Types of studies

We included RCTs or quasi‐randomised trials of TENS treatment. We included single treatment interventions without follow‐up and gave credence to studies that delivered at least two weeks of treatment and had a study duration of at least eight weeks. We included cross‐over and parallel‐group study designs. We required full journal publication, with the exception of online clinical study results summaries of otherwise unpublished clinical studies, and abstracts with sufficient data for analysis. We did not include short abstracts (usually meeting reports). We excluded studies that were non‐randomised, studies of experimental pain, case reports, and clinical observations.

Types of participants

We included studies of adults aged 18 years or above with pain due to fibromyalgia diagnosed using either the Wolfe (Wolfe 1990; Wolfe 2010) or earlier criteria in the case of older studies (e.g. Goldenberg 1987).

Types of interventions

We included studies that evaluated TENS administered using non‐invasive techniques for pain relief. We excluded invasive techniques such as percutaneous electrical nerve stimulation. We included TENS administered using a standard TENS device (Johnson 2014), regardless of the device manufacturer, which delivered biphasic or monophasic pulsed electrical currents that were greater than 1 mA using at least two surface electrodes. We excluded TENS delivered using single probe electrodes (i.e. TENS pens) and studies investigating 'TENS‐like' devices such as neuromuscular electrical stimulation (NMES) devices and interferential current devices. We included studies that administered TENS at intensities that produced perceptible TENS sensations during stimulation. To explore suboptimal stimulation, we conducted a subgroup analysis to compare TENS at intensities described as 'strong' (optimal) versus those described as 'barely perceptible,' 'faint,' or 'mild' (suboptimal). We included TENS administered on an area of the body that was sensate at either the site of pain or over nerve bundles proximal (or near) to the site of pain. We included AL‐TENS delivered at strong intensities to generate muscle twitches. We only included TENS delivered at acupuncture points if the point was lying over nerve bundles proximal (or near) to the site of pain. We included any TENS parameters meeting these criteria; any duration or regularity of TENS treatment; and either self‐applied or therapist‐applied TENS treatment. We included TENS administered as a sole treatment or in combination with usual care. We included studies that evaluated TENS versus:

• placebo TENS (e.g. sham (no current) TENS device);

• no treatment or waiting list control;

• usual care (including exercise);

• other treatment.

Sham credibility is an issue in TENS studies (Deyo 1990). We defined a sham TENS device as a device similar to the one used in the active group but where the current output was modified so that there was: no electrical current, a barely perceptible electrical current, or electrical current that ceased within one minute (Rakel 2010; Sluka 2013). We excluded studies where it was not possible to isolate the effects of TENS from other treatments.

Types of outcome measures

We anticipated that studies would use a variety of outcome measures, with the majority of studies using standard subjective scales (numerical rating scale (NRS) or visual analogue scale (VAS)) for pain intensity or pain relief, or both. We included measures of pain at rest and pain on movement. We were particularly interested in Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) definitions for moderate and substantial benefit in chronic pain studies (Dworkin 2008). These were defined as:

• at least 30% pain relief over baseline (moderate);

• at least 50% pain relief over baseline (substantial);

• much or very much improved on Patient Global Impression of Change scale (PGIC; moderate);

• very much improved on PGIC (substantial).

These outcomes concentrate on dichotomous outcomes where pain responses do not follow a normal (Gaussian) distribution. People with chronic pain desire high levels of pain relief, ideally more than 50%, and ideally with no worse than mild pain (Moore 2013b; O'Brien 2010). We included 'Summary of findings' tables as set out in the author guide (PaPaS 2012) where sufficient data were available. The 'Summary of findings' table included outcomes of at least 30% and at least 50% pain intensity reduction, PGIC, withdrawals due to adverse events, serious adverse events, and death. We used the GRADE approach to assess the quality of evidence related to each of the key outcomes listed in Types of outcome measures (Chapter 12, Higgins 2011), as appropriate. We planned to extract outcome measurement data before, during, and after the intervention, where data were available.

