The efficacy of traction for back and neck pain: a systemic, blinded review of randomized clinical trial methods.

Back pain and neck pain are common in western industrialized countries. Approximately 80% of all people will have one or more episodes of back pain in the course of their lives, and about 50% will have one or more episodes of neck pain. [1-3] The majority of all episodes of back and neck pain disappear within a few months, often with the help of rest, analgesics, and home exercises.[4] Only in about 5% of all cases do back and neck pain last for more than 3 months. [1] The recurrence rate of back and neck pain is high; approximately 60% of all episodes are followed by a relapse. [2,3] Little is known about the relevant prognostic features of back and neck pain. Prognoses seem to worsen with the occurrence of radiating pain and with increasing number of relapses. [5-11] Although back and neck pain are the most frequent disorders of the musculoskeletal system in general practice, there is no consensus about the management of these conditions. The efficacy of primary care treatment (including physical therapy) for back and neck pain remains questionable. [1,4,9-17] General practitioners in the Netherlands often refer patients with back and neck pain for physical therapy. The majority of these patients complain of persistent pain. [18] In these cases, traction is one of the possible treatment modalities. In the Netherlands, patients receive traction treatment in approximately 7% of the annual 21 million physical therapy sessions, often in combination with other treatments. [18-20] Doubt exists, however, whether traction is a beneficial treatment modality for back and neck pain. [4]

Lumbar traction is applied with a harness (with self-adhesive strapping) that is put around the lower rib cage and the iliac crest. A head halter sling is used for cervical traction. The duration and level of exerted traction can be varied in a continuous or intermittent mode. [21-24] Of the different traction techniques, manual traction (ie, traction exerted by the therapist, using the patient's head, arms, or legs) and motorized traction (ie, traction exerted by a motorized pulley) are most often used, whereas inverted suspension (ie, traction exerted by gravitational forces, through the body weight of the patient) and bed-rest traction (ie, traction is exerted by a pulley and weights) are only occasionally used.

During application of traction, muscle tension, skin stretch, and intra-abdominal pressure should be taken into account as counterforces. Friction between the body and the support surface is the main counterforce during application of traction on a table or in bed. This friction can be reduced by using a split tabletop with ball bearings and by altering the angle of pull. [25,26]

The rationale for traction is based on mechanical and reflex mechanisms. [21-24] Spinal elongation through an increase of intervertebral space and relaxation of spinal muscles is assumed to be the most important of the proposed mechanisms by which traction could be effective. [27-31] Because spinal elongation as the proposed specific effect is not expected to occur below a traction force of 25% of the total body weight, [26,32,33] a traction force below this weight is sometimes denoted as a sham treatment or placebo. The proposed mechanisms of traction, however, have not been supported by sufficient research. Furthermore, it is not very likely that an annular tear would disappear through traction, or that a protruded or prolapsed nucleus of an intervertebral disk could be reduced and stabilized within the annulus by spinal elongation. [29,33] To date, there is little clarity about the mechanism by which traction could be effective.

No systematic research has been performed into the adverse effects of traction. [34] Some case reports [22,35] suggest that there is some danger of adverse effects in heavy traction (eg, lumbar traction with forces exceeding 50% of the total body weight) or in cervical traction with forces exceeding 50% of the weight of the head (ie, approximately 4% of the total body weight). It has been theorized that traction in cases of medial or distal protrusion of the nerve root might increase nerve impingement. [36] Other risks described for traction concern increased blood pressure and respiratory constraints due to traction harness, and temporomandibular joint strain due to the head sling. [21,35,37-42]

The question addressed in this review is whether different traction modalities for back and neck pain have been shown to be clinically effective through published research (ie, have a causal relation with clinical improvement). Randomized clinical trials (RCTs) are considered to be the best design for control of validity (ie, absence of systematic error) and precision (ie, absence of random error).

We present a critical review of the available RCTs about the effectiveness of traction for back and neck pain. Although RCTs potentially provide the most valid and precise results, flaws in their design and conduct can result in overestimation or underestimation of treatment effects, and consequently can lead to false-positive or false-negative conclusions. Therefore, we will place strong emphasis on the quality of the methods of the studies selected for review.

