Anticonvulsants for chronic low-back pain

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the effectiveness and safety of anticonvulsants for the management of chronic low-back pain, with or without radiculopathy.


Description of the condition

Chronic low back pain is defined as pain persisting for 12 or more weeks involving the area between the bottom of the rib cage and the gluteal folds (Airaksinen 2006). Chronic low-back pain has been shown to affect up to 23% of the general population (Andersson 1993). Furthermore, recent studies found that at least in some parts of the world the prevalence of chronic low-back pain may be increasing (Freburger 2009; Meucci 2013). The total costs associated with the management of low-back pain in the USA have been estimated to exceed USD 100 billion per year (Katz 2006).

Description of the intervention

A variety of treatments have been advocated for the management of chronic low-back pain. These treatments include drugs, education, rehabilitation, exercise, psychotherapy programs and invasive procedures such as epidural corticosteroids. Current guidelines on the management of chronic low-back pain stress that, due to the multidimensional nature of pain, no single intervention is likely to be effective and multiple approaches are required for optimal patient management (Airaksinen 2006; Pillastrini 2012).

Several mechanisms have been hypothesized to contribute to the chronification of low-back pain (that is, the process by which acute pain becomes chronic pain). These mechanisms include psychological factors, changes of the patterns of activation of muscle groups, maladaptive neuroplasticity (or negative plasticity) and central sensitization to pain, as well as the remodelling of vertebral and paravertebral connective tissues (Langevin 2007). For example, chronic low-back pain patients have been shown to have decreased pre-frontal and thalamic gray matter density, possibly because of neuronal loss due to toxic effects of prolonged neuro-excitation. Furthermore, findings from functional neuro-imaging studies have demonstrated that several chronic pain conditions have a large central nervous system component (Mackey 2004).

Anticonvulsant drugs are a heterogeneous group of medications that exert their anti-seizure effect through a variety of mechanisms such as blocking ion channels (e.g. sodium and calcium ion channels) and receptors of neurotransmitters (e.g. gamma-aminobutyric acid and glutamate receptors). Even though the exact mechanism of the analgesic action of these drugs remains unclear, research suggests that it may be through enhancement of inhibitory pain pathways and limitation of neuronal hyperexcitation (Maizels 2005).

How the intervention might work

Traditionally, chronic pain syndromes have been categorized as either neuropathic or nociceptive. However, it has been argued that neuropathic pain may not be an 'all or none' phenomenon but rather one that can be present in different degrees even in pain syndromes previously classified as purely nociceptive (Fishbain 2014). A recent systematic review concluded that a neuropathic component is often present in both chronic low-back pain and soft tissue syndromes (e.g. myofascial pain and fibromyalgia) even in the absence of radiculopathy (disease of the spinal nerve roots) (Fishbain 2014). The neuropathic component could stem from central sensitization, long-term potentiation and peripheral nerve lesions (Xu 2012; Fishbain 2014). Anticonvulsants are considered first-line agents for the management of neuropathic pain syndromes (Dworkin 2007) and could be useful for treating the previously unknown neuropathic component of chronic low-back pain and soft tissue syndromes. Anticonvulsants may act on the modulation of neurotransmission of nociception by blockade of sodium and calcium channels and suppression of glutamate release or direct action on N-methyl-D-aspartate/α-amino-3-hydroxy-5-methyl-4-isoxazolepropionic acid (NMDA/AMPA) receptors (Woolf 1998; Dogrul 2003; Markman 2006).

Why it is important to do this review

The recently published World Health Organization (WHO) report on the Global Burden of Disease identified low-back pain as the leading cause of disability worldwide (Vos 2012). This report indicated that low-back pain was responsible for 10.7% of the total years of life lost due to disability, in the world, from 1990 to 2010 (Vos 2012). Even though anticonvulsant medications have been used commonly for the management of chronic low-back pain, with or without radiculopathy, we could not find a single systematic review dedicated specifically to the question of the effectiveness and safety of that practice. Even though the 2007 systematic review by the American Pain Society and the American College of Physicians on the treatment of acute and chronic low-back pain did examine the use of anticonvulsant drugs for low-back pain, that review had a number of limitations (Chou 2007). First, because it was a very broad review of medical interventions, anticonvulsant drugs received a very brief analysis with no attempt to provide a quantitative synthesis of the limited evidence found. Second, some important reference sources such as EMBASE and Web of Science were not searched and only English-language studies were examined. Finally, the review is already six years old and new trials have been published since that time. Some of these limitations also apply to the even older European Guidelines for the Management of Chronic Non-specific Low-Back Pain (Airaksinen 2006). We believe that an up-to-date systematic review of the effectiveness and safety of the use of anticonvulsants for the treatment of chronic low-back pain shall be useful to inform clinicians, public health stakeholders and researchers on the management of this common and debilitating condition.


