Summary of findings
Description of the condition
Low back pain (LBP) is the main cause of pain, disability, social and financial cost throughout the world (Volinn 1997; Vos 2012). Approximately 80% of people will experience at least one episode of acute back pain during their lifetime (Cassidy 1998). Almost one quarter of North Americans are estimated to have experienced an episode of LBP within the previous three months (Deyo 2006). Although an early review concluded that 80% to 90% of people with chronic low back pain (CLBP) improve by 12 weeks (Shekelle 1995), a proportion continue to report symptoms over several months and even years. In one study, one-third of people with CLBP continued to be symptomatic after 12 months (Thomas 1999). More recent reviews suggest that the prevalence of LBP is around 23% (Vos 2012). Moreover, a substantial proportion of people with back pain will have recurrences even after the resolution of initial symptoms (Von Korff 1996).
CLBP and functionality
LBP is the main cause of disability-adjusted life years (DALYs) worldwide (Vos 2012) and the prevalence of CLBP-related disability is estimated at 11% (Vos 2012). Individuals with CLBP not only experience personal distress, but also present with significant sleep disorders and disability (Gore 2012). According to an early study (Spitzer 1987), fewer than 50% of individuals with CLBP who missed work for more than 12 weeks actually returned to work. An absence of two years from employment was associated with almost no chance of returning to work.
Description of the intervention
The vast majority of CLBP treatments are directed towards symptomatic and functional improvement rather than cure. Patients may be offered a variety of treatment regimens as either monotherapy or a combination of therapies. Treatments may include medications and physical modalities (for example, transcutaneous electrical nerve stimulation (TENS), massage therapy, work hardening), rehabilitation, or injection therapy (such as, epidurals, facet joint blocks, and trigger point injections) that are directed specifically at potential anatomic causes for CLBP. A proportion of individuals with CLBP will undergo surgery to alleviate their symptoms. Despite general acceptance of lumbar discectomy, with or without decompression, and lumbar fusion (with or without instrumentation), the actual success rates for symptomatic and functional improvement have been variable, with surgical 'failure' rates estimated between 10% and 40% (Fritsch 1996; Ostelo 2003). Furthermore, the results are similar with surgery or pharmacological therapy (Peul 2007). These individuals often return to the pool of patients with CLBP, and they often experience poor outcomes regardless of future treatment. Medications play an important role in the management of CLBP and generally fall into four broad categories: non-steroidal anti-inflammatory drugs (NSAIDs), antidepressants, muscle relaxants, and analgesics including opioids.
Opioids are generally classified as either weak or strong. These terms refer to relative efficacy rather than potency; weak opioids exhibit a ceiling to their analgesic effect, limited principally by increased adverse reactions. The use of opioids remains a controversial issue in the management of chronic non-cancer pain (CNCP) (Furlan 2010), and CLBP in particular (Turk 2011). The American College of Physicians & The American Pain Society consensus guidelines for the treatment of LBP recommend opioids for the short-term management of severe and disabling LBP that has had no response with anti-inflammatories or acetaminophen. Notably, this guideline was published in 2007 and includes only a few trials (Chou 2007). In contrast, the American Geriatrics Society Guidelines have suggested that given the problems of NSAIDs and cyclooxygenase-2 (COX-2) inhibitors, opioids should be considered first line treatment for moderate-to-severe pain in older adults (Ferrell 2009). However, recent evidence links the abuse of opioids to negative social consequences (Bohnert 2011).
Controversies with use of opioids
Although many clinicians believe that opioids offer a valuable tool in the management of CNCP, there is still a large group of practitioners who remain hesitant, or even opposed to, the use of these medications. A survey of Canadian physicians exploring attitudes towards opioid use for chronic pain confirmed that 35% of general practitioners and 23% of palliative care physicians would never use opioids for the management of severe CNCP (Morley-Foster 2003). A recent study of opioid prescribing stratified across the United States by region and by medical specialty found that 41.5% of respondents prescribed long-term opioids in fewer than 20% of their CNCP patients (Wilson 2013). Clinicians reluctant to prescribe opioids to treat people with CNCP believe that side-effects (Wilson 2013), somnolence resulting in poor function, the risk of abuse (Von Korff 2004), and general ineffectiveness of opioids may outweigh any potential benefit. Several trials have demonstrated that rather than underlying pathology, characteristics such as age, depression, personality disorder, and substance abuse, distinguished patients with CLBP who were on opioids from those who were receiving non-opioid treatments (Turk 1997; Breckenridge 2003; Edlund 2007). These trials continue to contribute to the confusion and uncertainty regarding the indications and actual benefits of opioids in CLBP. A recent survey among Canadian primary care physicians revealed that the most common fears for opioid prescription were abuse, overdose, and early prescription renewals (Wenghofer 2011).
How the intervention might work
Current evidence suggests that opioids are effective for the treatment of CNCP in the short-term (Furlan 2010), irrespective of somatic or neuropathic etiology. The diverse mechanisms of action of opioids across the central and peripheral nervous system can be the reason for unpredictable responses to these medications. More importantly, they can lead to the potential development of adverse effects, including development of addictive behaviour.
Why it is important to do this review
This is an update of a Cochrane review that was published in 2007 (Deshpande 2007). The original review included only four RCTs. Three of the trials included tramadol and a fourth trial evaluated morphine and oxycodone in an open-label fashion.
Our primary objective was to determine whether opioids were effective in improving pain, or function, or both, in individuals with CLBP.
Our secondary objectives were to determine the effectiveness of opioids in:
- Patients with CLBP with or without prior spinal surgery;
- Patients with CLBP with or without radicular symptoms (patients with symptoms radiating into the buttock or leg irrespective of radiological or electrophysiological evidence);
- Patients with CLBP managed with tramadol;
- Patients with CLBP managed with transdermal buprenorphine;
- Patients with CLBP managed with strong opioids.
Criteria for considering studies for this review
Types of studies
We included published RCTs with a blinded assessment of outcomes that compared any opioid to placebo or any other drug with analgesic properties. We had no restriction on the language of the publication.
Types of participants
We included male and female participants, aged 18 years or older, that had persistent pain in the low-back for at least 12 weeks, with or without radiating symptoms to the legs or prior low-back surgery (failed back surgery syndrome).
We defined LBP as pain occurring below the lower ribs and above the gluteal folds, including the buttocks. We defined failed back surgery syndrome as back pain, leg pain, or both, lasting longer than six months from the date of surgical intervention, or pain that began prior to one year from the date of intervention, after the individual had achieved symptomatic relief.
We excluded patients with cancer, infections, inflammatory arthritic conditions (including osteoarthritis [OA]) or compression fractures. We also excluded trials where < 50% of participants had CLBP or study authors failed to report results separately for this specific cohort
Types of interventions
We included trials that examined the use of any opioid prescribed in an outpatient setting, for a period of one month or longer. We considered trials with opioids given by oral, transdermal, mucosal (nasal or rectal), or intramuscular routes, administered either alone or in combination with other interventions, such as: pharmacological therapy (for example, anti-inflammatories, antidepressants, sedatives), physical modalities (for example, TENS, chiropractic), exercise, or alternative pain management techniques (for example, acupuncture).