Method

We traced relevant study reports by means of a MEDLINE literature search (1966-1992, using the following Medical Subject Headings terms or free-text words: traction, therapeutic use, not fractures, musculoskeletal diseases, joint diseases, spinal diseases, neck, backache, cervical, adverse effects, comparative studies, evaluation studies, outcome and process assessment, physical therapy, epidemiology, statistics, science), as well as an EMBASE literature search (1974-1992, using the following key words: physiotherapy, traction, not fractures, musculoskeletal diseases, joint diseases, spinal diseases, neck, back, major clinical studies, placebo, randomization, double-blind procedure, review). In addition, a number of relevant journals not indexed in these two databases were screened, as well as the Index to Chiropractic Literature (1980-1992) and the Physiotherapy Index (1986-1992). To be included in the review, a study had to meet the following criteria: (1) A random procedure was used for treatment allocation, (2) included patients had back or neck pain, (3) one of the treatment regimens had to include a traction technique (additional care was allowed), (4) clinically relevant outcome measures were used (eg, global estimate of improvement, pain, mobility, functional status), and (5) results were published before june 1992. Abstracts, unpublished studies, and studies with alternate treatment allocation were excluded.

The quality of design and conduct of the selected studies were assessed according to generally accepted methodological principles of intervention research. [43-45] These methodological principles are grouped into four categories: (1) study population, (2) interventions, (3) measurement of effect, and (4) data presentation. These four categories comprise 16 criteria (Tab. 1, A-P), which have been further divided to create a 49-item checklist. Every checklist item is given a certain weight that relates to its possible contribution to validity and precision. A study can earn a maximum methodology score of 100 points. Similar lists have been used in reviews about the efficacy of various interventions. [12,13,16,46-48] For this blinded review, we adapted the items relating to clinical relevance to back and neck pain and traction (criteria A, B, G, and L). The methodological principles are briefly explained here in the order they are presented in Table 1. [TABULAR DATA 1 OMITTED]

Study Population

A prognostic homogeneous study population can be recruited if trial participation is restricted to a subgroup of patients with identical treatment susceptibility and prognoses. Randomization is used to exclude patients' treatment preferences, and therapists must be excluded during allocation of the interventions compared. In addition, randomization scatters confounders (ie, known and unknown determinants for prognosis and treatment susceptibility) over the groups, thereby creating prognostically comparable groups.

When prognostic subgroups can be specified, stratified randomization can further improve the prognostic comparability of groups. Restriction, stratification, and randomization, however, do not guarantee prognostically comparable groups in the case of small studies. Therefore, large studies in general provide more valid and more precise results than smaller studies.

Refusal to participate after enrollment, or attrition either during the treatment phase (dropouts) or at follow-up (loss to follow-up), can be due to a variety of causes. Validity, however, is only threatened when attrition is related to prognostic incomparability or to the success or failure of allocated interventions. Therefore, details about attrition rates are essential for evaluation of trial results.

Interventions

The contrast between interventions can be ascertained if the proposed specific treatment components of the interventions within groups can be standardized. The validity of this contrast is further improved if nonspecific treatment components (eg, attention and bedside manners), additional care, and cointerventions can be standardized for all patients. In addition, group differences in compliance can also obfuscate the intervention contrast.

Measurement of Effect

Treatment preferences of patient, therapist, and outcome assessor can give rise to biased effect measurement. Blinding for the nature of assigned interventions, therefore, is needed for unbiased outcome measurement. In explanatory trials, in which specific effects of interventions or their components are studied by comparison with a placebo, the blinding of patients and therapists is often done via use of a placebo. Because blinding can be jeopardized, therefore, ascertainment of blinding should be evaluated and reported. In management studies, in which two or more usual treatment modalities are compared, the blinding of patients and therapists is difficult to achieve. in such studies, blinding can be ensured, in part, by selection of patients who have no previous experience with the interventions. Furthermore, the participation of a blinded observer, coupled with the exclusion of the influence of the patients' opinion, is needed for the unbiased evaluation of treatment effects in management studies.

Data Presentation

Flaws in the design and conduct of a study can give rise to biased results that will lead to underestimation or overestimation of the effects of the compared interventions. Consequently, the results, whether statistically significant or not, will lead to false-positive or false-negative conclusions. Therefore, methodological shortcomings (eg, prognostic incomparability of groups, partial blinding or absence of blinding, poor compliance, the number of dropouts and loss to follow-up) must be reported, preferably for each group. Sometimes these methodological shortcomings can be corrected during data analysis.