To assess the effectiveness and safety of anticonvulsants for the management of chronic low-back pain, with or without radiculopathy.


Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs).

Types of participants

The target population will be adults (≥ 18 years old) diagnosed with non-specific or specific (e.g. lumbar/sacral radiculopathies and pathological causes of back pain) chronic low-back pain. Low-back pain is defined as pain in the lumbar region, with or without pain in the sacral region, gluteal regions and radiation to the lower extremities.

We will include trials of patients with multiple or generalised pain conditions if > 50% of participants had chronic low-back pain or study authors reported results separately.

Types of interventions

We will include clinical trials of orally administered anticonvulsants, such as gabapentin, pregabalin, carbamazepine, phenytoin, topiramate, without restrictions regarding type of anticonvulsant, dose or frequency. Anticonvulsants will be compared to placebo, no intervention, or other active treatments including both non-pharmacologic or pharmacologic treatments. We will also consider studies in which combinations of anticonvulsants or anticonvulsants plus another drug or non-pharmacologic strategy was the intervention (e.g. opioids, anti-inflammatories, antidepressants).

Types of outcome measures

We will categorise duration of follow-up as less than 4 weeks, 1 to 3 months, 4 to 8 months and greater than 9 months for all the outcomes.

Primary outcomes
  • Pain, measured as the percentage of patients with pain relief defined as at least 50% of improvement using a numerical scale, or as mean improvement on a continuous scale measured by any validated or non-validated measurement scale (e.g. Visual Analogue Scale (VAS), Verbal Rating and Numeric Rating Scales, McGill Pain Questionnaire) (Dworkin 2005).

Secondary outcomes
  • Global measure of improvement (e.g. overall improvement, proportion of patients recovered, subjective improvement of symptoms).

  • Back-specific disability (expressed on a back-specific index, such as the Roland Disability Questionnaire or the Oswestry Disability Index).

  • Neurological deficits (motor and sensory).

  • Generic health status or well-being (SF-36 Health Survey), return to work (measured as the number of days of sick leave or the proportion of patients returned to work).

  • Patient satisfaction measured by self report or an assessor.

  • Side effects (e.g. nausea, vomiting, drowsiness, somnolence, weight gain).

  • The Beck Depression Inventory.

Search methods for identification of studies

Electronic searches

We will use the methods recommended by Furlan 2009 and the Cochrane Handbook, Chapter 6 "Searching for Studies" (Higgins 2011) to guide the identification of relevant trials.

Trials will be obtained from the following sources: the Cochrane Central Register of Controlled Trials (CENTRAL, latest version), which includes the Back Review Group's Trials Register, MEDLINE (OVID SP, 1966 to present), MEDLINE In-Process & Other Non-Indexed Citations (latest version), EMBASE (OVID SP, 1980 to present), Web of Science (1864 to present), and LILACS (1982 to present). and the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP will be searched for on-going registered trials. There will be no language restrictions.

The search strategies will be developed by the Trials Search Coordinator of the Cochrane Back Review Group. Strategies will consist of controlled vocabulary terms and keywords to describe the condition, the intervention, and a filter to identify randomized controlled trials. The boolean operator "OR" will be used to combine terms within each concept and the operator "AND" will be used to combine the concepts together. See Appendix 1 for a draft Medline strategy. The strategy will be replicated as closely as possible across the other databases.

Searching other resources

We will check the reference lists of the identified studies for additional citations. We will contact pharmaceutical companies, study authors and experts about unpublished data. We will also make a request to the U.S. Food and Drug Administration for data from unpublished trials.

Data collection and analysis

Selection of studies

Two authors (FBF and GAMB) will independently screen the trials identified by the literature search. We will resolve disagreements regarding eligibility by consulting with an additional author (RED).

