Low-back pain (LBP) is a common musculoskeletal disorder affecting 80% of people at some point in their lives (Deyo 2001) and is the main cause of years lived with disability in the world (Vos 2012). It is among the 10 leading reasons for patient visits to emergency rooms, hospital out-patient departments, and physicians’ offices (Patel 2000). The aetiology of LBP is diverse; many causes have been related to weakness or injury of soft tissues in the lumbar area (O'Sullivan 2005). People with LBP and associated disability usually improve rapidly within weeks, nonetheless pain and disability are often ongoing and recurrences are common (Pengel 2003). It is estimated that 10% to 20% of affected adults develop symptoms of chronic low-back pain (CLBP). Despite the large number of pathological conditions that can give rise to LBP, 85% of LBP cases are without patho-anatomical or radiological abnormalities (Deyo 2001).
The management of LBP encompasses a diverse range of possible interventions including drug therapy, surgery, exercise, patient education, physiotherapy, cognitive-behavioural therapy and various other non-pharmacological therapies. A multidisciplinary approach founded on the biopsychosocial model has been advocated for most patients (Airaksinen 2006; Deyo 2001; Maher 2004; Sierpina 2002). The goals of treatment are to relieve pain, reduce muscle spasm, increase strength and range of motion, promote an early return to activity and improve overall functional status. The risks and benefits of these treatments vary (Delitto 1993; Ottenbacher 1995). Acute and chronic LBP warrant separate consideration as they may respond differently to the same interventions (Sierpina 2002; van Tulder 1999).
Description of the condition
Generally, there is a scarcity of information on the prevalence and incidence of CLBP, partly because of a lack of agreement about its definition. Chronic low-back pain is mostly defined as persistent pain occurring on most days and lasting longer than three months (Maher 2004; Von Korff 1996; Waddell 2004). Others define it as pain that lasts beyond the expected period of healing and acknowledge that chronic pain may not have well-defined underlying pathological causes. Still others have defined CLBP as frequently recurring back pain, probably because it intermittently affects an individual over a long period. Most national insurance and industrial sources of data include only those individuals in whom symptoms result in loss of days at work or other disability. CLBP appears to be a complex disorder with physical, neurological, and psychological underpinnings (Waddell 2004). Since the validity and reliability of some of the existing data are uncertain, caution is needed in an assessment of the information on this type of pain.
Description of the intervention
Transcutaneous electrical nerve stimulation (TENS) is widely used as a therapeutic adjunct in the management of LBP. However, despite the widespread use of TENS machines, the analgesic effectiveness of TENS still remains uncertain (Nnoaham 2008). It is a relatively safe, non-invasive and easy to use modality that can be conveniently self administered by patients at home, making it an attractive treatment option. A TENS unit delivers electrical stimulation to the underlying peripheral nerves via electrodes placed over the intact skin surface, near the source of maximal pain (Barr 1999; Deyo 1990; Sluka 2003).
Several types of TENS applications, differing in frequency, amplitude, pulse width and waveform, are used in clinical practice. The two most common application modes include: 1) high frequency or conventional TENS (frequency greater than 80 Hz, pulse width less than 150 microseconds (μsec), low intensity sufficient to produce a comfortable tingling sensation); and 2) low frequency or so-called acupuncture-like TENS (frequency less than 10 Hz, pulse width greater than 150 μsec, high intensity sufficient to elicit muscle twitching) (Belanger 2002). Acupuncture-like TENS is associated with a slower onset and longer duration of analgesia compared to conventional TENS (Belanger 2002). However, whether there is a significant difference in clinical effectiveness between high frequency and low frequency modes is unclear and not well defined (Belanger 2002; Johnson 1991a). Indeed, patient preference for, and response to, different stimulation settings may be highly individualized (Johnson 1991a; Johnson 1991b; Tulgar 1991). Three other standard modes of TENS include: 1) brief-intense TENS (frequency greater than 80 Hz, pulse width greater than 150 μsec, brief duration of stimulation, very high intensity sufficient to activate nociceptive fibres in addition to motor fibres and primary sensory afferents); 2) burst TENS (bursts of high frequency pulses delivered at low frequency (less than 10 Hz) and at a high enough intensity to activate both motor fibres and primary sensory afferents); and 3) modulation TENS (one or more parameters are randomly modulated during therapy).
