Spinal cord stimulation (SCS) is a recognised option for the management of chronic neuropathic pain with randomised controlled trials (RCTs) performed to investigate its effectiveness for conditions such as failed back surgery syndrome (FBSS),24 complex regional pain syndrome,20 and painful diabetic neuropathy.5 Conventional medical management has however been the comparator most commonly used in RCTs to date evaluating SCS for neuropathic pain.
Reports have suggested that at least some part of pain relief observed at early stages of SCS therapy may be the result of a placebo effect with long-term follow-up revealing loss of efficacy for a proportion of participants when compared with the earlier primary endpoint.8,19,21,25,33 It is widely accepted that use of placebo or sham controls in a clinical trial can reduce bias as the result of unblinding (knowing the treatment received) of patients and clinicians, and researchers can result in nonspecific treatment effects reported by patients. The literature suggests that factors relating to patient expectation of treatment success are central in the development of the placebo response; these are highly relevant in SCS use.49
In the past decade, several RCTs have evaluated SCS for neuropathic pain conditions when compared with a placebo arm. These RCTs have been possible due to the emergence of new sensation-free SCS modalities such as burst, high frequency, or high density. Despite difficulties with blinding, conventional or paraesthesia producing SCS has been compared with placebo in a number of small studies with varied results, including the effects of placebo stimulation being similar to those of active treatments.1,36
In our context, “placebo trials” are trials that specifically set out to select a comparator to “find out” what might be the placebo effect of the active intervention, eg, RCT of low-dose SCS vs traditional SCS (both groups get implant, etc). However, as we know, in this design, there is high likelihood that patients will be aware of their allocation, and therefore, the design is effectively “open label.” Within this framework, we could therefore define “sham trials” as a specific subgroup of placebo trials where there is the possibility to “fully blind” patients, clinicians, and researchers. In the neuromodulation setting, this would need to be an active intervention vs comparator that is completely paraesthesia-free, eg, RCT of HF10 vs no stimulation. Given the complexities in enabling a sham for a treatment such as SCS and for the purposes of this review, sham was defined as a control where all study procedures were equal between arms including implantable pulse generator (IPG) behaviour (ie, need for recharging). Placebo was defined as a control where the IPG was inactive and at least one of the study procedures was different between the arms (ie, no IPG spontaneous discharge, ie, built-in current leak), admitting overtly the possibility of unblinding.
We have recently conducted a systematic review that focused on the methodological facets of randomised placebo-controlled trials of SCS.9 The aim of this systematic review was to investigate the effectiveness of SCS for patients with neuropathic pain when compared with a placebo comparator arm.
The systematic review methods followed the general principles outlined in the Centre for Reviews and Dissemination (CRD) guidance for conducting reviews in health care.2 This systematic review is reported in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA).30 The protocol for this review is registered on PROSPERO as CRD42018090412. The current review focuses on the effectiveness results of SCS placebo-controlled trials in patients with neuropathic pain.
2.1. Search strategy
Electronic databases MEDLINE, CENTRAL, EMBASE, and WikiStim were initially searched from inception until February 2018 and updated on the January 29, 2019. The search strategies were designed using a combination of both indexing and free-text terms with no restriction on language. The search strategy used for the MEDLINE database is presented in supplementary material 1 of this article (available at http://links.lww.com/PAIN/A868). The MEDLINE search strategy was adapted to enable similar searches of the other relevant electronic databases. The reference lists of relevant systematic reviews and eligible studies were hand-searched to identify further potentially relevant studies.
2.2. Study selection
The citations identified were assessed for inclusion in the review using a 2-stage process. First, 2 reviewers independently screened all the titles and abstracts identified by the electronic searches to identify the potentially relevant articles to be retrieved. Second, full-text copies of these studies were obtained and assessed independently by 2 reviewers for inclusion using the eligibility criteria outlined in Table 1. Any disagreements were resolved through discussion at each stage, and, if necessary, in consultation with a third reviewer.
