Types of studies

We included randomised controlled trials (RCTs) or quasi‐randomised trials (including cross‐over designs) of TENS applied as treatment for central or peripheral neuropathic pain of any aetiology in adults. We excluded non‐randomised studies, case reports/series, studies of experimental pain, clinical observations and systematic reviews. We assessed studies for inclusion regardless of their publication status. We excluded studies designed to test the immediate effects of a single treatment only with follow‐up less than 24 hours. For non‐English language papers, we sourced translators through Cochrane Pain, Palliative and Supportive Care Review Group as well as personal networks where available.

Types of participants

We included participants aged 18 years or over identified as having pain of neuropathic origin from a wide range of conditions, including, but not limited to:

• cancer‐related neuropathy;

• HIV neuropathy;

• painful diabetic neuropathy (PDN);

• phantom limb pain;

• postherpetic neuralgia (PHN);

• postoperative or traumatic neuropathic pain;

• spinal cord injury;

• poststroke pain;

• trigeminal neuralgia.

We excluded studies that included participants with a mix of neuropathic and non‐neuropathic pain where it was impossible to extract data for the neuropathic pain participants independently. We excluded studies that included participants with complex regional pain syndrome (Type I or II) or fibromyalgia as these studies are considered in separate Cochrane Reviews (Johnson 2016; Smart 2016).

Types of interventions

We included all standard modes of TENS, regardless of the device manufacturer, in which the TENS condition delivered a clearly perceptible sensation. Given that self‐use and portability are key clinical features of TENS, we excluded non‐portable electrical stimulation devices such as interferential therapy (IFT). We included any parameters of treatment that evoked a perceptible sensation, and any frequency or duration of treatment or surface electrode configuration. We excluded studies delivering intensities of TENS that were subperceptual or barely perceptual due to the risk of suboptimal treatment. We excluded studies where current was delivered percutaneously (e.g. electroacupuncture, percutaneous electrical nerve stimulation (PENS), neuroreflexotherapy) and where the effect of TENS could not be separated from the effects of other treatments (i.e. comparison interventions standardised between groups). The comparisons of interest were TENS versus placebo (sham) TENS, TENS versus usual care, TENS versus no treatment and TENS in addition to usual care versus usual care alone.

Types of outcome measures

We included studies with pain intensity as the primary or secondary outcome.

Electronic searches

We searched the following electronic databases using a combination of controlled vocabulary, medical subject headings (MeSH) and free‐text terms to identify published articles.

• Cochrane Central Register of Controlled Trials (CENTRAL; 2016 Issue 8) via CRSO;

• MEDLINE (via Ovid) 1946 to August week 5 2016;

• Embase (via Ovid) 1974 to 2016 week 37;

• CINAHL (EBSCO) 1982 to August 2016;

• PsycINFO (Ovid) 1806 to July week 4 2016;

• LILACS (Birme) 1985 to September 2016;

• PEDro June 2016;

• Web of Science (ISI) SCI, SSCI, CPCI‐S, CPCI‐SS to September 2016;

• AMED (via Ovid) 1985 to August 2016;

• Database of Abstracts of Reviews of Effects June 2016;

• Health Technology Assessments February 2017.

There were no language restrictions. The search strategies used can be found in Appendix 1.

Searching other resources

We searched the metaRegister of controlled trials (mRCT) (www.controlled-trials.com/mrct), ClinicalTrials.gov (www.clinicaltrials.gov), and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) for ongoing trials. In addition, we checked the reference lists of reviews and retrieved articles for additional studies. We also sought relevant expert input in an attempt to elicit further contribution regarding novel studies.

Selection of studies

Two review authors (WG and BMW) independently assessed the titles and abstracts of potential studies identified by the search strategy for their eligibility. If the eligibility of a study was unclear from the title and abstract, we assessed the full paper. We excluded studies that did not match the inclusion criteria (see Criteria for considering studies for this review). We resolved disagreements between review authors regarding a study's inclusion by discussion. A third review author (NEO) was available to assess relevant studies if resolution and agreement could not be reached. This option was not required. We did not anonymise studies prior to assessment.

A PRISMA study flow diagram documents the screening process (Figure 1) (Liberati 2009), as recommended in Part 2, Section 11.2.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011).

Figure 1

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Study flow diagram.

