (i.e., the model used in the primary analyses). We will report the treatment effect within levels of each factor whether or not a significant interaction (P<0.10) is found.
We will assess treatment effect heterogeneity across levels of the following variables:
- sex (male, female)
- military (BAMC, WAMC, WRNMMC and NMCSD) vs. civilian (Cedars and UCSD)
- baseline average NRS (< 4, ≥ 4)
- baseline DVPRS (< 5, ≥ 5)
- baseline interference scale of the BPI < 20, ≥ 20)
- duration of surgery (< 90 min, ≥ 90 min)
- bupivacaine vs. ropivacaine (for the initial peripheral nerve block)
- saphenous nerve block (versus not) for lower extremity surgeries
- surgical site (shoulder, foot, ankle)
- surgical procedure (rotator cuff repair, hallux valgus, ankle arthrodesis, ankle arthroplasty)
- for brachial plexus leads: lead positioning (posterior to roots, superior trunk, middle trunk, other)
- for sciatic leads: lead positioning (medial, lateral)
- for sciatic leads: lead positioning (anterior, posterior)
Missing Data. While based on our pilot study (UG3) results very little missing outcome data is expected, any missing data will be summarized overall and by randomized group along with the known/presumed etiology of the absence. If the missing data for an analysis appear to be missing at random for an outcome which is only designed to be measured once for a patient, we will assign values using multiple imputation (using 5 imputed datasets, and aggregating results across them) in which all other available baseline and outcome data will be used to predict the missing data point(s). For longitudinal outcomes such as the primary outcome pain score, if data appear largely to be missing at random and with comparable frequency between groups, and all patients have at least some non-missing data, we will ignore the missing data for the primary analysis. If there would be a non-trivial amount of missing data (e.g., > 10 percent missing) for a particular outcome, and the data did not appear in general to be missing at random, we would consider implementing a pattern mixture model approach in which randomized groups are compared on outcome within subgroups defined by the pattern of missing data, for e.g., with results then aggregated across patterns.
Interim Analyses for Efficacy and Futility. A substantive difference from the planning phase is that in the full trial we will conduct interim analyses to assess efficacy and futility at each 25% of the maximum planned enrollment. We will use a group sequential design with gamma spending function8 and gamma parameters of -4 (quite conservative) for efficacy and -2 (moderately conservative) for futility. Assuming the alternative hypotheses were true, the probability of crossing a boundary for either efficacy (mainly) or futility at the first through fourth looks would be 0.07, 0.36, 0.75 and 1.0, respectively.
Sample size Justification and Considerations. Sample size parameters for the implementation phase were informed from our estimates in the planning phase which included N=31 Stimulation and N=34 Placebo patients. For this full trial we choose a sample size which will maintain an overall 90% power at the 0.025 significance level (since 1-tailed tests) to claim the intervention more effective than the control on postoperative opioid requirements and pain as measured by NRS pain score in our joint hypothesis testing framework. We plan the study to have 90% power to detect superiority on either outcome and at least noninferiority on both. Power for the joint hypothesis testing will be driven by superiority tests since superiority is needed for at least 1 of the 2 outcomes.
Opioid consumption. For cumulative opioid consumption through POD 7 our pilot study data had a coefficient of variation (CV) of 136% (mean (SD) of 17.9 ± 24.3 mg) for the Stimulation patients, 109% (mean (SD) of 17.9 ± 24.3 mg) for Placebo patients, and 142% (mean (SD) of 48 ± 68) overall. The ratio of geometric means (97.5% CI) in the pilot study was 0.20 (0.07, 0.57), for an 80% observed relative reduction, with confidence interval including as small as a 43% reduction.
For the implementation phase we conservatively assume a coefficient of variation of 150% for each group in opioid consumption through 7 days and plan for at least a 40% relative reduction. With these assumptions we will need a total of N= 228 patients to have 90% power to detect a relative reduction of 40% or more (i.e., ratio of geometric means of 0.60 or stronger) in mean opioid consumption at the overall 0.025 1-tailed significance level (0.0125 for each of the two 1-tailed tests for superiority). We use 1-tailed tests here because in the analysis we will only test for superiority after noninferiority of stimulation to placebo has been found. After adjusting for interim analyses the required maximum total sample size is 250 (125 per group).
With a sample size of 250 total we would further have 90% power to detect noninferiority in opioid consumption using a noninferiority delta of 1.2 for the ratio of geometric means after assuming a coefficient of variation of 150% and a true ratio of means of 0.75 or more. For a scenario with equal means (ratio of 1.0) we would only have about 25% power to detect noninferiority.
Pain score. In our pilot study we observed a reduction in the mean (97.5%CI) of average pain score of -1.7 (-2.5, -0.85) in Stimulation versus Placebo in the linear mixed effects model across POD 1-7. We also observed a within-group standard deviation of pain score ranging from 1.1 to 2.6 across POD 1-7, and values of 1.1 for Stimulation and 1.7 for Placebo for the patient mean across those days. Finally, we observed an intraclass correlation of 0.47 for pain score in the linear mixed effects model across POD 1-7. We used these estimates below in assessing the power and sample size for average pain score the implementation phase.
A difference between groups of 1.0 in average pain score is the smallest that would be considered clinically important. With a maximum total sample size of 250 we will have 95% power at the overall 0.025 1-tailed significance level (0.0125 for each of the two 1-tailed tests for superiority) to detect a difference of 1.0 or more between Stimulation and Placebo on mean pain score conservatively assuming a SD of 2.5 for pain score at each day (1, 2, 3, 4, 7) and ICC of 0.50.
Power for Subgroup Analyses. A main difference from the Planning/Pilot phase is that in this full trial we will have sufficient data to conduct the subgroup analyses and we also will have power to detect smaller treatment effects. For example, with 250 total patients, we would have about 90% power to detect a ratio of geometric means of 0.50 or stronger (smaller than observed in the pilot study) in subgroups of size N=125.
The overall significance level will be 0.025 for the primary aim when assessing noninferiority and superiority in 1-tailed tests, and 0.05 when assessing for superiority on secondary outcomes in both directions. SAS statistical software (Cary, NC) will be used for all analyses, and East 6.0 (Cytel, Inc. Cambridge, MA) for interim monitoring and sample size calculations.