2.3. Data extraction
A data extraction form was designed to enable data extraction relating to study author and year of publication, country where the study was conducted, study design, population, number of participants included in the analysis, intervention including frequency of stimulation (if reported), details on placebo or sham comparator, duration of placebo or sham, consideration of carryover effect and washout periods (for crossover RCTs only), and efficacy outcomes assessed.
Data extraction was performed by 1 reviewer and checked for accuracy by a second reviewer. Any disagreements were resolved through discussion, and, if necessary, in consultation with a third reviewer.
2.4. Risk of bias assessment
We planned to assess risk of bias by using the revised Cochrane risk of bias tool (RoB 2.0) appropriate to the study design of the included trials. All the studies that met the eligibility criteria were crossover trials. Therefore, we used the RoB 2.0 specific for crossover trials.16 Risk of bias assessment of the included studies was undertaken by 1 reviewer and checked for agreement by a second reviewer. Any disagreements were resolved by discussion, and, if necessary, in consultation with a third reviewer.
2.5. Data synthesis
Our primary efficacy outcome was pain, reported on a validated scale such as the visual analogue scale (VAS; 0-10 or 0-100 mm) or the numeric rating scale (NRS; 0-10). To standardise to a single scale, we assumed that the VAS (0-10 cm) and the NRS (0-10) were equivalent, and we converted the VAS (0-100 mm) by dividing pain scores by 10.
The measure of treatment effect for data synthesis was the mean difference and SEM difference between active stimulation and control, to be pooled through the generic inverse variance method of meta-analysis.6
For crossover studies, we intended to extract in the first instance, the mean difference in pain scores between treatment periods, and a measure of precision which takes account of the paired nature of the data.13 If such data were not reported, or if we were concerned regarding carryover effect across treatment periods, we would have extracted the mean pain score and a measure of precision for the first treatment period only and treated these data as a parallel study in data synthesis.
Four included crossover studies reported data only for the pain scores at the end of all treatment periods (ie, the mean pain score and SD of all participants during that treatment period). The results do not reflect the paired (correlated) nature of the data and, if used in meta-analysis, would overestimate the variance of the pooled result. We received partial individual participant data for 1 study36 and used these data to estimate a within-participant correlation value between treatment periods of 0.517. We were then able to calculate the mean difference and the SEM difference taking account of the correlated structure of the data using the formulae described in the Appendix of Elbourne et al.13
We were also able to extract individual participant data for 10 participants in 1 study52 and used these data to estimate a within-participant correlation value between treatment periods of 0.963. We repeated all data synthesis using this correlation value to calculate the mean difference and the SEM difference. Numerical results of meta-analysis were similar, and conclusions were unchanged (results not shown, available on request from corresponding author).
Three of the crossover studies with mean difference and associated SE adjusted for the paired design included more than 1 active treatment period and a sham or placebo treatment period. To allow comparisons for each of the active treatments to the control treatment period to be included in meta-analysis without multiple counting of the control treatment period, we divided the number of participants included in the study by the number of comparisons when calculating the mean difference and associated SE.
2.6. Assessment of heterogeneity and subgroup analysis
We assessed the level of heterogeneity present between trials by visual inspection of forest plots and formally according to the I2 statistic (the percentage of variability between trials that is due to statistical heterogeneity). We anticipated that clinical heterogeneity would be present in analysis because of differences in study design and participant characteristics; therefore, we performed a random-effects meta-analysis.6
We also performed subgroup analysis to further investigate statistical heterogeneity; we assessed the duration of treatment (subgroups of 1-4 weeks) and type of control (sham, placebo, or other). Subgroup meta-analyses were also performed with random-effects because of anticipated heterogeneity between studies. We did not formally test for differences between subgroups; rather, we interpreted any visual differences in the pooled results across subgroups.