Data extraction and management

Two review authors (WG and BMW) independently extracted data from all included studies using a standardised, piloted data extraction form. We resolved any discrepancies/disagreement by consensus. A third review author (NEO) was available for arbitration if consensus was not achieved. This option was not required. We extracted the following data from each study included in the review:

• country of origin;

• study design;

• study population (including diagnosis, diagnostic criteria used, symptom duration, age, gender);

• concomitant treatments that may affect outcome (medication, procedures, etc.);

• sample size, active and control/comparator groups;

• intervention(s) (including type, parameters (e.g. frequency, intensity, duration, electrode position, setting and professional discipline of the clinician delivering the therapy);

• type of placebo/comparator intervention;

• outcomes (primary and secondary) and time points assessed (only for the comparisons of interest to this review);

• adverse events;

• industry sponsorship;

• author conflict of interest statements.

Assessment of risk of bias in included studies

Two review authors (WG and BMW) independently assessed risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion (Higgins 2011). In cases where consensus was not reached, a third review author (NEO) was available for arbitration. This option was not required.

For each study of parallel design, we assessed the following.

• Random sequence generation (selection bias). We assessed the method used to generate allocation sequence as:

  • low risk of bias (any truly random process, e.g. random number table; computer random number generator);

  • unclear risk of bias (method used to generate sequence not clearly stated);

  • high risk of bias (studies using a non‐random process, e.g. odd or even date of birth; hospital or clinic record number).

• Allocation concealment (checking for possible selection bias). We assessed the method used to conceal allocation to group assignment as:

  • low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

  • unclear risk of bias (method not clearly stated);

  • high risk of bias (studies that did not conceal allocation e.g. open list).

• Blinding of study participants (checking for possible performance and detection bias). We assessed the methods used to blind participants and personnel (care providers) as follows:

  • low risk of bias (participants/personnel blinded to allocated intervention; and unlikely that blinding broken);

  • unclear risk of bias (insufficient information to permit judgement of low/high risk of bias);

  • high risk of bias (participants/personnel not blinded to allocated intervention, two interventions clearly identifiable to personnel as experimental and control OR participants/personnel blinded to allocated intervention but it is likely that blinding may have been broken).

• Blinding of outcome assessor (detection bias). We assessed the methods used to blind outcome assessors as:

  • low risk of bias (outcome assessor (including 'participants' with respect to self‐report outcomes) blinded to participants' allocated interventions and unlikely that blinding broken);

  • unclear risk of bias (insufficient information to permit judgement of low/high risk of bias);

  • high risk of bias (outcome assessor (including 'participants' with respect to self‐report outcomes) unblinded to participants' allocated interventions OR outcome assessor blinded to allocated intervention but likely that blinding may have been broken).

• Incomplete outcome data (attrition bias). We assessed attrition bias by considering if participant dropout rate was appropriately described and acceptable:

  • low risk of bias (less than 20% dropout and appeared to be missing at random. Numbers given per group and reasons for dropout described);

  • unclear risk of bias (if less than 20% but reasons not described and numbers per group not given. Unclear that data were missing at random);

  • high risk of bias (if over 20% even if imputed appropriately).

• Incomplete outcome data (participant exclusion). We assessed whether participants were analysed in the group to which they were allocated as:

  • low risk of bias (if analysed data in group to which originally assigned with appropriately imputed data or as an available‐case analysis);

  • unclear risk of bias (insufficient information provided to determine if analysis was per protocol or intention to treat);

  • high risk of bias (if per‐protocol analysis used. Where available data were not analysed or participant data were included in group they were not originally assigned to).

• Selective reporting (reporting bias). We assessed whether studies were free of the suggestion of reporting bias as:

  • low risk of bias (study protocol available and all prespecified outcomes of interest adequately reported; study protocol not available but all expected outcomes of interest adequately reported; all primary outcomes numerically reported with point estimates and measures of variance for all time points);

  • unclear risk of bias (inadequate information to allow judgement of a study to be classified as 'low risk' or 'high risk');

  • high risk of bias (incomplete reporting of prespecified outcomes; one or more primary outcomes was reported using measurements, analysis methods or subsets of data that were not prespecified; one or more reported primary outcomes were not prespecified; one or more outcomes of interest reported incompletely and cannot be entered into a meta‐analysis; results for a key outcome expected to have been reported excluded).