Adverse reactions reported with TENS include skin irritation at the site of electrode placement (Deyo 1990; Rushton 2002). Treatment with TENS is contraindicated in patients with cardiac pacemakers due to the potential for interfering with pacemaker activity (Belanger 2002; Rushton 2002).
How the intervention might work
The development and application of TENS was based on the Gate Control Theory, conceptualized by Melzack and Wall (Melzack 1982). According to this theory, the stimulation of large diameter (A-beta), primary sensory afferents activates inhibitory interneurons in the substantia gelatinosa of the spinal cord dorsal horn, and thereby blocks the transmission of nociceptive signals from small diameter A-delta and C fibres (Melzack 1965; Melzack 1982). Supraspinal mechanisms involving the endogenous opioid system have also been described (Han 1991; Hughes 1984; Kalra 2001; Salar 1981). Overall, TENS is postulated to "close the gate" and dampen the perception of pain (Melzack 1982).
Why it is important to do this review
A Cochrane review on this topic was first published in 2001 (Milne 2001) and then updated in 2005 and 2010 (Khadilkar 2005; Khadilkar 2010), yet the clinical benefit of TENS for chronic LBP remains uncertain. The aim of this update is to re-evaluate its efficacy in managing CLBP in light of recent studies and methodological advances. Moreover, earlier versions of this review excluded studies that compared TENS to an active comparator (e.g., acupuncture or massage). Now we will include these comparisons.
To determine the effectiveness of TENS in the management of chronic LBP. We will compare TENS (either alone or in combination with another treatment) to placebo, no treatment, or other interventions for chronic LBP and evaluate outcomes in terms of pain intensity, back-specific functional status, general health, work disability, and patient satisfaction. A secondary objective is to determine the most effective dosage and intensity of TENS for chronic LBP.
Criteria for considering studies for this review
Types of studies
Studies will be included if they are full journal publications of randomized controlled trials (RCTs) in which the effects of TENS has been studied in patients with chronic LBP. Chronic LBP will be defined as pain of at least three months duration. We will exclude studies if the author(s) did not explicitly state that the interventions had been randomly allocated; the method of randomisation was inadequate (i.e. sequential, 'quasi', pseudo, or alternate allocation); or if studies were published as abstracts, letters or review articles.
Types of participants
Patients with non-specific chronic LBP, aged 18 years and above will be considered for this review. Non-specific LBP indicates that no specific cause is detectable, such as malignancy, infection, neoplasm, osteoporosis, fracture, inflammatory disorder or neurological syndrome (Waddell 2004). LBP is defined as any pain localized to the area between the costal margin or the 12
Types of interventions
We will consider all standard modes of TENS in this review. Articles evaluating the effects of electrical stimulation percutaneously using acupuncture needles will be excluded. The use of co-interventions assigned equally to both the experimental and control groups will be accepted. We will exclude RCTs in which TENS had been one part of a treatment package and for which it is not possible to determine the effectiveness of TENS alone.
Types of outcome measures
The primary outcome measures will be taken from a core set of instruments recommended for LBP research. These include: 1) pain (typically measured using a visual analogue scale (VAS)); 2) back-specific functional status (e.g. Roland Morris Disability Scale or Oswestry Disability Index); 3) generic health status (e.g. SF36); 4) work disability (e.g. loss of work, sick days); and 5) patient satisfaction (Bombardier 2000; Deyo 1998; Schaufele 2003). Treatment side-effects will also be used as primary outcome measure. We will report the timing of measuring outcomes separately as short-term (closest to four weeks), intermediate-term (closest to six months), and long-term (closest to one year).
Physical examination measures such as range of motion, finger-to-floor distance, degrees of straight leg raising, muscle strength, medication use and use of medical services will be considered as secondary outcomes.
Search methods for identification of studies
We will identify relevant RCTs by searching the following databases from their beginning to the time of the search: the Cochrane Back Group Specialized Registry, the Cochrane Central Register of Controlled Trials (CENTRAL)in The Cochrane Library (current issue), MEDLINE, EMBASE, the Physiotherapy Evidence Database (PEDro), and CINAHL.
We will use the search strategy recommended by the Cochrane Back Review Group (Furlan 2009). See Appendix 1 for the MEDLINE search strategy, which will be adapted for the other databases. We will consider RCTs in all languages for inclusion.