3.1. Study selection
The searches resulted in the identification of 1473 citations. After the removal of duplicate records, we identified 1309 potential citations. After initial screening of titles and abstracts, 35 publications were considered to be potentially relevant and were retrieved to allow assessment of the full-text publication. After review of the full-text publications, 8 studies were included in the review.1,4,23,29,36,39,46,52 Twenty-seven studies were excluded at the full-text paper screening stage because the comparator was not placebo or sham neurostimulation.3,5,7,8,12,17,18,20,22,24,27,31–34,38,40-45,47,48,50,51,54 The PRISMA flow chart detailing the screening process for the review is shown in Figure 1.
3.2. Characteristics of included studies
The characteristics of the 8 included studies are summarised in Table 2. All the included studies were crossover RCTs.1,4,23,29,36,39,46,52 Four studies restricted the participants to a specific condition such as FBSS1,36,39 or complex regional pain syndrome.23 Four studies included participants with a range of conditions.4,29,46,52
The type of stimulation investigated in the studies included paraesthesia inducing, subthreshold, burst, and high-frequency SCS. Two studies included patients new to SCS (ie, study was performed immediately after implantation of the device).1,4 One of the studies with patients new to SCS involved a trial period conducted with an external IPG system through externalised extension wires. Participants who completed the 28-day period of external stimulation then underwent permanent implantation of the SCS device.4 The remaining 6 studies included patients already receiving paraesthesia stimulation for at least 4 weeks before enrolment in the trial.23,29,36,39,46,52 The phases (ie, different settings) in the crossover RCTs ranged from 2 to 5 phases. The duration of each phase ranged from 1 week in 3 studies4,39,52 to 3 weeks in 1 study.1 One study included only a 12-hour interval before quantitative sensory testing assessment.29 The duration of each crossover phase was 2 weeks in 3 studies.23,36,46 Four of the studies did not consider a carryover effect or washout period between the different stimulation phases.1,4,39,52 In the studies that included a washout period, this consisted of a 12-hour,29 2-day,23 or 2-week washout period with their own paraesthesia stimulation.36,46
3.3. Risk of bias assessment
The summary of the risk of bias assessment is presented in Table 3. The full assessment for each included study is presented in supplementary material 2 (available at http://links.lww.com/PAIN/A868). Four studies were judged to have some concerns for the randomisation domain, as no information was presented about how the sequence was generated or concealed.4,29,46,45 Although some studies included an intervention arm where patients would feel paraesthesias23,29 and therefore would not be blind to intervention, other studies29,39,52 were judged to have a high risk of bias because of the possibility of a carryover effect (domain deviations from intended interventions). No information was presented in Tjepkema-Cloostermans et al.46 besides stating that the study was double-blind; therefore, it was judged as presenting some concerns of bias for the domain deviations from intended interventions. Four studies reported only information on patients who received the interventions and provided data at all assessment times (per-protocol analysis) or did not report how many patients were initially randomised.1,29,36,52 Therefore, it was considered there were some concerns of bias for the missing outcome data domain. There were some concerns of bias for the measurement of the outcome domain in 4 studies as outcome assessors were aware of the intervention received by study participants or no information was provided.4,23,29,46 One study did not perform statistical analysis appropriate for a crossover design,39 whereas another study did not report any analysis methods.4 There were some concerns with selective reporting in the studies by Al-Kaisy et al.,1 De Ridder et al.,4 and Kriek et al.23 The numerical results were provided only for statistically significant results. This omission includes test for carryover effect which was not presented because it was not statistically significant.1 It was considered that there were some concerns of bias regarding the selection of the reported result domain for these 3 studies. Overall bias of included studies ranged from some concerns to high risk of bias. None of the studies was considered to have a low risk of overall bias.
3.4. Outcomes of included studies
Pain outcomes, treatment satisfaction, and patient stimulation preferences for all included studies are presented in Table 4.