• Size of study (checking for possible biases confounded by small sample size). We assessed studies as:

  • low risk of bias (200 participants or more per treatment arm);

  • unclear risk of bias (50 to 199 participants per treatment arm);

  • high risk of bias (fewer than 50 participants per treatment arm).

• Other sources of bias. We also assessed other risk factors such as whether trials were stopped early, differences between groups at baseline, differences between groups in timing of outcome assessment, insufficient control of cointerventions and author source of funding declarations.

Measures of treatment effect

We analysed primary outcomes and presented this on a continuous scale as mean difference (MD) with 95% confidence intervals (CI). Where data were available, we planned to present outcomes in a dichotomised format. For dichotomised data (responder analyses), we planned to consider analyses based upon a 30% or greater reduction in pain to represent a moderately important benefit, and a 50% or greater reduction in pain intensity to represent a substantially important benefit as suggested by the IMMPACT guidelines (Dworkin 2008). Where possible, we planned to present risk ratio (RR) and risk difference (RD) with 95% CIs for dichotomised outcome measures. We planned to calculate the number needed to treat for an additional beneficial outcome (NNTB) as an absolute measure of treatment effect. However, these data were not available in the included studies. For HRQoL data, we preplanned a minimally important clinical difference to be greater than 10% of the scale employed (Furlan 2009), however we were unable to report on HRQoL.

The IMMPACT thresholds are based on estimates of the degree of within‐person change from baseline that participants might consider clinically important, whereas the studies in this review typically presented effect sizes as the mean between‐group change. There is little consensus or evidence regarding what the threshold should be for a clinically important difference in pain intensity based on the between‐group difference postintervention. For some pharmacological interventions, the distribution of participant outcomes is bimodally distributed (Moore 2013). That is, some participants experience a substantial reduction in symptoms (Moore 2014), some experience minimal to no improvement and very few experience intermediate (moderate) improvements. In this instance, and if the distribution of participant outcomes reflects the distribution of treatment effects, then the mean effect may be the effect that the fewest participants actually demonstrate (Moore 2013). Therefore, it is possible that a small mean between‐group effect size might reflect that a proportion of participants responded very well to the intervention tested. It is unknown whether outcomes are commonly bimodally distributed in trials of TENS and the advantage of focusing on the between‐group difference is that it is the only direct estimate of the mean specific effect of the intervention. Equally, it remains possible that a very small mean between‐group effect might accurately represent generally very small effects of an intervention for most or all individuals.

The OMERACT 12 group have reported recommendations for minimally important difference for pain outcomes (Busse 2015). They recommend 10 mm on a 0 mm to 100 mm VAS as the threshold for minimal importance for mean between‐group change though they stress this should be interpreted with caution as it remains possible that estimates that fall closely below this point may still reflect a treatment that benefits an appreciable number of people. We use this threshold but interpret it appropriately given the quality of the included studies.

Unit of analysis issues

In cross‐over studies, we planned to use first period data only wherever possible (Higgins 2011). Where this was not reported, we undertook analysis as if the treatment periods were parallel and highlighted the potential bias this may have introduced. All included studies randomised at the level of the individual participant.

Dealing with missing data

Where insufficient data were presented to enter into an otherwise viable meta‐analysis, we contacted the study authors. Two included studies did not present data in a format suitable for data extraction. One study author replied with further data (Buchmuller 2012). We were unable to contact the authors of one further study (Prabhakar 2011).

Assessment of heterogeneity

We planned to combine studies that examined similar conditions. However, given the limited number of studies, we pooled data from studies in different neuropathic pain conditions but have considered whether diagnostic group appears to be a source of important heterogeneity. We evaluated the included studies for clinical homogeneity regarding study population, treatment procedure, control intervention, timing of follow‐up and outcome measurement. We did not combine studies that compared TENS to usual care with studies that compared TENS to sham/placebo in the same analysis. We formally explored heterogeneity using the Chi² test to investigate the statistical significance of any heterogeneity, and the l² statistic to estimate the amount of heterogeneity. Where significant heterogeneity (P < 0.1) was present, we planned to explore subgroup analyses. Preplanned comparisons are described in Subgroup analysis and investigation of heterogeneity.