The selected reports were blinded for author(s), journal, and results by the first author (GJMGH). The methodological quality of the reported studies was assessed, via the checklist, by two of the authors (BWK, WJJA). in a subsequent meeting, these two authors (still blinded) reached consensus on every checklist item they disagreed about. The assessment resulted in a methodological score for each study. This process enabled us to make a hierarchical list on the basis of methodological quality. We labeled the outcome of a study "positive" if the authors of the report concluded that there was a difference in effect between the compared treatments in favor of at least one of the traction modalities applied. The outcome of a study was labeled "negative" if the authors of the report concluded that there was no difference between the compared treatments, or that there was a difference in effect in favor of one or more reference treatments.

Results

We found 21 papers, [49-69] reporting 24 studies, that met the four conditions for inclusion in the blinded review. Three studies about the efficacy of lumbar traction [49-51] were excluded from the blinded review because the patients receiving the traction regimen could not be identified. in addition, comparison of the reports revealed that some studies [52-57] were reported in more than one article. Table 2 presents 17 RCTs (3 on cervical traction and 14 on lumbar traction) in hierarchical order based on their methodological scores.

Initially, the two blinded reviewers agreed on more than 80% of all checklist items. After a consensus meeting (still blinded), there was agreement in all instances. The discrepant scores were found mainly to be due to reading errors. Of the studies reported in more than one article, the reports with the lower scores did not reveal additional or different information.

Table 2 shows the wide range in method scores (range=23-68). Only 3 RCTs (2 lumbar traction, 1 cervical traction) scored more than 50 points. These 3 RCTs showed no favorable effects of traction on pain, mobility, functional status, or other symptoms and complaints. Among the remaining 14 studies, only 4 showed positive results according to the authors of the reports (3 lumbar traction, [60-62] 1 cervical traction[63]). In total, only 5 RCTs (2 cervical traction, 3 lumbar traction) scored more than 40 points, indicating the poor overall methodological quality of most of the studies. [TABULAR DATA 2 OMITTED]

Common methodological flaws concerned incomparability of prognosis at baseline (criterion B), insufficient description of randomization procedure (criterion C), small sample size (criterion F), incomparability of cointerventions (criterion I), no attempts to blind patients (criterion K), and no attempts to blind outcome measurement or failure to include a blinded assessor (criterion M). Blinding of the therapists was not reported for any of the studies. Despite some incomplete information, the studies reported were methodologically sound with respect to restriction to a homogeneous population criterion A), little loss to follow-up (criterion E), sufficient description of traction modalities and reference intervention(s) (criteria G and H), and adequate data presented on the most important outcome measures (criterion P).

Recalculation of the weighted and unweighted method scores for the 16 criteria (A-P) and the 49 checklist items provides a sensitivity analysis of the checklist and the distribution of weights. The results of these recalculations (Tab. 3) revealed only minor differences in the hierarchical order of the studies, and the three best studies and the four worst studies remained so. In between, the sequence varied little. These recalculations show the robustness of the scoring system. [TABULAR DATA 3 OMITTED]

Table 4 presents a description of the details of the three RCTs [59,63,64] that compared cervical traction techniques with different control treatments. The method score of one study [59] exceeded 50 points, and one study [63] showed positive results according to the authors of the report. information about the standardization of traction treatment was incomplete for all three studies. Goldie and Landquist [59] excluded additional care in their study. The other two studies [63,64] used additional care, but only Zylbergold and Piper, [63] applied it in a standardized way for an patients. [TABULAR DATA 4 OMITTED]

Table 5 presents a concise description of the details of the seven RCTs [54,56,58,65-68] that compared lumbar traction techniques with placebo traction. Four of these studies [56,58,65-68] were concerned with continuous motorized traction, two studies [54,66] were concerned with autotraction, and one study [67] was concerned with continuous bed traction. Only one study [58] had a method score exceeding 50 points, and none showed positive results according to the authors of the reports. In three studies, [54,66,68] the information about the standardization of the traction treatment was incomplete. In two studies, [65,66] additional care was used, but only Reust et al [65] applied it in a standardized way for all patients. The remaining five studies excluded additional care. [TABULAR DATA 5 OMITTED]

Table 6 summarizes the details of the seven RCTs [52,54,57,60-62,69] that compared different lumbar traction techniques or lumbar traction with heat, corset, exercises, massage, and rest. Three of these studies [57,60,62] were concerned with autotraction, two studies [54,57] were concerned with manual traction, two studies [61,69] were concerned with intermittent motorized traction, and one study [52] dealt with continuous motorized traction. The method score of only one negative study [52] exceeded 50 points, whereas positive results were reported for three studies [60-62] with lower method scores. Information about the standardization of the traction treatment was incomplete in five studies. [52,54,57,62,69] [TABULAR DATA 6 OMITTED]