We required opioids to be prescribed for a period of one month or longer to provide relevant feedback to the clinician and identify trials that may simulate actual clinical practice patterns. We excluded trials that examined opioids given by intravenous route, including implantable pumps, due to the invasive nature of the therapy and its limited clinical relevance in the outpatient setting. We did not assess the effectiveness of opioids used in neuraxial implantable pumps as this has been discussed elsewhere (Noble 2008).
We considered trials with the following comparisons:
- Opioids compared to placebo;
- Opioids compared to no treatment;
- Opioids compared to non-pharmacological treatments;
- Opioids compared to other pharmacological agents, alone or in combination (for example, NSAIDs, muscle relaxants, anti-depressants);
- Opioids given in combination with other pharmacological agents (for example, NSAIDs, muscle relaxants, anti-depressants) or non-pharmacological treatments compared to other pharmacological or non-pharmacological treatments, either alone or in combination.
We excluded trials where comparisons were made between opioids.
Types of outcome measures
Trials must have reported on at least one of four primary outcome measures for efficacy:
- Pain ratings: verbal rating scale, visual analog scale or final visit pain score.
- Function: Oswestry Disability Index (ODI), Roland-Morris Disability Questionnaire (RMDQ) or Quebec Back Pain Disability Scale (QBPDS).
- Global improvement: patient satisfaction or quality of life improvements.
- Proportion of patients reporting 30% or 50% pain relief.
- Work-related disability: time on compensation, return-to-work, or productivity.
- Treatment-related adverse effects.
- Others: healthcare usage, non-opioid medication consumption, addiction, or overdose-related events.
We grouped outcome measures according to the timing of post-randomization follow-up: very short-term (less than one month), short-term (between one and three months), intermediate (greater than three but less than six months) and long-term (longer than six months).
Search methods for identification of studies
We searched the following databases for relevant trials: MEDLINE (OVID) 1966 to Oct 2012; EMBASE (OVID) 1980 to Oct 2012; Cochrane Library, Central Register of Controlled Trials (Wiley) 2012, Issue 10; PsycINFO (OVID) 1967 to Oct 2012; and CINAHL (Ebsco) 1982 to Oct 2012. We performed electronic searches with the assistance of an experienced librarian, using the sensitive searches recommended by the Cochrane Back Review Group (Furlan 2009). We have presented the search strategy for MEDLINE in Appendix 1. We adapted this search strategy as indicated to search the other databases (see Appendix 2). We examined references provided in the trials we identified from the database search and relevant systematic reviews for further trials. We also tracked the citations of identified relevant trials.
Data collection and analysis
We followed the methods recommended by the Cochrane Back Review Group (Furlan 2009).
Selection of studies
Two teams of two authors each (AF and LEC; LEC and AD) independently screened titles, abstracts, and keywords of trials that we identified by the search strategies to determine if the references met the inclusion criteria. We obtained the full text of trials that either appeared to meet criteria or for which we considered their inclusion was uncertain. We screened these articles for inclusion and we resolved any disagreements through discussion.
Data extraction and management
Three authors (LEC, AD, AF) independently extracted data, using the standardized forms developed by the Cochrane Back Review Group, on characteristics of participants, intervention group, clinical setting, method of recruitment, interventions, primary and secondary outcomes, opioid abuse or addiction, side effects, country of study, and sponsorship of study. If data were not available in a format that was appropriate for data extraction, we contacted the authors of the trial for further clarification. We resolved any disagreements through discussion.
Given the similarities in populations, methodology, interventions and outcomes, we pooled data from trials comparing opioids to placebo (using Review Manager (RevMan)). We performed meta-analyses (both fixed-effect and random-effects methods) on the outcomes of pain, function, and side effects. If we noted a significant statistical discrepancy between methods, we reported the more conservative result. We reported the results of pain and function from the pooled data as standardized mean difference (SMD) with a 95% confidence interval (CI). We reported side effects using absolute risk differences (RD) with a 95% CI.
We used the GRADE approach, as recommended by the Cochrane Collaboration (Higgins 2011) and by the updated Cochrane Back Review Group method guidelines (Furlan 2009). Following GRADE guidelines, we categorized the quality of evidence as follows:
· High: further research is very unlikely to change the confidence in the estimate of effect.
· Moderate: further research is likely to have an important impact in the confidence in the estimate of effect.
· Low: 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: any estimate of effect is very uncertain.
We graded the evidence available on specific domains as follows:
1. Study design
In this review we only included randomized, controlled, double-blinded trials.
2. Risk of bias
Three authors (LC, AD and AF) independently evaluated the risk of bias of the selected articles, based on criteria described in the Cochrane Back Review Group's updated methods guidelines (Furlan 2009). We scored each criterion as "low risk", "high risk", or "unclear". We have presented the description of this evaluation in Appendix 3. We examined all trials for five types of bias:
- Selection (random sequence generation, allocation concealment, group similarities at baseline)
- Performance (blinding of participants, blinding of healthcare providers, co-interventions, and compliance with intervention)
- Attrition (dropouts and intention-to-treat (ITT) analysis)
- Measurement (blinding of the outcome assessors and timing of outcome assessment)
- Reporting bias (selective reporting)
We used the overall risk of bias for each trial in the GRADE synthesis. When all trials were judged as "low risk of bias" for all five categories, we did not downgrade the evidence. We downgraded the evidence by one point when less than three categories were judged "high or unclear". We downgraded the evidence by 2 points when four or more categories were judged "high or unclear".
Inconsistency refers to an unexplained heterogeneity of results. Widely differing estimates of the treatment effect (such as, heterogeneity or variability in results) across trials suggest true differences in underlying treatment effect. Inconsistency may arise from differences in: populations (for example, drugs may have larger relative effects in sicker populations), interventions (for example, larger effects with higher drug doses), or outcomes (for example, diminishing treatment effect with time). This item does not apply when there is only one trial. We downgraded the quality of evidence by one point when the heterogeneity or variability in results was large (for example: I
We assessed whether the question being addressed in this systematic review was different from the available evidence regarding the population, intervention, comparator, or an outcome. We downgraded the quality of evidence by one point when there was indirectness in only one area; and by two levels when there was indirectness in two or more areas.
Results are imprecise when trials include relatively few patients and few events and thus have wide CIs around the estimate of the effect.
For dichotomous outcomes, we considered imprecision for either of the following two reasons:
(1) There was only one trial. When there was more than one trial, the total number of events was < 300 (a threshold rule-of-thumb value) (Mueller 2007).