Assessment of reporting biases

We planned to consider the possible influence of publication/small study biases on review findings. The influence of small study biases were, in part, addressed by the risk of bias criterion 'study size.' We planned to use funnel plots to visually explore the likelihood of reporting biases when there were at least 10 studies in a meta‐analysis and included studies differ in size. For continuous outcomes, we planned to use Egger's test to detect possible small study bias and, for dichotomised outcomes, we planned to test for the possible influence of publication bias on each outcome by estimating the number of participants in studies with zero effect required to change the NNTB to an unacceptably high level (defined as a NNTB of 10), as outlined by Moore 2008. Given the small number of studies in the meta‐analysis and that the remaining studies investigated different TENS comparisons, we did not undertake the above processes.

Data synthesis

We extracted data and classified them according to outcome and duration of follow‐up (during‐use effects; short term: zero to less than two weeks postintervention; mid‐term: two to seven weeks postintervention; and long term: eight or more weeks postintervention). Where adequate data existed, we used a random‐effects model to meta‐analyse outcome data from suitably homogeneous studies using Review Manager 5 (RevMan 2014). For the pooled analysis, pain intensity data was extracted as 0‐10 VAS rating scale except one study which used a 0‐100 VAS scale (Barbarisi 2010). For this study, we converted the results to a 0‐10 scale by dividing the measure by 10. The pooled effect sizes for pain intensity were presented as MDs. We planned to pool data for adverse events across conditions though adequate data were not available to do so. We considered meta‐analysis appropriate for only one comparison (TENS versus sham TENS). This decision reflects the clinical diversity across the included studies, particularly in relation to the control condition. We described the remaining studies as a narrative synthesis. We used the GRADE system to summarise the quality of the body of evidence for key comparisons (Guyatt 2008).

• Limitations of studies: downgraded once if greater than 25% of participants were from studies at high risk of bias across any key 'Risk of bias' criteria.

• Inconsistency: downgraded once if heterogeneity was statistically significant and I² ≥ 40% or when reported treatment effects were in opposition directions.

• Indirectness: downgraded once if greater than 50% of the participants were outside the target group.

• Imprecision: downgraded once if fewer than 400 participants for continuous data and fewer than 300 events for dichotomous data (Guyatt 2011).

• Publication bias: downgrade once where there was direct evidence of publication bias.

We considered single studies both inconsistent and imprecise (unless sample size was greater than 400 participants for continuous data and greater than 300 events for dichotomous data). Two review authors (WG and BW) made these judgements independently and we resolved disagreements by discussion. A third review author (NEO) was available if agreement could not be reached. This option was not required.

The GRADE system uses the following criteria for assigning grade of evidence:

• high: we are very confident that the true effect lies close to that of the estimate of the effect;

• moderate: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of effect, but there is a possibility that it is substantially different;

• low: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect;

• very low: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

We included a 'Summary of findings' table to present the main findings for the comparison 'TENS versus sham TENS' in a transparent and simple tabular format. In particular, we included key information concerning the quality of evidence, the magnitude of effect of the intervention examined and the sum of available data on the outcome(s). Due to clinical heterogeneity and lack of studies, we were unable to compare TENS versus usual care, TENS versus no treatment or TENS in addition to usual care versus usual care alone, therefore we did not present 'Summary of findings' tables for these comparisons.

Subgroup analysis and investigation of heterogeneity

We planned subgroup analysis in the following domains:

• type of neuropathic pain: central neuropathic pain (pain due to identifiable pathology of the central nervous system (e.g. stroke, spinal cord injury) or peripheral neuropathic pain (pain resulting from pathology of the nerve root or peripheral nerves);

• type of neuropathic condition (as feasible from included studies);

• stimulation parameters: intensity (subgroup studies in which intensity was titrated to a strong sensation versus studies in which intensity was not titrated);

• stimulation parameters: frequency (low frequency TENS 10 Hz or less versus high frequency TENS 100 Hz or greater).

We did not undertake these analyses due to insufficient number of included studies and for the pooled analysis clinical homogeneity.

Sensitivity analysis

We undertook a sensitivity analysis on risk of bias (investigating the effect of including/excluding studies at high risk of bias from the analysis) and the choice of meta‐analysis model (investigating the impact of applying a fixed‐effect instead of a random‐effects model) for the comparison TENS versus sham TENS. We described all other studies narratively.