Electronic searches

We searched the following electronic databases using a combination of controlled vocabulary (i.e. MeSH and free‐text terms) to identify published articles:

• Cochrane Central Register of Controlled Trials (CENTRAL; 2016 Issue 12) via CRSO searched on 18 January 2017;

• MEDLINE (via Ovid) from 1950 to 18 January 2017;

• Embase (via Ovid) from 1980 to 18 January 2017;

• CINAHL (via EBSCO) from 1982 to 18 January 2017;

• PsycINFO (via Ovid) from 1806 to 18 January 2017;

• LILACS (via Birme) from 1982 to 18 January 2017;

• PEDRO from 1929 to 18 January 2017;

• Web of Science (SCI, SSCI, CPCI, SCPCI‐SSH) to 18 January 2017;

• AMED (via Ovid) from 1985 to 18 January 2017;

• SPORTDiscus (via EBSCO) from 1975 to 18 January 2017.

There were no language restrictions. We tailored the searches to the individual databases. We adapted the MEDLINE search strategy for the other databases listed. The search strategy combined the subject‐specific search with phase one and two of the Cochrane Sensitive Search Strategy for RCTs (as published in Sections 6.3.2.1, 6.3.3.2, and 6.4.11.1 in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011)). The search strategies can be found in Appendix 2. We identified all relevant studies irrespective of language and translated articles when possible.

Searching other resources

We reviewed the bibliographies of RCTs and review articles, and searched clinical trial databases (e.g. ClinicalTrials.gov (www.clinicaltrials.gov), World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP, apps.who.int/trialsearch/), and metaRegister of Controlled Trials (mRCT, www.isrctn.com/page/mrct) to identify additional published or unpublished data. We did not contact investigators or study sponsors.

Selection of studies

We determined eligibility of studies for inclusion first by title, then by reading the abstract of each record identified by the search. We eliminated records where it was clear from the abstract that they did not satisfy the inclusion criteria, then obtained full copies of the remaining records. Two review authors (MIJ, CAP) made the decisions by reading these records independently and reached agreement by discussion. Disagreements at any stage of the process were/would have been resolved by consensus using a third review author as arbiter (GJ). We did not anonymise the records of studies in any way before assessment. We created a PRISMA flow chart (Higgins 2011; Liberati 2009).

Data extraction and management

Two review authors (LSC, CAP) extracted data of included studies independently using a standard form and checked for agreement before entry into Review Manager 5 (RevMan 2014). Disagreements were resolved by consensus using the arbiter (MIJ). We included information about:

• country of origin;

• study design: cross‐over, parallel‐group;

• study duration;

• study participants: age, gender, fibromyalgia diagnostic criteria used, duration of pain and symptoms;

• sample size: active and comparator groups;

• concomitant treatments: pharmacological and non‐pharmacological;

• TENS intervention(s) used: type, electrical parameters, electrode location, perceptual experience during intervention including intensity of stimulation, dosing regimen;

• comparison group(s) used: placebo, no treatment, usual treatment, other treatment, dosing regimen;

• outcomes: time points used including follow‐up, withdrawals;

• adverse and serious adverse effects;

• other: sponsorship, country of origin, conflict of interest statements.

We used these data to populate the Characteristics of included studies table.

Assessment of risk of bias in included studies

Two review authors (LSC, CAP) independently assessed risk of bias for each trial, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), with disagreements resolved by consensus with a third review author (MIJ) acing as arbiter. We assessed the following for each trial.

• Random sequence generation (selection bias). We assessed the method used to generate the 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). We excluded studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number).

• Allocation concealment (selection bias). The method used to conceal allocation to interventions prior to assignment determines whether the intervention allocation could have been foreseen in advance of, or during, recruitment or changed after assignment. We assessed the methods 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 participants and personnel (performance bias): participants, and care providers administering TENS.

• • Blinding of participants: low risk of bias (participants 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 not blinded to allocated intervention OR participants blinded to allocated intervention but it was likely that blinding may have been broken).

  • Blinding of personnel (care provider(s) administering TENS): low risk of bias (care provider 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 (care provider not blinded to allocated intervention and the two interventions clearly identifiable to the care provider as experimental and control OR care provider blinded to allocated intervention but likely that blinding was broken).

• Blinding of outcome assessment (detection bias): outcome assessors.