Twelve comparisons of an active stimulation and control treatment period, including 155 participants from 6 crossover studies, could be pooled in meta-analysis to investigate the effect on pain intensity (Fig. 2). We were unable to include any numerical results for 2 studies recruiting 29 participants within meta-analysis4,29 because of inadequate numerical data presented within the trial journal publications. Meta-analysis shows a statistically significant reduction in pain intensity (VAS 0-10 cm or NRS 0-10) during the active stimulation treatment periods compared with the control treatment periods, pooled mean difference −1.15 (95% confidence interval [CI]: −1.75 to −0.55, P = 0.001). There was a substantial amount of heterogeneity present between the comparisons (I2 = 65.8%).
3.5. Subgroup analyses
We performed subgroup analysis to further investigate the duration of treatment (subgroups of 1-4 weeks) and type of control (sham, placebo, or other) on the treatment effect.
Two studies had treatment periods of 1 week,39,52 2 studies had treatment periods of 2 weeks,36,46 1 study had treatment periods of 3 weeks,1 and 1 study had treatment periods of 4 weeks.23 Subgroup analysis by duration of treatment shows no clear differences in treatment effect according to the duration of the stimulation and control treatment period (Fig. 3). Duration of treatment is relevant particularly in respect of timing of pain data collection where some investigators have chosen to collect data only during the last 3 days of the period1,36 to minimise the impact of any carryover effect from the previous period.
Two studies used a sham control,1,36 3 studies used a placebo control,23,39,52 and 1 study used low-amplitude burst stimulation as the control treatment (Fig. 4).46 Subgroup analysis by type of control shows that the treatment effect of stimulation compared with control appears much larger in the studies using placebo control (pooled MD, −1.88, 95% CI −2.77 to −0.98) than the studies using sham control—IPG behaviour equal in all arms, ie, need for recharging (pooled MD, −0.34, 95% CI −1.04 to 0.36) and the study using low-amplitude burst stimulation (MD −0.20, 95% CI −1.01 to 0.61). However, a substantial amount of heterogeneity remains between the studies using placebo control (I2 = 65.2%).
To the best of our knowledge, this is the first systematic review of randomised placebo (“sham”)-controlled trials of SCS for neuropathic pain. Our meta-analysis of 6 crossover studies and a total of 155 participants have shown an average reduction in pain intensity (VAS 0-10 cm or NRS 0-10) during the active stimulation treatment periods compared with the control treatment periods of −1.15 (95% CI: −1.75 to −0.55, P = 0.001). The substantial statistical heterogeneity in effect across trials may be partly explained by the type of control. Exploratory subgroup analysis by type of control shows that the treatment effect of stimulation compared was larger in the studies using placebo control23,39,52 than the studies using sham control.1,36 We defined sham as a control when all study procedures were equal between arms including IPG behaviour (ie, need for recharging) as opposed to placebo where the IPG was inactive and at least one of the study procedures was different between the arms (ie, no spontaneous IPG discharge and no current leak). Presumably, a sham control is more plausible to participants and would be associated with a smaller potential of unblinding particularly where the participants have previous experience with SCS. Accidental unblinding during the placebo phase might reduce the impact of the placebo arm and consequently inflate the effect of the active intervention. However, included studies were generally poorly reported and had methodological limitations related to quality of blinding and handling of carryover effects due to crossover designs.
Despite limiting the scope of our review to subjects with neuropathic pain, we found a great deal of variation in pain conditions between the studies which varied from FBSS to general neuropathic pain with a range of conditions. Furthermore, the type of stimulation investigated included a wide range of modalities such as paraesthesia stimulation, subthreshold, burst, and varying kilohertz frequencies up to 5880 Hz. In addition, the determination of the perception threshold in studies using subthreshold stimulation has been performed in variable positions with a number of studies not reporting how the threshold was measured. Perceptual threshold for conventional paraesthesia-based SCS varies by about 25% with simple postural changes, and this could easily lead to unblinding.35 No study has yet evaluated the 10-kHz frequency against a sham control.
All 8 included studies used a crossover design with most including a number of treatment phases. To conduct a pairwise comparison of placebo vs various modes of stimulation, the study populations were divided into pairwise comparisons, and our statistical analysis was adjusted accordingly to take account of these different comparisons.