Data extraction and management

Two authors (FBF and GAMB) will independently extract data. Any discrepancies in the extracted data will be resolved by discussion. We will use a standard data extraction form to extract the following information: characteristics of the study (design, method of randomisation), participants, interventions and outcomes (types of outcome measures, adverse events). We will then check for accuracy before entering the data into the Cochrane Collaboration statistical software, Review Manager 5.2 (Review Manager 2011).

Clinical relevance assessment

We will assess the clinical relevance of each study based on the criteria recommended by the Cochrane Back Review Group (van Tulder 2003). These criteria consist of five questions that relate to key factors, such as patients, interventions and outcomes. Each factor is scored as “yes”, “no”, or “unsure” to indicate whether the study provides sufficient information to determine the relevance of the study’s results to the patient population in question.

Assessment of risk of bias in included studies

For the assessment of study quality, we will follow the guidance of the Cochrane Collaboration (Higgins 2011) and the Cochrane Back Review Group (Furlan 2009). Criteria for assessing risk of bias are listed in Appendix 2.

Initially, we will copy information relevant for making a judgement on a criteria from the original publication into an assessment table. If additional information is available from study authors, we will also enter this in the table along with an indication that this is unpublished information.

Two review authors (FBF and GAMB) will independently make a judgement as to whether the risk of bias for each criteria is considered to be 'low', 'unclear', or 'high'. Consensus will be reached with a third author (RED). We will resolve disagreements by discussion. We will consider trials which are classified as low risk of bias in sequence generation, allocation concealment, blinding, incomplete data and selective outcome reporting as overall low bias-risk trials.

Measures of treatment effect

When possible, the analyses of treatment effects will be conducted separately for chronic low-back pain, with and without radiculopathy.

(a) Binary outcomes
For dichotomous data, we will use relative risk (RR) and absolute risk reduction (ARR) as the effect measures with 95% confidence intervals (CI).

(b) Continuous outcomes
For continuous data, we will present the results as mean differences (MD) with 95% confidence intervals (CI). When pooling data across studies we will estimate the mean difference if the outcomes are measured in the same way between trials.

Unit of analysis issues

The unit of analysis will be each patient recruited into the trials.

Dealing with missing data

We will analyse studies on an intention-to-treat (ITT) basis, i.e. we will analyse patients according to the intervention they were allocated, whether they received the intervention or not. We will impute a poor outcome for a drop-out rate of > 5%. We will also perform a sensitivity analysis imputing a favourable outcome for patients who dropped out from the studies.

For each trial we will report whether or not the investigators stated if the analysis was performed according to the ITT principle.

Assessment of heterogeneity

We will look for clinical heterogeneity by examining the study details to determine the appropriateness of combining studies quantitatively, and test for statistical heterogeneity between trial results using the Chi2 test and the I2 statistic when they are combined (see Chapter 9 of The Cochrane Handbook of Systematic Reviews of Interventions) (Higgins 2011). We will classify heterogeneity using the following I2 values:
• 0 to 40%, might not be important;
• 30% to 60%, may represent moderate heterogeneity;
• 50% to 90%, may represent substantial heterogeneity;
• 75% to 100%, considerable heterogeneity.

If substantial heterogeneity exists we will explore reasons for this through sensitivity and subgroup analyses on factors related to risk of bias, study design, patient and intervention characteristics.

Assessment of reporting biases

Apart from assessing the risk of selective outcome reporting, considered under assessment of risk of bias in included studies, we will assess the likelihood of potential publication bias using funnel plots, provided that there are at least 10 trials (Sterne 2011). Although small sample effects in a funnel plot can be a marker of publication bias, other causes will be considered including: selection biases, poor methodological quality, heterogeneity, artefactual and chance. Furthermore, we will contact drug companies and authors also as a strategy to assess reporting bias.

Data synthesis

Dichotomous outcomes will be analysed by calculating the relative risk (RR) and absolute risk reduction (ARR). Continuous outcomes will be analysed by calculating the mean difference (MD) when the same instrument is used to measure outcomes, or the standardised mean difference (SMD) when different instruments are used to measure the outcomes. The degree of uncertainty will be expressed with 95% confidence intervals (95% CI). The outcome measures from the individual trials will be combined through meta-analysis when appropriate (based on the clinical comparability of population, intervention and outcomes between trials) using a random-effects model. A P value of less than 0.05, using the Chi2 test, indicates significant statistical heterogeneity.