(2) 95% CI around the pooled or best estimate of effect included both (1) no effect and (2) appreciable benefit or appreciable harm. The threshold for "appreciable benefit" or "appreciable harm" is a relative risk reduction (RRR) or relative risk increase (RRI) > 25%. We downgraded the quality of the evidence by one point when there was imprecision due to (1) or (2); or by two levels when there was imprecision due to (1) and (2).
For continuous outcomes, we considered imprecision for either of the following two reasons:
(1) There was only one trial. When there was more than one trial, the total population size was < 400 (a threshold rule-of-thumb value; using the usual α and β, and an effect size of 0.2 SD, representing a small effect).
(2) 95% CI included no effect and the upper or lower CI crosses an effect size (standardized mean difference) of 0.5 in either direction. We downgraded the quality of the evidence by one point when there was imprecision due to (1) or (2); or by two points when there was imprecision due to (1) and (2).
6. Publication bias
Publication bias is a systematic underestimate or an overestimate of the underlying beneficial or harmful effect due to the selective publication of trials. We downgraded the quality of the evidence by one point when the funnel plot suggested publication bias.
7. Magnitude of the effect
We did not assess this in the review.
8. Dose response gradient
We did not assess this in the review.
9. Influence of all plausible residual confounding
We did not assess this in the review.
We prepared the summary of findings tables following published guidelines from the Cochrane Collaboration (Higgins 2011).
We used GRADEprofiler 3.6 to prepare the GRADE tables and Summary of Findings Tables.
Description of studies
Results of the search
We identified 2201 references through the literature search, which three authors (LC, AF, AD) screened by title and abstract. We obtained full-text articles for 91 studies and 12 RCTs met the inclusion criteria. We included three of the four trials that we included in the original review; we excluded one study (Jamison 1998) because it was not blinded. In total, we included 15 trials (5540 participants) in this review (Figure 1).
|Figure 1. Study flow diagram.|
We searched for trials registered on the clinicaltrials.gov website and we identified one trial evaluating the combination oxycodone + naltrexone (NCT01571362); one trial for hydromorphone (NCT01455519); one trial for the combination oxycodone naloxone (NCT01358526); and two trials using hydrocodone (NCT01789970 - NCT01081912) (see Characteristics of ongoing studies).
We included 15 RCTs in this review update. Six trials evaluated either tramadol alone (Schnitzer 2000; Vorsanger 2008; O'Donnell 2009; Uberall 2012) or the combination tramadol/acetaminophen (Ruoff 2003; Peloso 2004). One trial evaluated a drug with a similar mechanism of action, tapentadol (Buynak 2010). Two trials focused on morphine (Khoromi 2007; Chu 2012); two on oxymorphone (Hale 2007; Katz 2007); two trials investigated the effect of transdermal buprenorphine (Gordon 2010; Steiner 2011); and two papers evaluated the effectiveness of oxycodone (Webster 2006) or hydromorphone (Hale 2010) for CLBP.
All included trials were performed in a placebo-controlled fashion, except for one publication that reported two trials with identical methodology and used celecoxib in the control arm (O'Donnell 2009). All trials were conducted in the United States (Buynak 2010; Chu 2012; Hale 2007; Hale 2010; Katz 2007; Khoromi 2007; O'Donnell 2009; Peloso 2004; Ruoff 2003; Schnitzer 2000; Steiner 2011; Vorsanger 2008; Webster 2006), except for one in Canada (Gordon 2010) and another in Germany (Uberall 2012). We summarized the study characteristics of included trials in the Characteristics of included studies section.
Tramadol compared to placebo
Five RCTs, including 1378 participants, examined the use of tramadol compared to placebo (Schnitzer 2000; Ruoff 2003; Peloso 2004; Vorsanger 2008; Uberall 2012). Uberall 2012 used tramadol as the active control arm and evaluated the efficacy of flupirtine (a centrally-acting, non-opioid agent) for treatment of people with CLBP.
The five trials were similar in their reported demographics including age (mean age ranged between 47.1 (Schnitzer 2000) and 58.5 (Uberall 2012)); sex (female = 64.1% (Peloso 2004); female = 63.2% (Ruoff 2003); female = 50% (Schnitzer 2000); female = 62% (Uberall 2012); female: 50% (Vorsanger 2008)) and ethnicity (all involved a large number of Caucasian participants (> 85% of the randomized population)). Two trials included patients with previous low-back surgery if it was performed more than five years previously, but only if it was associated with complete pain relief (Schnitzer 2000; Peloso 2004). However, failed back surgery pain was an exclusion criteria across the other trials. All trials also excluded patients with pain in areas other than the low-back and individuals with a past history of substance abuse. Patient history prior to enrolment, including factors such as number of patients actively employed, status of compensation or the average duration of pain before entry into the trial, was not stated.
In two RCTs, tramadol was combined with acetaminophen (paracetamol) (Ruoff 2003; Peloso 2004). The average daily dose of tramadol was approximately 150 mg (Ruoff 2003; Peloso 2004), 242 mg (Schnitzer 2000), 200 mg (Uberall 2012) and 200 to 300 mg/day (Vorsanger 2008). Three trials had a double-blind phase duration of 90 days (Peloso 2004; Ruoff 2003; Vorsanger 2008); whereas two studies were just over four weeks in duration (Schnitzer 2000; Uberall 2012). The included trials did not allow initiation of other treatments during the follow-up periods, although two trials permitted continuation of physiotherapy started prior to inclusion in the trial (Schnitzer 2000; Peloso 2004). None of the included trials documented the number of people receiving concurrent treatments or the types of concurrent treatment they received. Two trials allowed the concomitant use of diclofenac (Uberall 2012) or acetaminophen (Vorsanger 2008).
Each of the included studies included pain intensity as the primary outcome. Three trials used a visual analogue scale (VAS) (Ruoff 2003; Peloso 2004; Vorsanger 2008). In Schnitzer 2000, trial authors used the primary efficacy outcome of "distribution of time to therapeutic failure" (which the trial authors defined as the time to discontinuation of therapy due to inadequate pain relief). They included pain measured with the VAS as a secondary outcome. Uberall 2012 used the change from baseline as the primary outcome. Four trials used the RMDQ to measure functional outcome and Uberall 2012 opted for the pain disability index (PDI).
Buprenorphine compared to placebo
We included two RCTs that compared transdermal buprenorphine versus placebo for treatment of people with CLBP (Gordon 2010; Steiner 2011). Gordon 2010 used a crossover design, each period included a four-weeks follow-up; Steiner 2011 used a 15-week enrichment design including three weeks of open-label titration followed by 12-week randomized and double-blind fashion.