In Table 7, the studies are once again ordered by their method scores. For this table, we calculated the power (1-[Beta]) and the 90% confidence interval (90% CI) for the differences in success rates of the compared interventions of each study. When a 90% CI excludes zero, there is no significant difference with accepting a 10% chance of a Type I error (alpha=10%). [70] The power (1-[Beta]) was calculated for detecting a 30% difference with the reported success rates in the reference groups, because this was the difference in success rate of the study with the highest method score. Power indicates the chance of missing a true significant difference in success rates (ie, a Type II error) and is acceptable when it exceeds 80% ([Beta]=20%). [71] Apart from the assumed clinically relevant effect size (ie, 30%), power depends on the number of patients per group (sample size). Therefore, most of the comparisons shown in Table 7 lack power due to small sample sizes. [TABULAR DATA 7 OMITTED]

In one study, [61] the calculated 90% CI was negative and excluded zero; therefore, the published results favored the control treatment. In three studies that were concerned with lumbar traction [60,62,65] and in two studies that were concerned with cervical traction, [59,63] the 90% CI was positive and excluded zero. In only one of these studies [59] did the method score exceed 50 points. Our power calculations showed that this study also reached an acceptable power (1--[Beta] of >80%). Although two other studies with significant results [60,61] reached an acceptable power, their method scores did not exceed 50 points.

Discussion and Conclusions

Studies could only earn points if a report provided die necessary details that met with the methodological requirements. The standard of 100 points is probably not easy to reach in this area of intervention research, but it is disappointing to find that the methodological quality of the available RCTs on traction is so low. In some instances, a more informative report might have revealed additional flaws in the design or conduct of the studies included in this review.

Study Population

Biased treatment assignment could not be excluded for most studies because the reports provided insufficient information about how and by whom the randomization procedure was carried out. A statement about the "at random" division of subjects over intervention groups is no guarantee that all selected patients had the same chance to be assigned to any of the groups.

Although most studies proved methodologically sound with respect to prognostic homogeneity of the selected population, they hardly included a sufficient number of patients (sample size). Prognostic comparability of groups after randomization was impeded by these small sample sizes. In addition, few authors reported adequate information about dropouts and loss to follow-up.

Intervention

Because forces exerted during inverted suspension and manual traction are limited by total body weight and the strength of the patient or therapist, these modalities cannot necessarily be standardized. In contrast, forces exerted during motorized traction and bed-rest traction can be standardized. Occasionally, however, traction modalities and control intervention(s) seemed sufficiently standardized. Additional care and cointerventions were not standardized or poorly standardized. Compliance was only reported occasionally and therefore, in the case of unequal distribution, may have affected the intended intervention contrast.

The 90% CI (Tab. 7) of a comparison of cervical traction with no treatment excluded zero, and its power was sufficient. [59] The method score of this study was 51 points. In situations, however, in which a desired treatment is withheld from the control group, expectation bias and disappointment of patients will easily lead to an over-estimation of the effect of traction, and thus to false-positive conclusions. Remarkably, the confidence interval of another study [63] with the same flaw also excluded zero (ie, was statistically significant). A credible placebo can prevent this type of bias. In de context, it is remarkable that the confidence intervals of the studies that used sham traction as the control treatment always included zero (ie, were not statistically significant).

Measurement of Effect

In the selected trials, hardly any attempts at blinding patients, therapists, and outcome measurements were reported. Only occasionally were long-term effects reported.

Little is known about valid and precise outcome measures that are also sensitive for clinically important changes. In addition, because the relevance of outcome measures is mainly determined by the research question, it is not possible to define in general which outcome measures are relevant. Nevertheless, in day-to-day practice, clinically relevant outcome measures, such as a global measure of improvement, pain, spinal mobility, or functional status, are preferred. That is because they correspond with complaints most often heard as reasons for encounter or referral. Only a few authors, however, reported on more than two of these clinically relevant outcome measures.