Searching other resources
We will screen conference proceedings as well as reference lists from guidelines, literature reviews and retrieved articles for further identification of relevant work. Content experts will then be contacted for additional studies.
Data collection and analysis
Selection of studies
Two authors (DO & NH) will screen the titles and abstracts of all studies retrieved to identify those meeting the inclusion criteria. The authors will select the studies independently and discuss the results to make the final selection. They will make the final decision after reading the full text of all potentially eligible articles. In case of disagreement, they will consult with a third author (LC). We will retrieve publications in all languages and seek appropriate translation if necessary.
Data extraction and management
Two reviewers (DO & NH) will independently extract the data from each trial using a standard form. These reviewers will also perform pilot testing of the standardized form on a sample of three articles. The authors will examine inter-rater reliability throughout the pilot data collection process, will note the frequency of disagreements for specific data, and modifications will be made on the coding instructions accordingly.
The following data will be extracted from each study: characteristics of the study population (e.g. number of participants, age, gender, severity of LBP), study characteristics (e.g. country, recruitment modality, study funding, risk of bias), description of the experimental and control interventions, co-interventions, duration of follow-up, outcomes assessed, and results. We will discuss any disagreement and consult a third review author if necessary.
Assessment of risk of bias in included studies
Two review authors (DO & NH) will independently assess the risks of bias of all included studies using the updated Cochrane Back Review Group criteria shown in Appendix 2. We will attempt to obtain additional information from authors of the studies regarding any items that remain unclear. Studies meeting at least six of the 12 criteria and having no serious flaws will be considered to have a "low" risk of bias (Furlan 2009).
Measures of treatment effect
We will analyze continuous outcomes by calculating the mean difference (MD) or the standardized mean difference (SMD) with 95% confidence intervals (CI). If dichotomous outcomes are presented, the risk ratio will be calculated as the effect measure. In cases where more than two interventions are evaluated in the same study, we will calculate a single "pair-wise" comparison. This is necessary to correct for error introduced by "double-counting" of subjects in the meta-analyses. For each treatment comparison, we will calculate an effect size and a 95% CI and display them as forest plots. We will conduct all analyses in Review Manager 5.
Dealing with missing data
Where the required data for an included study are missing, we will attempt to contact the corresponding author of the study. Where data are reported in a graph and not in a table or the text, we will estimate the means and standard deviations from them. When standard deviations are not reported, we will estimate these from the confidence intervals or other measures of variance if possible. If the standard deviation for follow-up measurements is missing, we will use the standard deviation for that measure at baseline for subsequent follow-up measurements. Finally, if no measure of variation is reported anywhere in the text, we will estimate the standard deviation based upon other studies with a similar population and risk of bias.
Assessment of heterogeneity
We will assess clinical heterogeneity in the included RCTs by considering whether the studies are similar for the setting, participants, interventions and outcomes. Additionally, methodological heterogeneity will be assessed by examining the variability in study design and risk of bias. We will check for statistical heterogeneity using theChi² test with the level of significance at 0.05. Values of I² that are greater than 75% show a very high level of heterogeneity, in which case, we will not pool studies. If values of I² are 40% to 74%, we will pool studies using a random-effects model; in case of low or no heterogeneity, we will analyze studies using a fixed-effect model.
Assessment of reporting biases
We will create and use funnel plots to evaluate the presence of reporting biases.
The outcome measures from the individual trials will be combined through meta-analysis where possible (clinical comparability of population, intervention and outcomes between trials) using a fixed-effect model unless there is significant statistical heterogeneity, in which case a random-effects model will be used. If a meta-analysis is not possible, the results from clinically comparable trials will be described qualitatively in the text. The clinical relevance of the results will be evaluated using a five-point criteria list (Appendix 3) and considered in the summary of the findings. The criteria list includes items on the reporting of patients, interventions and treatment settings, as well as assessing likely treatment benefits in relation to potential harms. We will consider an improvement of 30% on low-back pain or function as a clinically important change (Ostelo 2005).
Regardless of whether there are sufficient data available to use quantitative analyses to summarize the data, we will assess the overall quality of the evidence for each outcome. To accomplish this, we will use the GRADE approach (Guyatt 2008). Factors that may decrease the quality of the evidence are: study design and risk of bias, inconsistency of results, indirectness (not generalisable), imprecision (sparse data) and other factors (e.g. reporting bias). Single studies are considered to provide "low" or "very low" quality evidence, depending upon whether they are associated with a low or high risk of bias, respectively. The quality of the evidence for a specific outcome will be reduced by a level, according to the performance of the studies against these five factors.