Both studies reported similar demographics including mean age (50.7 (Gordon 2010); 49.4 (Steiner 2011)); and sex (female (Steiner 2011): 55%; female: 60.3% (Gordon 2010)). In Steiner 2011, 70% of the participants were caucasian, while Gordon 2010 did not report the ethnicity of the participants. Both studies had substance abuse as an exclusion criteria. Additionally, Steiner 2011 monitored opioid abuse or diversion behaviour and listed radicular symptoms as an exclusion criteria. Gordon 2010 used concurrent physiotherapy as an exclusion criteria; in contrast, Steiner 2011 allowed physiotherapy if participants started it at least two weeks prior to study entry. The trial authors did not state working or compensation status in the study demographics.
Gordon 2010 used buprenorphine patches of 10 or 20 mcg/hour, up to a maximum dose of 40. Steiner 2011 titrated the dose of buprenorphine from 5 mcg/hour to 20 mcg/hour during the run-in period and maintained a maximum dose of 20 mcg/hour during the double-blind phase. Gordon 2010 allowed participants to use analgesic rescue with acetaminophen and Steiner 2011 allowed participants to use acetaminophen plus ibuprofen and oxycodone IR during the first six weeks of the double-blind phase. Gordon 2010 allowed participants to use non-opioid analgesics (antidepressants or anticonvulsants).
Steiner 2011 defined the primary outcome as the "average pain in the last 24 hours at week 12". Gordon 2010 used daily pain intensity as the primary outcome. The trials authors measured functional status using either the ODI (Steiner 2011) or the QBPD (Gordon 2010).
Strong opioids (morphine, hydromorphone, oxymorphone, tapentadol or oxycodone) compared to placebo
We included seven RCTs in this category: Buynak 2010 used tapentadol; two RCTs used morphine (Khoromi 2007; Chu 2012); two RCTs evaluated oxymorphone (Hale 2007; Katz 2007); one RCT assessed hydromorphone (Hale 2010); and one RCT focused on oxycodone (Webster 2006). Notably, three of the seven included RCTs were not designed with the primary objective of demonstrating the effectiveness of the opioid for the treatment of people with CLBP. Webster 2006 aimed to explore an opioid alternative (oxycodone combined with low-dose naltrexone) to avoid physical dependence after long-term treatment. Khoromi 2007 explored the effectiveness of morphine in chronic radicular LBP. Chu 2012 focused on the potential development of opioid tolerance versus opioid-induced hyperalgesia.
In the included trials, the mean age of participants ranged between 45 years (Chu 2012) and 53 years (Khoromi 2007). The proportion of women did not significantly differed across the trials (female = 59.3.1% (Buynak 2010); female = 43.9% (Chu 2012); female = 45.1% (Hale 2007); female = 50.4% (Hale 2010); female: 53.2% (Katz 2007); female: 50% (Khoromi 2007); female: 61.2% (Webster 2006)). The vast majority of the participants were Caucasian. Four trials excluded patients with any history of opioid abuse (Buynak 2010; Chu 2012; Khoromi 2007; Webster 2006), but three included chronic opioid users (Hale 2007; Katz 2007; Hale 2010). History of failed back surgery pain or LBP that could have some benefit with spine surgery were also exclusion criteria. All RCTs excluded patients with radicular symptoms or neurological abnormalities in the lower extremities, except for Khoromi 2007, which focused on patients with sciatica. All RCTs allowed physiotherapy or physical exercise if participants started at least two weeks prior to the trial start. Only Khoromi 2007 described the work or compensation status of the participants.
The mean dose of opioids was 78 mg morphine (Chu 2012); 62 mg morphine (Khoromi 2007); 100 to 250 mg tapentadol (40 to 100 morphine equivalent) (Buynak 2010); 80.9 mg oxymorphone (243morphine equivalent) (Hale 2007); 39.2 mg oxymorphone (117.6 morphine equivalent) (Katz 2007); 37.8 mg hydromorphone (189 morphine equivalent) (Hale 2010), and 39 mg of oxycodone (58.5 morphine equivalent) (Webster 2006). The included trials that evaluated strong opioids for LBP did not allow participants to use concurrent analgesics (including antidepressants and anticonvulsants). All strong opioid trials used pain scores as a primary outcome. Additionally, one trial used quantitative sensory testing (Chu 2012). Trial authors measured functional status using SF-36 (Buynak 2010), RMDQ (Hale 2010; Chu 2012), ODI (Webster 2006; Khoromi 2007); but two oxymorphone trials did not report functional scores (Hale 2007; Katz 2007).
Most of the studies had a duration of 12 weeks (Webster 2006; Hale 2007; Katz 2007; Hale 2010). The tapentadol trial had the longest follow-up (15 weeks) (Buynak 2010). The morphine trials ran for four weeks (Chu 2012) and nine weeks (Khoromi 2007). Three out of seven RCTs used an enriched enrolment randomized withdrawal design (Hale 2007; Katz 2007; Hale 2010) and the pharmaceutical industry conducted and sponsored all three of these RCTs.
Opioids compared with other analgesics
O'Donnell 2009 reported two trials with identical methodology (randomized, double-blinded and parallel) that compared the effectiveness of tramadol (50 mg four times a day) versus celecoxib (200 mg twice a day) for treatment of CLBP. 798 participants (mean age 47.5; female 56.4%) received tramadol versus 785 participants (mean age 48; female 58.7%) treated with celecoxib. The rate of participants that completed the six weeks of follow-up was significantly higher in the celecoxib group (86% versus 71.8%). 62% of the participants were Caucasian. This is the only trial that used the rate of participants that had at least 30% improvement in pain ratings from baseline to week 6. The trial authors excluded patients with low back surgery within six months prior to study entry or those taking any kind of analgesic treatment.
Five of the studies that we already described had a second active arm: Buynak 2010 compared tapentadol to sustained-release (SR) oxycodone. Webster 2006 used oxycodone and included two additional arms of a tablet combining oxycodone and naltrexone; we did not use any of the data from the combination arms in the review. Vorsanger 2008 analyzed the dose response of tramadol and had two tramadol treatment arms; we included the data using the higher dose. Khoromi 2007 (crossover design) included one period of nortriptyline. Finally, Uberall 2012 included a control arm of tramadol and we used these data in the review.
We excluded 36 studies from the review: six were developed in an open label fashion (Jamison 1998 (included in the original review); Adams 2006; Allan 2005; Gaertner 2006; Pascual 2007; Peniston 2009); 12 compared opioid versus opioid (Beaulieu 2007; Gostick 1989; Hale 1997; Hale 1999; Hale 2005; Hale 2009; Likar 2007; Nicholson 2006a; Perrot 2006; Rauck 2006; Rauck 2007; Salzman 1999); two used an opioid for analgesic rescue (Cloutier 2013; Vondrackova 2008); one did not meet our definition of CLBP (Gordon 2010a); three due to follow-up < four weeks (Kuntz 1996; Li 2008; Muller 1998); in two, the study population had < 50% of participants with a primary diagnosis of CLBP (Landau 2007; Moulin 1996); seven were secondary analyses (Gould 2009; Kalso 2007) or observational studies (Taylor 2007; Volinn 2009; Wallace 2007; Weinstein 2006; Wiesel 1980); one focused on the effectiveness of opioids for breakthrough LBP (Portenoy 2007); one focused on the timing or scheduling of the drug (Nicholson 2006), or pharmacokinetics issues (Sarbu 2008). See Characteristics of excluded studies.