If a meta-analysis is not possible or appropriate, the results from clinically comparable trials will be described qualitatively in the text.

Summary of findings (SoF) tables

We will use the principles of the GRADE system (Guyatt 2008), as recommended in The Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and adapted in the updated Cochrane Back Review Group method guidelines (Furlan 2009) to assess the quality of the body of evidence associated with specific outcomes (pain, global measure of improvement, back-specific disability, neurological deficits and side effects) in our review and construct a SoF table using the GRADE software. The main comparison will be anticonvulsants compared to other active treatments including both non-pharmacologic or pharmacologic treatments.

Factors that may decrease the quality of the evidence include the following:

  • Risk of bias: Is a judgement made on the basis of the chance that bias in included studies have influenced the estimate of effect?

  • Imprecision: Is a judgement made on the basis of the chance that the observed estimate of effect could change completely?

  • Indirectness: Is a judgement made on the basis of the differences in characteristics of how the study was conducted and how the results are actually going to be applied?

  • Inconsistency: Is a judgement made on the basis of the variability of results across the included studies?

  • Publication bias: Is a judgement made on the basis of the question whether all the research evidence has been taken to account?

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. There are five levels of evidence:

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.

Subgroup analysis and investigation of heterogeneity

In the case of excessive statistical heterogeneity (I2 > 50%), we will use subgroup analysis to evaluate for potential sources of heterogeneity. Subgroup analyses are secondary analyses in which the participants are divided into groups according to shared characteristics and outcome analyses are conducted to determine if any significant treatment effect occurs according to that characteristic. If data permit, we will carry out the following subgroup analyses:

1. different type of anticonvulsants (such as calcium (e.g. pregabalin) versus sodium (e.g. carbamazepine) channel blockers;

2. different type of drug as the associated intervention (e.g. opioids versus antidepressants);
3. most prominent component of pain (i.e. neuropathic versus nociceptive);
4. age (e.g. 18 to 60 years old versus > 60 years old).

Sensitivity analysis

If there are an adequate number of studies, we will perform the following sensitivity analyses:

1. restricting the analysis to studies of high quality and low risk of bias;

2. cross-over design versus non-cross-over;

3. for those studies assessing multiple and generalised pain conditions (e.g. fybromyalgia), we also intend to perform a sensitivity analysis of the primary outcome of the treatment of chronic low-back pain with anticonvulsants according to the presence or absence of multiple or generalised pain conditions.


We would like to thank Teresa Marin and Allison Kelly for their help and editorial advice during the preparation of this protocol for the systematic review.


Appendix 1. Detailed search strategies


1 randomized controlled

2 controlled clinical

3 randomi#ed.ti,ab.

4 placebo.ti,ab.

5 randomly.ti,ab.

6 controlled.ti,ab.

7 prospective.ti,ab.

8 trial.ti,ab.

9 groups.ti,ab.

10 or/1-9

11 (animals not (humans and animals)).sh.

12 10 not 11

13 dorsalgia.ti,ab.

14 exp Back Pain/

15 backache.ti,ab.

16 exp Low Back Pain/

17 (lumbar adj pain).ti,ab.

18 coccyx.ti,ab.

19 coccydynia.ti,ab.

20 sciatica.ti,ab.

21 sciatic neuropathy/

22 spondylosis.ti,ab.

23 lumbago.ti,ab.

24 back disorder$.ti,ab.

25 or/13-24

26 Anticonvulsants/

27 (anticonvulsant* or anti convulsant* or anti-convulsant* or antiepileptic* or anti epileptic* or anti-epileptic*).mp.

28 exp Carbamazepine/

29 (Carbamazepine or Amizepin or Amizepine or Atretol or Biston or Calepsin or Carbamazepin or Carbategral or Carbatrol or Convuline or Epimax or Epitol or Equetro or Finlepsin or Lexin or Mazepine or Neurotol or Neurotop or Servimazepin or Sirtal or Tegral or Tegretal or Tegretol or Tegrital or Telesmin or Teril or Timonil).mp.

30 (Oxcarbazepine or Apydan or Oxocarbamazepine or Oxocarbazepine or Timox or Trileptal).mp.

31 (Felbamat or Felbatol or Taloxa).mp.

32 (Gabapentin or Neurontin or Neurotonin).mp.