High quality evidence: there are consistent findings among at least 75% of RCTs with low risk of bias, consistent, direct and precise data and no known or suspected publication biases. Further research is unlikely to change either the estimate or our confidence in the results.
Moderate quality evidence: one of the domains is not met. Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate.
Low quality evidence: two of the domains are not met. Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate.
Very low quality evidence: three of the domains are not met. We are very uncertain about the results.
No evidence: no RCTs were identified that addressed this outcome
We will complete Summary of Findings tables to improve the readability of the review. The following outcomes will be included in these tables: pain, back-specific functional status, work disability, patient satisfaction, medication use, and adverse effects.
Subgroup analysis and investigation of heterogeneity
If a sufficient number of studies exist, we will perform subgroup analyses to see the effect of study methods, risk of bias and clinical differences.
We will perform sensitivity analyses to check whether including or excluding high risk of bias studies, according to predefined criteria, affects the effectiveness between comparison groups.
The authors wish to thank Teresa Marin for her important feedback and Lucie Brosseau, George Wells, Amole Khadilkar, Sarah Milne, Vivian (Robinson) Welch, Michael Saginur, Beverley Shea, and Peter Tugwell for their contributions to earlier versions of this work.
Appendix 1. MEDLINE search strategy
1. randomized controlled trial [pt]
2. controlled clinical trial [pt]
3. randomized [tiab]
4. placebo [tiab]
5. drug therapy [sh]
6. randomly [tiab]
7. trial [tiab]
8. groups [tiab]
9. #1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8
10. animals [mh] not (humans [mh] and animals [mh])
11. #9 not #10
12. Back Pain[mh]
13. back pain [tiab]
14. Low-back pain[mh]
15. low back pain [tiab]
22. lumbar pain[tiab]
25. OR #12 - #24
26 Transcutaneous Electric Nerve Stimulation[mh]
29 transcutaneous nerve stimulation[tiab]
31 transcutaneous electrical neurostimulation[tiab]
34 transdermal electrical stimulation[tiab]
35 peripheral conditioning stimulation[tiab]
36 percutaneous neural stimulation[tiab]
37 microamperage electrical stimulation[tiab]
38 cranial electrotherapy stimulation[tiab]
39 transcutaneous cranial electrical stimulation[tiab]
40 transabdominal neurostimulation[tiab]
41 Electric Stimulation Therapy[mh]
42 Electric Stimulation[mh]
45 OR #26 - #44
46 #11 AND #25 AND #45
Appendix 2. Criteria for judging risk of bias
Random sequence generation (selection bias)
Selection bias (biased allocation to interventions) due to inadequate generation of a randomized sequence
There is a low risk of selection bias if the investigators describe a random component in the sequence generation process such as: referring to a random number table, using a computer random number generator, coin tossing, shuffling cards or envelopes, throwing dice, drawing of lots, minimization (minimization may be implemented without a random element, and this is considered to be equivalent to being random).
There is a high risk of selection bias if the investigators describe a non-random component in the sequence generation process, such as: sequence generated by odd or even date of birth, date (or day) of admission, hospital or clinic record number; or allocation by judgment of the clinician, preference of the participant, results of a laboratory test or a series of tests, or availability of the intervention.
Allocation concealment (selection bias)
Selection bias (biased allocation to interventions) due to inadequate concealment of allocations prior to assignment
There is a low risk of selection bias if the participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web-based and pharmacy-controlled randomization); sequentially numbered drug containers of identical appearance; or sequentially numbered, opaque, sealed envelopes.
There is a high risk of bias if participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes were used without appropriate safeguards (e.g. if envelopes were unsealed or non-opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; or other explicitly unconcealed procedures.
Blinding of participants
Performance bias due to knowledge of the allocated interventions by participants during the study
There is a low risk of performance bias if blinding of participants was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding.
Blinding of personnel/care providers (performance bias)
Performance bias due to knowledge of the allocated interventions by personnel/care providers during the study
There is a low risk of performance bias if blinding of personnel was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding.