Risk of bias in included studies
We presented the results of the included articles in Figure 2.
|Figure 2. Summary of risk of bias of included studies.|
Only four trials described the method used for sequence generation and allocation concealment (Webster 2006; Khoromi 2007; Buynak 2010; Gordon 2010); five trials described adequately the sequence generation (Schnitzer 2000; Ruoff 2003; Vorsanger 2008; O'Donnell 2009; Uberall 2012) and six trials reported the allocation concealment (Schnitzer 2000; Ruoff 2003; Katz 2007; Vorsanger 2008; O'Donnell 2009; Uberall 2012).
Participants and medication providers were properly blinded in most of the studies through the use of physically identical capsules/tablets (Buynak 2010; Chu 2012; Gordon 2010; Hale 2010; Katz 2007; Khoromi 2007; Peloso 2004; Ruoff 2003; Schnitzer 2000; Steiner 2011; Uberall 2012; Vorsanger 2008; Webster 2006). However, a method to keep the outcome assessors blinded was generally flawed in all trials except for Khoromi 2007 (outcomes assessors could have guessed the allocation based on the side effects profile of the opioids).
Incomplete outcome data
All included studies had a drop-out rate over 20% that qualified them for high risk of bias; however, ITT analysis played in favour of most of them. A Last-Observation-Carried-Forward analysis was qualified as high risk of bias (Figure 2).
Only nine out of 15 studies indicated pre-trial registration on a clinical trial registry (Buynak 2010; Chu 2012; Gordon 2010; Hale 2010; Katz 2007; Khoromi 2007; O'Donnell 2009; Steiner 2011; Uberall 2012); however, most of the trials reported outcomes that were clinically relevant.
Other potential sources of bias
All studies showed that participants between groups were similar. Only one study assessed the count of tablets to verify the compliance of medication intake (Uberall 2012). More commonly, the number of drop-outs due to non-compliance to medications was reported. In several the studies (Hale 2007; Hale 2010; Katz 2007; Vorsanger 2008; Webster 2006) the use of analgesics was restricted to the study drugs. We constructed funnel plots but we could not identify any evidence of publication bias (Figure 3; Figure 4; Figure 5; Figure 6).
|Figure 3. Funnel plot of comparison: 1 Tramadol compared to placebo, outcome: 1.1 Pain intensity (higher score means worse pain levels).|
|Figure 4. Funnel plot of comparison: 1 Tramadol compared to placebo, outcome: 1.2 Disability (higher ratings mean greater disability).|
|Figure 5. Funnel plot of comparison: 3 Strong opioids compared to placebo, outcome: 1.3 Mean pain intensity.|
|Figure 6. Funnel plot of comparison: 3 Strong opioids compared to placebo, outcome: 3.4 Disability.|
Effects of interventions
Efficacy of tramadol compared to placebo
A total of 1378 participants were included in five studies of tramadol compared to placebo (Peloso 2004, Ruoff 2003, Schnitzer 2000, Uberall 2012, Vorsanger 2008). Meta analysis (fixed effects) was used to combine the results of these studies. There is low quality evidence ( Table 1) that tramadol is better than placebo in improving pain (SMD -0.55, 95% CI -0.66 to -0.44) (see Analysis 1.1); and moderate quality evidence that tramadol is better than placebo in improving functional outcomes (SMD -0.18, 95%CI -0.29 to -0.07) (see Analysis 1.2).
Efficacy of buprenorphine compared to placebo
A total of 653 participants were included in two studies of transdermal buprenorphine compared to placebo (Gordon 2010 and Steiner 2011). Meta-analysis (fixed effects) was used to combine the results of these studies. There is very low quality evidence ( Table 2) that transdermal buprenorphine is better than placebo in improving pain (SMD -2.47, 95%CI -2.69 to -2.25) (see Analysis 2.1); and very low quality evidence of no difference on functionality outcomes (SMD -0.14, 95%CI -0.53 to 0.25) (see Analysis 2.4).
Efficacy of strong opioids compared to placebo
We identified seven RCTs for inclusion but we could only use six in the meta-analysis, as we could not obtain relevant data for the primary outcome from the authors of Hale 2007. A total of 1887 participants were included in six studies of strong opioids compared to placebo (Buynak 2010, Chu 2012, Hale 2010, Katz 2007, Khoromi 2007, Webster 2006). Meta-analysis (fixed effects) was used to combine the results of these studies. There is moderate quality evidence ( Table 3) that strong opioids are better than placebo in reducing pain (SMD -0.43, 95%CI -0.52 to -0.33) (see Analysis 3.1); and moderate quality evidence that they are better than placebo in improving functional outcomes (SMD -0.26, 95% CI -0.37 to -0.15) (see Analysis 3.4).
Adverse effects of opioids compared to placebo
Ten studies described one or more of 14 adverse events ( Analysis 4.2). People treated with opioids had a statistically significant higher incidence of nausea (10%, 95% CI 7% to 14%), dizziness (8%, 95% CI 5% to 11%), constipation (7%, 95% CI 4% to 11%), vomiting (7%, 95% CI 4% to 9%), somnolence (6%, 95% CI 3% to 9%) and dry mouth (6%, 95% CI 2% to 10%) than people treated with placebo. People who received opioids had a < 5% higher incidence of headaches, pruritis, fatigue, anorexia, increased sweating and hot flushes compared to placebo. People treated with either opioids or placebo showed no differences regarding the number of people with upper respiratory tract infection (-2%, 95% CI -8% to 3%) or sinusitis (2%, 95% CI -3% to 6%).
Effectiveness of opioids versus other drugs
We could not perform a meta-analysis of data comparing opioids (tramadol) and NSAIDs (such as celecoxib) as we only found one RCT with 1583 participants (O'Donnell 2009). There is very low quality evidence ( Table 4) that tramadol is better than celecoxib in reducing pain (RR 0.82, 95% CI 0.76 to 0.90) (see Analysis 5.1). There was no information about functional status outcomes.
Two RCTs, including 272 participants in total, compared opioids to the antidepressants nortriptyline (Khoromi 2007) or flupirtine (Uberall 2012). Meta-analysis (fixed effects) was used to combine the results of these studies. There is very low quality evidence ( Table 5) of no difference in pain outcomes (SMD 0.21, 95% CI -0.03 to 0.45) (see Analysis 6.1); and there is very low quality evidence of no difference for functional status outcomes (SMD -0.11, 95% -0.63 to 0.42) (see Analysis 6.2)
We could not assess the secondary objectives of this review due to paucity of data. In particular, we could not perform subgroup analyses on the following categories:
- Route of opioid delivery (oral, intramuscular, transdermal);
- Type of opioid (morphine, codeine, oxycodone, hydromorphone, fentanyl);
- Duration of treatment (shorter than 12 months, 12 months or longer);
- CLBP non-surgical versus prior spine surgery (failed back surgery syndrome);
- CLBP with or without radiating symptoms;
- Pharmaceutical sponsored studies compared to non-sponsored trials;
- Enriched versus non-enriched enrolment randomized design.