The use of a crossover design with a number of stimulation parameters and periods generates a risk of a carryover effect of active modes of stimulation spilling onto the placebo period. We note that, investigators used various strategies to address the carryover issue such as including a washout period varying from 12 hours29 to 2 weeks46 or collecting outcomes at the end of the crossover period.1,36 However, we consider that despite these mitigating strategies, estimating the impact of any carryover remains difficult to quantify. Indeed, in experimental animals, the duration of neuronal inhibition and pain relief by SCS often exceeds the stimulation period.14,28 These findings are consistent with clinical observations that analgesia not only occurs during the SCS but also often outlasts the period of SCS.15 In a study looking at intermittent vs continuous conventional SCS, Wolter and Winkelmüller suggest that in most patients, a clinically significant carryover effect is demonstrable during 90 minutes or less.53 Although clinical experience suggests the washout (as well as the wash-in) time is influenced both by the diagnosis and the stimulation mode, the fact remains that no reliable data on the duration of carryover effect are available. Therefore, it remains possible that the overall placebo effect in our meta-analysis has been increased by the carryover effect from active stimulation.
Only 2 studies examined the impact of the “period effect” or the order of the treatment introduction on outcomes. Perruchoud et al.36 concluded that the first treatment introduced produced the highest impact regardless of whether it was sham or active treatment; by contrast, Al-Kaisy et al.1 found no period effect in their study.
Another factor which may impact the magnitude of the response to a placebo device in the studies is the plausibility of the sham control or inactive device. A sham/placebo control may be more plausible in de novo patients who lack familiarity with the functioning of an SCS device and have limited knowledge of the handheld controller and no clear estimate of the recharging period after a particular mode of stimulation. By contrast, participants with long experience of SCS require a more robust placebo due to their ability to unmask a placebo device particularly where the recharging duration is drastically reduced.
Only 2 of the 8 studies recruited de novo participants.1,4 The De Ridder study4 was conducted entirely during the screening trial period where attitudes and expectations may differ from following an IPG implant.37 Al-Kaisy et al.1 used de novo patients as well as a robust placebo control including a controlled current leak from a rechargeable IPG; no handheld patient controller was issued throughout the study. As such in this study, 2 of the 3 frequencies tested produced pain relief that was not significantly different from placebo stimulation. By contrast, in the study by Kriek et al., the information on the placebo used is limited to “Programming placebo was performed with a 100-Hz stimulus to maintain an equal programming paradigm and sensation for the patient. However, the IPG was switched off immediately after ‘programming’ placebo stimulation and remained switched off during the coming 2-week test period.”23 Since the study tested high frequency as well as burst it is safe to assume that the participants were implanted with a rechargeable IPG. We, however, found no reference in the article to either the IPG being programmed to produce a current leak in the placebo phase nor could we find a clear indication of what arrangements were made to prevent accidental unblinding during the placebo phase based on a sudden reduction of need for recharging.
Apart from a single study that favoured placebo stimulation, all other studies favoured the test stimulation mode. However, the pain intensity forest plot needs to be interpreted with caution; for while the study by Perruchoud et al.36found no significant statistical or clinical difference between 5-kHz stimulation and sham, it remains a fact that, in the study, 5-kHz stimulation was better than placebo by a margin of 11% on the primary outcome measure. Yet, it may be argued that the electrodes were positioned to obtain the best overlapping paraesthesia rather than targeting Th9 to Th10 level. By contrast, the study of Tjepkema-Cloostermans found burst as well as low burst to be better than conventional stimulation.46 Since the authors had initially conceived low burst as a placebo control, these results are difficult to interpret.