Blinding of outcome assessor (detection bias)
Detection bias due to knowledge of the allocated interventions by outcome assessors
There is low risk of detection bias if the blinding of the outcome assessment was ensured and it was unlikely that the blinding could have been broken; or if there was no blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding, or:
- for patient-reported outcomes in which the patient was the outcome assessor (e.g. pain, disability): there is a low risk of bias for outcome assessors if there is a low risk of bias for participant blinding (Boutron 2005);
- for outcome criteria that are clinical or therapeutic events that will be determined by the interaction between patients and care providers (e.g. co-interventions, length of hospitalization, treatment failure), in which the care provider is the outcome assessor: there is a low risk of bias for outcome assessors if there is a low risk of bias for care providers (Boutron 2005);
- for outcome criteria that are assessed from data from medical forms: there is a low risk of bias if the treatment or adverse effects of the treatment could not be noticed in the extracted data (Boutron 2005).
Incomplete outcome data (attrition bias)
Attrition bias due to amount, nature or handling of incomplete outcome data
There is a low risk of attrition bias if there were no missing outcome data; reasons for missing outcome data were unlikely to be related to the true outcome (for survival data, censoring unlikely to be introducing bias); missing outcome data were balanced in numbers, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with the observed event risk was not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, the plausible effect size (difference in means or standardized difference in means) among missing outcomes was not enough to have a clinically relevant impact on observed effect size, or missing data were imputed using appropriate methods (if drop-outs are very large, imputation using even 'acceptable' methods may still suggest a high risk of bias) (van Tulder 2003). The percentage of withdrawals and drop-outs should not exceed 20% for short-term follow-up and 30% for long-term follow-up and should not lead to substantial bias (these percentages are commonly used but arbitrary, not supported by literature) (van Tulder 2003).
Selective reporting (reporting bias)
Reporting bias due to selective outcome reporting
There is low risk of reporting bias if the study protocol is available and all of the study's pre-specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre-specified way, or if the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre-specified (convincing text of this nature may be uncommon).
There is a high risk of reporting bias if not all of the study's pre-specified primary outcomes have been reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not pre-specified; one or more reported primary outcomes were not pre-specified (unless clear justification for their reporting is provided, such as an unexpected adverse effect); one or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta-analysis; the study report fails to include results for a key outcome that would be expected to have been reported for such a study.
Group similarity at baseline (selection bias)
Bias due to dissimilarity at baseline for the most important prognostic indicators.
There is low risk of bias if groups are similar at baseline for demographic factors, value of main outcome measure(s), and important prognostic factors (examples in the field of back and neck pain are duration and severity of complaints, vocational status, percentage of patients with neurological symptoms) (van Tulder 2003).
Co-interventions (performance bias)
Bias because co-interventions were different across groups
There is low risk of bias if there were no co-interventions or they were similar between the index and control groups (van Tulder 2003).
Compliance (performance bias)
Bias due to inappropriate compliance with interventions across groups
There is low risk of bias if compliance with the interventions was acceptable, based on the reported intensity/dosage, duration, number and frequency for both the index and control intervention(s). For single-session interventions (e.g. surgery), this item is irrelevant (van Tulder 2003).
There is low risk of bias if all randomized patients were reported/analysed in the group to which they were allocated by randomization.
Timing of outcome assessments (detection bias)
Bias because important outcomes were not measured at the same time across groups
There is low risk of bias if all important outcome assessments for all intervention groups were measured at the same time (van Tulder 2003).
Bias due to problems not covered elsewhere in the table
There is a low risk of bias if the study appears to be free of other sources of bias not addressed elsewhere (e.g. study funding).
Appendix 3. Questions for clinical relevance
- Are the patients described in detail so that you can decide whether they are comparable to those that you see in your practice?
- Are the interventions and treatment settings described well enough so that you can provide the same for your patients?
- Were all clinically relevant outcomes measured and reported?
- Is the size of the effect clinically important?
- Are the likely treatment benefits worth the potential harms?
Contributions of authors
DO and NH designed the protocol. DO drafted the protocol with help from the other authors. All authors read and approved the final version.
Declarations of interest
In trials considered for inclusion, where one of the authors is also an author of this review, that author was not involved in decisions regarding the inclusion, risk of bias assessment, or conclusions of the trial. The authors declare that they have no other conflicts of interest.
Sources of support
- College of Medicine, University of Lagos, Nigeria.
- No sources of support supplied