We included 15 RCTs in this review that assessed the use of opioids for longer than four weeks in the management of CLBP. Overall, the quality of the evidence ranged from very low to moderate regarding use of opioids compared to placebo for pain and functional outcomes. The magnitude of the effect sizes were small to medium. All trials suffered from attrition bias with a large number of drop-outs. Many trials employed an enriched enrolment design which is known to under-report adverse events (Furlan 2011). The duration of the included RCTs was longer than four weeks but shorter than 15 weeks. Also, there was poor generalizability to populations at high risk for complications. We identified very few active-controlled (non placebo-controlled) trials. We identified an insufficient number of trials that examined use of tramadol compared to NSAIDS (such as celecoxib) or compared use of opioids with use of antidepressants to treat people with CLBP.
1) Strict inclusion criteria and duration of treatment
In the included trials, CLBP was well-defined. However, these trials imposed limitations by excluding patients who presented with pain outside this area (even those with radicular symptoms), had previous unsuccessful lumbar surgery or a history of substance abuse. Given the heterogeneous nature of the CLBP population, narrowly defined criteria prevent extrapolation of results to a more diverse group commonly seen in clinical settings. Importantly, exclusion of failed back surgery syndrome is also significant since it may occur in 10% to 40% of lumbar spine operations and contributes to CLBP (Oaklander 2001).
Our review excluded trials of opioid use in CLBP that were shorter than four weeks. Only two trials followed the participants for more than three months (15 weeks) (Buynak 2010; Steiner 2011). While these trials lasted substantially longer than most involving opioids and CLBP, we consider these articles to have a 'short-term' time frame. This limited treatment duration, when in reality patients are often treated for years, leaves important unanswered questions including long-term efficacy, safety, tolerance and pain sensitivity (Ballantyne 2003). Only one study focused on the potential development of opioid tolerance (Chu 2012), but the participants were followed for only one month. The high drop-out rate in the included studies demonstrates the huge challenge of developing double-blinded and placebo-controlled studies for long-term follow-up. We recommend that future studies should compare opioids to other analgesics with the goal of obtaining long-term data on relative effectiveness and safety. These studies should also enroll patients commonly presenting with CLBP, including those with prior spine surgery and at variable risk for opioid misuse or abuse (for example, explicitly identifying risk using valid questionnaires).
2) Poorly-defined study population
In the included RCTs that compared opioids with placebo, the study authors did not report sufficient information regarding the history of study populations. Although study authors documented demographic data well, many studies neglected to report other parameters affecting outcomes, such as duration of pain prior to enrolment, employment or compensation status or poor response to previous treatment, including opioids (Sanders 1986; Greenough 1993; Andersson 1999). Thus we were unable to compare intervention and placebo arms based on potentially relevant factors other than age, sex and race. Finally, all studies permitted physiotherapy under certain circumstances, but none of the trials reported the number of patients who may have received concurrent treatment or the types of therapy these patients obtained.
3) Limited interpretation of functional improvement
Most of the studies used validated questionnaires to assess functional outcomes. As noted by our results, the pooled SMD favoured in a moderate grade the use of tramadol or strong opioids for improvement of the functional outcomes. Further information is required for any recommendation for transdermal buprenorphine.
An additional limitation regarding functional outcomes is the difficulty associated with the interpretation of these data in meaningful economic or social activities, such as return-to-work or improvement in ADLs. This issue is not specific to these trials, but highlights a problem present in the pain literature when attempting to interpret improvement registered in research-based tools alone.
4) High drop-out rates and ITT analysis
Most studies had significant drop-out rates (> 20%). Although the reasons were clearly documented, the implications on final outcomes could be significant. Experimental mortality (loss of patients during the trial) with greater loss in the control arm could enhance the effect seen in favour of treatment. In addition, substantial drop-outs reduce the power of the study, compromising the ability to detect a significant difference. Overall, interpretation of the study outcomes with any level of confidence is questionable, given the significant number of drop-outs.
Several studies stated that efficacy analysis was performed on the ITT population. However, some of them failed to perform a proper ITT. The method of handling absent data for patients lost to follow-up was documented through the use of LOCF. This method has been criticized given the potential overestimation of the effect (Moore 2012).
5) Comparison to other reviews on opioids in CNCP and CLBP
Two recently published systematic reviews have addressed the issue of opioids in the pharmacological management of CNCP (Furlan 2011) and CLBP (Kuijpers 2011). Furlan 2011 concluded that opioids were more effective than placebo for improving both pain and function in the management of CNCP. The results were significant for both neuropathic and nociceptive pain. Subgroup analyses revealed that only strong opioids (oxycodone and morphine) were statistically more effective in reducing pain but not function when compared to naproxen and nortriptyline. Kuijpers 2011 evaluated opioids, antidepressants and NSAIDs for CLBP; however, they excluded patients with sciatica. Several studies that we included in our review were not considered in Kuijpers 2011 due to timing of publication. Their conclusion regarding the effectiveness of opioids does not differ from our conclusion.
Our review confirms the effectiveness of tramadol, buprenorphine and strong opioids in the management of CLBP in the short-term. Other systematic reviews on opioids in people with CNCP have included people with multiple pathologies. This factor and the predominance of short-term studies could limit any meaningful interpretation when considering opioids for the long-term management of CLBP.
The results of our review differ from another published systematic review (Martell 2007). The review (Martell 2007) included 15 studies in the literature assessing the efficacy of opioids in CLBP. Nine of the studies considered comparisons among different opioids, while another six compared opioids with placebo or other analgesics. Meta-analysis of this latter group was completed with four of the six studies. The review authors found that opioids were ineffective in the management of CLBP when compared to the pooled sample of placebo and other analgesics.