33 (Levetiracetam or Keppra).mp.

34 (Pregabalin or Lyrica).mp.

35 (Phenytoin or Alepsin or Aleviatin or Antilepsin or Antisacer or Cansoin or Citrullamon or Comital or Danten or Dantoin or Denyl or Difetoin or Differenin or Difhydan or Di Hydan or Dihydan or Dilantin or Dintoin or Dintoina or Diphantoin or Diphantoine or Diphantoin or Diphedal or Diphedan or Diphenin or Diphenine or Diphentoin or Diphenylan or Diphenytoin or Ekko or Epanutin or Epelin or Epilantin or Eptal or Eptoin or Fenantoin or Fenitoin or Fenytoin or Fenytoine or Hidantal or Hydantin or Hydantinal or Hydantoinal or Idantoin or Lepitoin or Minetoin or Neosidantoina or Phenhydan or Phenhydane or Phenybin or Phenydan or Phenydantin or Phenytoine or Phenytoin or Phenytoinum or Phenytonium or Sanepil or Sodantoin or Sodanton or Solantoin or Solantyl or Tacosal or Zentropil).mp.

36 (lacosamide or erlosamide or vimpat).mp.

37 (Lamotrigine or Labileno or Lamictal).mp.

38 (Sodium valproate or Alpha Propylvalerate or Alpha Propylvaleric Acid or Apilepsin or Convulex or Depacon or Depakene or Depakin or Depakine or Deprakine or Dipropylacetate or Dipropylacetatic Acid or Dipropyl Acetic Acid or Dipropylacetic Acid or Diprosin or Epilim or Ergenyl or Everiden or Goilim or Labazene or Leptilan or Leptilanil or Mylproin or Myproic Acid or Orfiril or Orlept or Propymal or Valerin or Valparin or Valpro or Valproate or Valproate Sodium or Vupral).mp.

39 (Tiagabin or Gabitril).mp.

40 (Topiramate or Epitomax or Topamax or Topimax).mp.

41 (Clonazepam or Clonex or Klonopin or Paxam or Kriadex or Ravotril or Rivatril or Rivotril).mp.

42 or/26-41

43 12 and 25 and 42

Appendix 2. Criteria for assessing risk of bias for internal validity

Random sequence generation (selection bias)

Selection bias (biased allocation to interventions) due to inadequate generation of a randomised 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, minimisation (minimisation 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 judgement 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 randomisation); 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 hospitalisation, 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 standardised 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 randomised patients were reported/analysed in the group to which they were allocated by randomisation.   

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).

Other bias

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).

Contributions of authors

Conceiving the review: Fernanda Bono Fukushima (FBF) and Edison Iglesias de Oliveira Vidal (EIOV)
Co-ordinating the review: Regina El Dib (RED) and Roger Chou (RC)
Undertaking manual searches: Dailson Mamede Bezerra (DMB)
Screening search results: FBF, EIOV and Guilherme Antonio Moreira De Barros (GAMB)
Organising retrieval of papers: DMB
Screening retrieved papers against inclusion criteria: FBF, EIOV and GAMB

Appraising quality of papers: FBF and EIOV
Abstracting data from papers: FBF, EIOV and DMB
Writing to authors of papers for additional information: DMB
Providing additional data about papers: GAMB
Obtaining and screening data on unpublished studies: DMB and GAMB
Data management for the review: FBF and EIOV
Entering data into Review Manager (RevMan 5.2): FBF and EIOV
RevMan statistical data: RED
Other statistical analysis not using RevMan: RED
Interpretation of data: FBF, EIOV, GAMB, RC and RED
Statistical inferences: FBF, EIOV, GAMB, RC and RED
Writing the review: FBF, EIOV, GAMB, DMB, RC and RED
Securing funding for the review: FBF
Guarantor for the review (one author): RED
Person responsible for reading and checking review before submission: FBF, EIOV, GAMB, DMB, RC and RED

Declarations of interest

Dailson Mamede Bezerra: none known.

Regina El Dib: none known.

Edison Iglesias de Oliveira Vidal: none known.

Guilherme Antonio Moreira De Barros: none known.

Roger Chou: none known.

Fernanda Bono Fukushima: none known.

Sources of support

Internal sources

  • Our own, Brazil.

External sources

  • No sources of support supplied