Some of the studies included did not present a power calculation.4,29,46 Considering the IMMPACT recommendation10 of detection of ≥2.0-point pain difference in the VAS/NRS between groups (and assuming a typical SD of 2.5%, 20% attrition, and 90% power), a parallel group design study would need a total of ≥84 patients (42 per arm) and a crossover design (with conservative assumption of no within correlation between before and after VAS/NRS) would need a total of ≥24 patients. Four of the studies included were therefore not adequately powered at 90% level to detect differences in pain intensity between the groups.4,29,39,52
4.1. Strengths and weaknesses
We believe this to be the first systematic review and meta-analysis of placebo-controlled trials of SCS in neuropathic pain. A focused eligibility criteria attempted to minimise the heterogeneity observed. The review process, including study identification, selection, and data extraction, was performed in line with PRISMA30 and CRD guidance.2 The review seeks to provide clarity and direction in reporting and methods in placebo (or sham)-controlled trials in SCS, which may well have relevance to the broader field of neuromodulation trials.
The review cites a limited number of RCTs, none of which judged as having a low risk of bias. All the studies used a crossover design in which each participant served as their own control, which can increase the statistical power of the study. Nonetheless, all the included studies enrolled small sample sizes ranging from 10 to 40 participants, and although all the studies compared some form of SCS with sham, none used the same SCS comparator. The small study size, differing SCS modalities and differing control setups, may explain the heterogeneity observed.
We were unable to include any numerical results for 2 studies recruiting 29 participants within meta-analysis4,29 due to inadequate numerical data provided in the publications. Furthermore, numerical results presented in 4 of the studies1,23,39,46 included in the meta-analysis were only suitable after our statistical adjustment for the within-patient correlation inherent to the crossover design.
Although we were aware of a number of RCTs comparing SCS with placebo in refractory angina,11,26,55 we decided to limit the scope of our review to the trials recruiting participants with neuropathic pain because of the use of different outcome measures as well as the use of a parallel trial design in one of the studies.
In conclusion, the findings of this systematic review show that use of SCS leads to a decrease in pain intensity when compared with a placebo intervention. Nevertheless, exploratory subgroup analyses suggests that the magnitude of treatment effect varies across trials and depends on methodological characteristics including quality of patient blinding and minimisation of carryover effects. No studies have been identified assessing SCS at 10 kHz vs placebo. Further research is needed to evaluate the “true” effect of SCS in decreasing pain intensity of patients with neuropathic pain. The differentiation between placebo and sham concepts introduced in this article merits further investigation in reviews and meta-analysis of trials evaluating surgical or medical procedures.
Conflicts of interest statement
S. Eldabe has received consultancy fees from Medtronic, Inc, Mainstay Medical, Boston Scientific Corp, and Abbott. He has received Department Research funding from the National Institute of Health Research, Medtronic, Inc, and Nevro Corp. R.S. Taylor has received consultancy fees from Medtronic, Inc, and Nevro Corp. R.V. Duarte has received consultancy fees from Medtronic, Inc, and Boston Scientific Corp. R.B. North serves as an unpaid officer of the nonprofit Neuromodulation Foundation, Inc, to which (like his former employers Johns Hopkins University and Sinai Hospital) grants and support have been provided by Abbott, Boston Scientific Corp, Medtronic, Inc, Nevro Corp, Nuvectra, and Stimwave, Inc. He receives royalties from Abbott and consulting fees and royalties from Nuvectra. His wife holds shares in Stimwave, Inc. E. Buchser has received consultancy fees from Medtronic, and his Department has received research funding from Medtronic and the Swiss National Foundation. The remaining authors have no conflicts of interest to declare.
Appendix A. Supplemental digital content
Supplemental digital content associated with this article can be found online at http://links.lww.com/PAIN/A868.
Supplemental video content
Video content associated with this article can be found online at http://links.lww.com/PAIN/A869.
Author contributions: S. Eldabe conceptualised the study. E. McNicol conducted the searches. R.V. Duarte, E. McNicol, and S. Eldabe screened the search results for eligibility. R.V. Duarte, S. Nevitt, and S. Eldabe extracted the data. R.V. Duarte and S. Nevitt conducted the risk of bias assessment. S. Nevitt performed the data analysis. All authors contributed to drafts of the manuscript and approved the final version of the manuscript.
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