The existence of discordant reviews has been previously described in the literature (Jadad 1997; Furlan 2001). The only common clinical query between our review and that of Martell 2007 related to the efficacy of opioids in CLBP. Notably, the two reviews used different outcomes to define the efficacy of opioids. Our review considered pain and function as outcome measures. Also, there were differences between inclusion and exclusion criteria. Our review restricted original articles to opioid treatment that was longer than one month in duration to provide more meaningful clinical interpretation in the management of CLBP. We excluded comparisons among opioids to avoid issues with head-to-head trials or equivalency determinations. We also considered only articles published in peer-review journals. Taking these criteria into account, we excluded nine trials (all opioid comparators) found in Martell 2007 from our review. From the six trials comparing the efficacy of opioids to placebo or another analgesic, we excluded five from our review for the following reasons: two trials were published in abstract form (Tennant 1993; Richards 2002), two trials had a treatment duration of less than 30 days (Kuntz 1996; Muller 1998) and one trial had a lack of randomization when comparing opioids to placebo (Hale 2005; Characteristics of excluded studies). The three trials (all involving tramadol) we used to derive our meta-analyses were absent from the Martell 2007 review. Although not specifically stated in their inclusion and exclusion criteria, the review authors may have excluded tramadol as an opioid, given its atypical status. Finally, Martell 2007 combined studies involving placebo and other comparators to determine efficacy. In this case, conceptual homogeneity may not have existed due to differences in patient response to an active control compared with placebo. Statistical pooling of these studies may lead to questionable results.
Many people experience recurring episodes of LBP or never fully recover from their initial episode (Abenhaim 1988; Von Korff 1996). With direct and indirect costs estimated to exceed $100 billion annually in the United States alone, LBP continues to inflict a huge economic toll on society (Hashemi 1997; Katz 2006). Opioids have become a popular tool to help manage patients with CLBP. The prevalence of opioid prescribing in CLBP varies by treatment setting but has been found to be as low as 3% or as high as 66% (Martell 2007). Moreover, the same review (Martell 2007) identified prescription of opioids to be more common to patients with impaired functional status. Despite significant concerns surrounding the use of opioids, there is still little evidence in the literature for their efficacy and effectiveness in long-term treatment of CLBP. Although few systematic reviews suggest that opioids are effective in the management of CNCP in general, the extrapolation of this evidence to CLBP is cautioned. Further, the few original studies that do exist focusing on opioids for the management of CLBP are of limited value in clinical practice given their lack of long-term follow-up and description of long-term safety profile. As the pendulum has swung from an 'opiophobic' to an 'opiophilic' society, physicians should question whether the current trend is based on evidence or simply the outcries of well-intentioned patient advocates and aggressive marketing efforts by the pharmaceutical industry (Chinellato 2003).
Implications for practice
There is evidence (multiple high quality RCTs) that the use of tramadol (a weak atypical opioid) or strong opioids results in improved pain and moderate changes in function in the short-term in people with CLBP when compared with placebo. However, the general applicability of this treatment to the clinical setting is questionable. Several factors, including the strict inclusion criteria of the original studies, high drop-out rates, and the poor description of the study population regarding duration of pain, concurrent treatments, work status, and compensation, limit the reported results. Notably, a number of important outcomes that capture patient function were absent (such as return-to-work). Finally, there is strong evidence that nausea is more common in patients with CLBP being treated with opioids when compared to placebo.
Implications for research
CLBP is a prevalent condition with significant socioeconomic implications in the Western world. Given the escalating use of opioids in CNCP (a subset of which is CLBP) more quality research is needed to understand i) the long term benefits and risks of opioid therapy including the different subgroups of CLBP (for example, failed back surgery syndrome and CLBP with radicular symptoms); ii) opioid effectiveness relative to other conventional physical and medical treatments; iii) characteristics of patients who are most likely to respond to long-term opioid therapy; and iv) the predictors of opioid side effects, abuse and misuse in this population.
We are grateful to Rachel Couban (Cochrane Back Review Group Trials Coordinator) for assisting with literature searches and Ute Bültmann for helping to translate the non-English language study. We would like to gratefully and sincerely thank Teresa Marin (Managing Editor, Cochrane Back Review Group) for her invaluable assistance on the manuscript preparation.
Data and analyses
- Top of page
- Summary of findings [Explanations]
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Index terms
Appendix 1. MEDLINE search strategy
1 randomized controlled trial.pt.
2 controlled clinical trial.pt.
3 Randomized Controlled Trials/
4 Random Allocation/
5 Double-Blind Method/
6 Single-Blind Method/
8 Animal/ not Human/
9 7 not 8
10 clinical trial.pt.
11 explode Clinical Trials/
12 (clinical$ adj 25 trial$).tw.
13 ((singl$ or doubl$ or trebl$ or tripl$) adj(mask$ or blind$)).tw.
17 Research Design/
18 (latin adj square).tw.
20 19 not 8
21 20 not 9
22 Comparative Study/
23 explode Evaluation Studies/
24 Follow-Up Studies/
25 Prospective Studies/
26 (control$ or prospective$ or volunteer$).tw.
27 Cross-Over Studies/
29 28 not 8
30 29 not (9 or 21)
31 9 or 21 or 30
32 PAIN/pc, dt, rh, th [Prevention & Control, Drug Therapy, Rehabilitation, Therapy]
33 Chronic Disease/dt, pc, rh, th [Drug Therapy, Prevention & Control, Rehabilitation, Therapy]
34 (chronic adj3 pain).mp
35 Low Back Pain/
36 (low adj back adj pain).mp
37 or/ 32-36
38 exp Analgesics, opioid/
52 or/ 38-51
53 31 and 37 and 52
Appendix 2. Other search strategies
1 exp Clinical Trial/
2 exp randomization/
3 Double Blind Procedure/
4 Single Blind Procedure/
6 exp animal/
8 6 or 7
9 exp human/
10 8 not 9
11 5 not 10
12 (clinical$ adj25 trial$).tw.
13 ((singl$ or doubl$ or trebl$ or tripl$) adj (mask$ or blind$)).tw.
14 exp Placebo/
17 methodology/ or latin square design/
18 (latin adj square).tw.
20 19 not 10
21 20 not 11
22 comparative study/
24 Follow Up/
25 Prospective Study/
26 (control$ or prospective$ or volunteer$).tw.
27 Crossover Procedure/
29 28 not 10
30 29 not (11 or 21)
31 30 or 21 or 11
32 exp Chronic Pain/
33 exp PAIN/pc, rh, dt, th [Prevention, Rehabilitation, Drug Therapy, Therapy]
34 exp Chronic Disease/pc, rh, dt, th [Prevention, Rehabilitation, Drug Therapy, Therapy]
35 33 and 34
36 32 or 35
37 (chronic adj3 pain$).tw.
38 exp Low Back Pain/
39 (low adj back adj pain$).tw.