  • Blinding of assessor: low risk of bias (outcome assessor (including 'participants' with respect to self‐report outcomes) blinded to participants' 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 (outcome assessor (including 'participants' with respect to self‐report outcomes) unblinded to participants' allocated intervention OR outcome assessor blinded to allocated intervention but likely that blinding was broken)).

• Incomplete outcome data (dropouts). We checked for possible attrition bias by considering if participant dropout was acceptable and described: low risk of bias (less than 20% dropout and appeared to be random with numbers per group provided along with reasons for dropout); unclear risk of bias (less than 20% and unclear if random with numbers per group and reasons for dropout not described); high risk of bias (greater than 20% dropout).

• Incomplete outcome data (protocol violations). We considered if participants were analysed as per original group allocation: low risk of bias (if participants were analysed in the group to which they were originally assigned); unclear risk of bias (where insufficient information was provided to determine if analysis was per protocol or intention‐to‐treat (ITT)); high risk of bias (where per protocol analysis was used, where available data were not analysed or participants' data were included in the group to which they were not originally assigned).

• Selective reporting. We assessed whether studies selectively reported outcomes. We assessed the methods as: low risk of bias (study protocol was available and all prespecified outcomes were reported or study protocol was not available but all expected outcomes were reported); 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 specified outcomes. One or more primary outcomes were reported using measurements or analysis that were not prespecified. One or more of the primary outcomes was not prespecified. One or more outcomes of interest were reported incompletely and could not be entered into a meta‐analysis. Results for a key outcome expected to be reported were excluded).

• Size of study (checking for biases confounded by small size). We assessed this 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 considered other factors such as whether studies were stopped early, there were differences between groups at baseline, the timing of outcome measurement, cointervention comparability, and funding declarations.

Measures of treatment effect

Where available and appropriate we presented quantitative and ITT data. For dichotomous data (responder analyses), we used the Initiative on Methods, Measurement and Pain Assessment in Clinical Trials (IMMPACT) definitions for interpreting the clinical importance in change in outcome measures compared with baseline (Dworkin 2008). We intended to calculate risk ratio (RR) and risk difference (RD) with 95% confidence intervals (CI) for dichotomised outcome measures. We intended to calculate the NNTB as an absolute measure of treatment effect where possible. We intended to present pain outcomes collected as continuous data on identical scales as mean difference (MD) with 95% CI. We intended to present pain outcomes collected as continuous data using different scales as standardised mean difference (SMD) with 95% CI. We intended to interpret reductions in pain over baseline as follows:

• less than 15%: no important change;

• 15% or greater: minimally important change;

• 30% or greater: moderately important change;

• 50% or greater: substantially important change.

For health‐related quality of life data, we intended to consider a clinical difference greater than 10% of the scale employed to be minimally important (Furlan 2009).

The IMMPACT thresholds are based on estimates of the degree of within‐person change from baseline that participants might consider to be clinically important. We expected that the studies in this review would most likely present effect sizes as the mean between‐group change between intervention groups. 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 during or after the intervention. It has been found that in pharmacological studies, pain outcomes for acute pain (Moore 2011b; Moore 2011c), back pain (Moore 2010d), arthritis (Moore 2010c), and fibromyalgia (Straube 2010), tend to have a U‐shaped rather than a bell‐shaped distribution, with some people experiencing a substantial reduction in symptoms, some minimal to no improvement, and few experiencing mean (moderate) improvement. Thus, data expressed as means may be misleading as a small mean between‐group effect size may represent a proportion of participants that actually responded very well to the intervention (Moore 2013c; Moore 2014a). It is unknown whether outcomes are commonly bimodally distributed in studies of TENS. 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 and a small mean between‐group effect might accurately represent very small effects of the intervention for most or all people. We intended to use a threshold of 10 mm on a 0‐ to 100‐mm VAS for minimally important outcome for pain when analysing mean between‐group change, in line with the OMERACT 12 group, which states that the proportion of people achieving one or more thresholds of improvement from baseline pain (e.g. greater than 10%, 20% or greater, 30% or greater, 50% or greater) should be reported in addition to mean change (Busse 2015). We would interpret these findings with caution as it remains possible that estimates that fall close to this point may reflect a treatment that benefits an appreciable number of people.