Data Presentation

The aim of treatment is a desired treatment outcome that concerns an expected minimal effect size at relevant moments of measurement for predetermined relevant outcome measures. Before mounting an RCT, this desired treatment outcome is also important for calculation of the sample size. None of the authors in our review, however, reported a desired treatment outcome, or the anticipated sample size. For our calculations of 900% CI and power, we used a 300% improvement in the global estimation of the patient or clinician as a relevant outcome measure. We propose it as a clinically relevant measure that is easy to apply in clinical trials and in day-today practice. Although confidence intervals and power were only reported occasionally, the presentation of results was sufficient. However, an alternative analysis accounting for shortcomings that occurred was never reported.

The criteria we used to assess the available RCTs are based on generally accepted requirements for high methodological quality in intervention research. We do not pretend that our methodological checklist is exhaustive. Because the data in Table 2 show that criteria B (prognostic comparability), D (dropouts described), F (study size), L (relevant outcome measures), M (binding of outcome measurement), and P (data presentation) contribute most to the disriminative character of the checklist, we believe that our rating system can be used to distinguish methodologically sound studies from those that are not. [TABULAR DATA 2 OMITTED]

We did not pool the results of the studies statistically for two reasons: (1) All studies used different protocols for selection, intervention, and effect measurements; and (2) we prefer not to pool data from studies with high and low methodological quality.

Possible disagreement among independent readers might give rise to conflicting conclusions. This disagreement can be reduced by standardization of the scoring system. Our conclusions are based on methods scoring by two independent assessors with our 49-item checklist. Concordance of their scores was high, and differences were mainly based on reading errors. Blinding of both assessors for results, conclusions, and journal identification was used to prevent occurrence of reviewer bias. In addition, both assessors were not involved in the design or conduct of any of the selected studies.

The weights given to the criteria were chosen arbitrarily, but were assumed to reflect their relative importance for validity and precision. Readers may wish to assign different weights and calculate their own method scores. The sensitivity analysis, however, confirmed the robustness of the methodological scoring system. This analysis revealed that the hierarchical order was not severely affected by discarding weighting factors or by the use of either the 49 checklist items or the 16 criteria. In addition, Shekelle et al[72] validated our rating system in a meta-analysis of spinal manipulation. Their study yielded similar results when our scoring system was compared with that of Chalmers et al. [73]

In meta-analysis, publication bias never can be ruled out completely because relevant studies could have been missed. Its occurrence in studies such as this leads to false-positive conclusions. Publication bias, however, mainly exists for articles that are difficult to publish, because they report trials with small sample sizes and negative results. [74] Because the selected articles mainly report on studies with small samples, the occurrence of publication bias in this research area is not very likely.

Due to the poor methodological quality of the studies we reviewed, it is not possible to formulate a strong and valid judgment about either lumbar traction or cervical traction. So far, there has been no clear-cut information about the mechanism nor evidence for any specific effect of cervical and lumbar traction. There is no conclusive evidence, however, that traction is an ineffective therapy for back and neck pain. In view of the results of this review, it seems advisable to perform new RCTs that focus on the modalities from the three best studies (ie, intermittent motorized cervical traction and continuous motorized lumbar traction). Future studies should avoid the methodological flaws presented, and more attention should be given to the proper execution of the RCTs, as well as to the clear description of the crucial features of their design and results.

In addition, in RCTs priority should be given to the specific effect of traction, that is, comparison of these modalities with a traction placebo (sham or low-dosage traction). To warrant validity in such explanatory studies, the development of a credible traction placebo is very important. When in this respect information for the compared groups differs (eg, during traction, a tolerable but distinct force from the harness must be felt, whereas during a traction placebo, very little pulling from the harness must be felt), the persuasiveness of physical therapists will be crucial.

The available RCTs do not allow conclusions about the effectiveness of cervical or lumbar traction. Therefore, intervention studies do not support the common practical recommendations or clinical guidelines about traction that are mainly based on the rationale of spinal elongation.

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GJMG van der Heijden, PT, is Research Fellow, Department of Epidemiology, University of Limburg, PO Box 616, 6200 MD Maastricht, the Netherlands. Address all correspondence to Mr van der Heijden.

AJHM Beurskens, is Research Fellow, Department of Epidemiology, University of Limburg.

BW Koes, PhD, is Research Fellow, Institute for Research in Extramural Medicine, Vrije Universiteit, Amsterdam, the Netherlands.

WJJ Assendelft, MD, is Research Fellow, Institute for Research in Extramural Medicine, Vrije Universiteit.

HCW de Vet, PhD, is Assistent Professor, Department of Epidemiology, University of Limburg.

LM Bouter, is Professor of Epidemiology, Institute for Research in Extramural Medicine, Vrije Universiteit.