41 exp Narcotic Analgesic Agent/
56 31 and 40 and 55
S69 S53 and S68
S68 S54 or S55 or S56 or S57 or S58 or S59 or S60 or S61 or S62 or S63 or S64 or S65 or S66 or S67
S67 (MH "Tramadol") OR "tramadol"
S66 (MH "Sufentanil") OR "sufentanil"
S65 (MH "Propoxyphene") OR "propoxyphene"
S64 (MH "Pentazocine") OR "pentazocine"
S62 (MH "Oxycodone") OR "oxycodone"
S61 (MH "Morphine+") OR "morphine"
S60 (MH "Meperidine") OR "meperidine"
S56 (MH "Fentanyl+") OR "fentanyl"
S55 (MH "Codeine+") OR "codeine"
S54 (MH "Analgesics, Opioid+")
S53 S28 and S52
S52 S48 or S51
S51 S49 or S50
S50 (MM "Chronic Disease/DT/PC/RH/TH")
S49 (MM "Pain/PC/DT/RH/TH")
S48 S35 or S43 or S47
S47 S44 or S45 or S46
S45 (MH "Spondylolisthesis") OR (MH "Spondylolysis")
S44 (MH "Thoracic Vertebrae")
S43 S36 or S37 or S38 or S39 or S40 or S41 or S42
S42 lumbar N2 vertebra
S41 (MH "Lumbar Vertebrae")
S37 (MH "Sciatica")
S36 (MH "Coccyx")
S35 S29 or S30 or S31 or S32 or S33 or S34
S34 lumbar N5 pain
S33 lumbar W1 pain
S31 (MH "Low Back Pain")
S30 (MH "Back Pain+")
S28 S26 NOT S27
S27 (MH "Animals")
S26 S7 or S12 or S19 or S25
S25 S20 or S21 or S22 or S23 or S24
S21 followup stud*
S20 follow-up stud*
S19 S13 or S14 or S15 or S16 or S17 or S18
S18 (MH "Prospective Studies+")
S17 (MH "Evaluation Research+")
S16 (MH "Comparative Studies")
S15 latin square
S14 (MH "Study Design+")
S13 (MH "Random Sample")
S12 S8 or S9 or S10 or S11
S9 (MH "Placebos")
S8 (MH "Placebo Effect")
S7 S1 or S2 or S3 or S4 or S5 or S6
S3 clinical W3 trial
S2 "randomi?ed controlled trial*"
S1 (MH "Clinical Trials+")
#1 MeSH descriptor: [Back Pain] explode all trees
#4 MeSH descriptor: [Low Back Pain] explode all trees
#5 lumbar next pain OR coccyx OR coccydynia OR sciatica OR spondylosis
#6 MeSH descriptor: [Spine] explode all trees
#7 MeSH descriptor: [Spinal Diseases] explode all trees
#8 lumbago OR discitis OR disc near degeneration OR disc near prolapse OR disc near herniation
#9 spinal fusion
#10 spinal neoplasms
#11 facet near joints
#12 MeSH descriptor: [Intervertebral Disk] explode all trees
#15 failed near back
#16 MeSH descriptor: [Cauda Equina] explode all trees
#17 lumbar near vertebra*
#18 spinal near stenosis
#19 slipped near (disc* or disk*)
#20 degenerat* near (disc* or disk*)
#21 stenosis near (spine or root or spinal)
#22 displace* near (disc* or disk*)
#23 prolap* near (disc* or disk*)
#24 MeSH descriptor: [Sciatic Neuropathy] explode all trees
#26 back disorder*
#27 back near pain
#28 #1 or #2 or #3 or #4 or #5 or #6 or #7 or #8 or #9 or #10 or #11 or #12 or #13 or #14 or #15 or #16 or #17 or #18 or #19 or #20 or #21 or #22 or #23 or #24 or #25 or #26 or #27
#29 MeSH descriptor: [Analgesics, Opioid] explode all trees
#46 #29 or #30 or #31 or #32 or #33 or #34 or #35 or #36 or #37 or #38 or #39 or #40 or #41 or #42 or #43 or #44 or #45
#47 #28 and #46 in Trials
1 clinical trials/
2 controlled trial.mp.
4 (Random* adj3 trial).mp.
5 (clin* adj3 trial).mp
6 (sing* adj2 blind*).mp.
7 (doub* adj2 blind*).mp.
8 placebo.mp. or exp Placebo/
9 latin square.mp.
10 (random* adj2 assign*).mp.
11 prospective studies/
12 (prospective adj stud*).mp.
13 (comparative adj stud*).mp.
14 treatment effectiveness evaluation/
15 treatment effectiveness evaluation/
16 (evaluation adj stud*).mp.
17 exp Posttreatment Followup/
18 follow?up stud*.mp.
20 back pain/
21 lumbar spinal cord/
22 (low adj back adj pain).mp.
23 (back adj pain).mp.
24 spinal column/
25 (lumbar adj2 vertebra*).mp.
30 back disorder*.mp.
31 "back (anatomy)"/
32 ((disc or disk) adj degenerat*).mp.
33 ((disc or disk) adj herniat*).mp.
34 ((disc or disk) adj prolapse*).mp.
35 (failed adj back).mp.
37 exp opiates/
38 exp analgesic drugs/
39 codeine.mp. or exp Codeine/
40 fentanyl.mp. or exp Fentanyl/
44 exp Meperidine/ or meperidine.mp.
45 morphine.mp. or exp Morphine/
48 pentazocine.mp. or exp Pentazocine/
50 tramadol.mp. or exp Tramadol/
54 36 and 53
55 19 and 54
Appendix 3. Criteria for risk of bias assessment for RCTs
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 or 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 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 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 (for example, a list of random numbers); assignment envelopes were used without appropriate safeguards (for example, 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 (for example, 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 (for example, 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 (for example, 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 (for example surgery), this item is irrelevant (van Tulder 2003).
There is low risk of bias if all randomized patients were reported or 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 (for example, study funding).
Appendix 4. Questions for clinical relevance assessment
1. Are the patients described in detail so that you can decide whether they are comparable to those that you see in your practice?
2. Are the interventions and treatment settings described well enough so that you can provide the same for your patients?
3. Were all clinically relevant outcomes measured and reported?
4. Is the size of the effect clinically important?
5. Are the likely treatment benefits worth the potential harms?
Last assessed as up-to-date: 1 April 2013.
Protocol first published: Issue 4, 2004
Review first published: Issue 3, 2007
Contributions of authors
S Atlas contributed to study selection, reviewed and edited the protocol and review.
LE Chaparro contributed to study selection, risk of bias assessment, data extraction, data analysis and drafting of the review.
A Deshpande contributed to study selection, risk of bias assessment, data extraction, data analysis and drafted both the protocol and review.
A Furlan - contributed to study selection, risk of bias assessment, data extraction, data analysis, assisted with writing and editing the protocol and review.
A Mailis-Gagnon reviewed and edited the protocol and review.
D Turk reviewed and edited the protocol and review.
Declarations of interest
Sources of support
- Canadian Institutes for Health Research, Canada.Andrea Furlan received a New Investigator Award from CiHR (2012-2017)
- No sources of support supplied
Medical Subject Headings (MeSH)
Analgesics, Opioid [adverse effects; *therapeutic use]; Anti-Inflammatory Agents, Non-Steroidal [therapeutic use]; Chronic Pain [*drug therapy]; Low Back Pain [*drug therapy]; Randomized Controlled Trials as Topic
MeSH check words
Adult; Female; Humans; Male; Middle Aged