Unit of analysis issues

We intended to split the control treatment arm between active treatment arms in a single study if the active treatment arms were not combined for analysis. In the unlikely event that the unit of randomisation is not the participant, or where a cross‐over design was used, we intended not to include the data unless a suitable adjustment for the study design had been, or could be, made. We included cross‐over designs but intended only to enter the first period data into the meta‐analysis. If this was not reported, we intended to note this and not include the data. If data were reported appropriately, then we intended to include the data using the generic inverse variance feature.

Dealing with missing data

We intended to use ITT analysis where the ITT population consisted of participants who were randomised, received at least one dose of the assigned study intervention, and provided at least one post‐baseline assessment. We intended to assign missing participants zero improvement wherever possible.

Assessment of heterogeneity

We intended to deal with clinical heterogeneity by combining studies that examined similar conditions. We performed separate analyses where TENS was compared with different control conditions such as placebo or no treatment control. We intended to examine heterogeneity using visual inspection of forest plots, the I² statistic, and L'Abbé Plots (L'Abbé 1987), and the Chi² test, if appropriate. Where significant heterogeneity existed, we intended to explore subgroup analyses. Preplanned comparisons are described in the Subgroup analysis and investigation of heterogeneity section.

Assessment of reporting biases

The aim of this review was to use dichotomous outcomes of known utility and of value to patients (Moore 2010b; Moore 2010c; Moore 2010d; Moore 2013b). It was intended that the review would not depend on what the authors of the original studies chose to report or not, though clearly difficulties would arise in studies failing to report any dichotomous results. We planned to extract and use continuous data, which would probably poorly reflect efficacy and utility and therefore be useful for illustrative purposes only. We intended to assess publication bias using a method designed to detect the amount of unpublished data with a null effect required to make any result clinically irrelevant (usually taken to mean a NNTB of 10 or higher; Moore 2008). We considered the possible influence of small‐study samples by the risk of bias criterion "study size." If at least 10 studies were included in a meta‐analysis and included studies differed in sample size, we planned to visually inspect funnel plots to explore the likelihood of reporting biases. For studies that used continuous outcomes, we intended to use Egger's test to detect small‐study bias (Higgins 2011). We would have interpreted the results of this process cautiously since we were aware that all approaches to the quantification of possible reporting biases have important limitations (Moore 2008).

Data synthesis

We intended to perform pooling of results where adequate data existed using Review Manager 5 (RevMan 2014). We would have undertaken meta‐analyses of outcome data only from suitably homogeneous studies using a random‐effects model. Where possible, we would have grouped extracted data according to outcome and measurement time points. Time points would have included during stimulation or immediately after stimulation at each treatment session, or both; and post‐intervention follow‐up at less than two weeks' post‐intervention (short‐term), two to seven weeks' post‐intervention (mid‐term), and eight weeks or more post‐intervention (long‐term).

Subgroup analysis and investigation of heterogeneity

We anticipated too few data for any meaningful subgroup analysis. However, if sufficient data were available, we planned the following analyses: where substantial heterogeneity was found (I² greater than 40%, P < 0.1), we would conduct a subgroup analysis investigating the possible impact of the TENS technique on analgesic efficacy. If appropriate, we would have conducted the following analyses.

• Optimal intensity described as 'strong' or greater versus suboptimal intensity described as 'barely perceptible,' 'faint,' or 'mild.'

• Low‐frequency (10 Hz or less) TENS versus other frequency (e.g. greater than 10 Hz) TENS.

• Conventional TENS (no visible muscle contraction) versus AL‐TENS (visible phasic muscle contractions).

• Assessment during TENS versus after TENS.

• TENS administered as a sole treatment versus TENS administered in combination with other treatments.

• TENS administered as a single dose versus repetitive dose.

• Opioid‐treated participants versus opioid‐naïve participants.

Sensitivity analysis

We anticipated too few data for any meaningful sensitivity analysis. However, if sufficient data were available, we planned to analyse the effect of excluding studies with high risk of bias and the effect of using a random‐effects versus a fixed‐effect model.