A critical look at the British randomised clinical trial;
Meade TW, Dyer S et al 1990. Low Back Pain of Mechanical Origin. Randomised Comparison of Chiropractic and Hospital Outpatient Treatment, BMJ 300: 1431-37;
and the follow up study:
Meade T W, Dyer S et al 1995. Randomised Comparison of Chiropractic and Hospital Outpatients Management for Low Back Pain Results from Extended Follow Up, BMJ 311: 349-351.
This page was last updated on 7th November 2010.
The General Chiropractic Council has often cited the Meade Report(s) (and the 2004 UK BEAM Trial) in support of its claim that "the main treatments of chiropractic have been shown consistently in reviews to be more effective than the treatments to which they have been compared". However, it is generally well recognised that the Meade study of chiropractic is seriously flawed in comparing two very different settings with greatly differing non-specific effects, i.e., private chiropractic clinics and health service hospital outpatients. [pdf]
For critical comment on the BEAM Trial, and others - including the 2009 NICE guidelines on low back pain - see further down this page.
"People familiar with clinical tests of spinal manipulative therapy (SMT) for back pain were puzzled by the outcome of the British study by Meade, et al, (Brit Med J, 300:1431-37, 1990) which found chiropractic care to be more effective in the long term than hospital management (for chronic back pain sufferers only). Studies designed to test SMT against other modalities have consistently found that although SMT may produce more rapid relief there are no differences over the long term (for a review see Clinical Orthopaedics & Related Research, 179:62-70, 1983).
The Meade study did not test SMT against other modalities but merely compared hospital with chiropractic care in which a flock of modalities were employed. It did not even equalize the number of treatment sessions nor length of time under care. The most likely answer to this anomalous finding lies in patient satisfaction.
The Ostwestry Disability Questionnaire employed by Meade is a 10-item patient self-report on the relief of symptoms during specified activities. Although the test has high reliability (.99), this matter involves its validity. Cherkin reports "there is mounting evidence that patient satisfaction is associated with desirable outcomes including self-assessed relief of symptoms" (Chiropractic Technique, 2:138-142, 1990). Parker & Tupling (Med J Aust, 2:373-376, 1976) also reported: "satisfaction at follow-up was associated with reported improvement in the condition, greater approval of chiropractic treatment, and less reporting of pain at follow-up." DCs generally score better than MDs on patient satisfaction because of such factors as:
"making the patient feel welcome"
"ability to explain problem & treatment"(1)
"amount of time spent listening to my description of pain"
"seemed to believe that my pain was real"
"seemed confident that the diagnosis s/he gave was correct"
"seemed confident that the treatment s/he recommended would work"
"seemed comfortable dealing with my back pain"
"concern about my pain after the office visit" (2)
The explanation that patient satisfaction rather than real differences was responsible for better long term Ostwestry scores is supported by the fact that a significantly greater portion of chiropractic patients reported being "satisfied or very satisfied" in the Meade Study."
National Council Against Health Fraud News, Volume 14, Issue1 (Jan/Feb 1991) [Citations: (1.) Lancet, 1974, June, 29, 1333-36. (2.) West J Med, 150:351-355, 1989]
Effectiveness of chiropractic and physiotherapy in the treatment of low back pain: a critical discussion of the British Randomized Clinical Trial
"This article discusses the methodology of a recently published British randomized clinical trial comparing chiropractic and physiotherapy as treatments for low back pain.
The authors base their main conclusions on a difference shown by the Oswestry pain questionnaire 2 yr after randomization, when data of only 26% of the patients were available. This might have led to an overestimation, because it appears that the difference in Oswestry scores is much larger for patients included early in the study. It may also be doubted whether the magnitude of the effect reported really indicates a clinically significant difference between the interventions.
In addition to allocated intervention, the groups also differ in duration of treatment, number of sessions, level of experience of the therapist, and health care setting.
The results are difficult to extrapolate, because only a small portion of the eligible patients participated, and chiropractic seems to be clearly superior only in the subgroup originally presenting to a chiropractic clinic.
We conclude that it is premature to draw conclusions about the long-term effectiveness of chiropractic based on the results of this study alone."
Assendelft WJ, Bouter LM, Kessels AG., Department of Epidemiology/Health Care Research, University of Limburg, Maastricht, The Netherlands. ( J Manipulative Physiol Ther. 1991 Jun;14(5):281-6)
"EDITOR,--T W Meade and colleagues have provided further data from their study comparing chiropractic with hospital physiotherapy.1 Unfortunately, their report is far from convincing. The "headline" advantage of chiropractic over hospital management at three years (29%) sounds impressive but refers to an improvement of three points on the 100 point Oswestry scale, or one and a half responses on the questionnaire. This difference may be statistically significant but is clinically trivial.
In their original article the authors noted that chiropractic was 50% more expensive,2 and in the latest report they note that the chiropractic group had more treatments in the long term. The measured improvement does not seem to support such an expenditure.
The design of the study was criticised after the first paper was published.3 The patients initially presenting to a chiropractor were self selected on the basis that they believed that chiropractic would be effective (as they were expecting to pay for treatment).
It is interesting that only the patients referred by chiropractors showed a significant advantage for chiropractic. Those initially recruited in hospital practice showed no significant difference. The study compares private practice with NHS treatment with all the implications for environmental and personal factors that this brings.
The follow up rate (70% and 77%) is inadequate and would preclude publication in some journals.4 Analysis by intention to treat does not obviate this deficiency.
Important variables such as psychological disturbance are not addressed although these are noted to have a greater impact on results than does treatment.5
It is disappointing that in the five years between the reports these and the other criticisms that were raised were not more fully addressed. Despite the acclamation of the first report in the popular media I do not think that this study has advanced our understanding of the treatment of back pain in any useful way."
Letter to the British Medical Journal (1995)
“If we look at the paper, Meade et al., 1990 … several things jump out. First, the Oswestry disability index scale runs for 0 to 100, but scores are plotted only from 0 to 35, so the size of the effects are exaggerated. Second, there are no error bars on the points. Third there is essentially no advantage for chiropractic at all when all patients are taken together (top graph). Fourth, and most important, the patients who were followed up for two years (bottom graph) seem to show a slight advantage for chiropractic but on average, the effect is 7 percent (on the 100 point scale), NOT 70 percent as claimed on the web site of Peter Dixon Associates.
What sort of mistake was made?
The abstract of the paper itself says “A benefit of about 7% points on the Oswestry scale was seen at two years.” How did this become “improved by 70% more”?
It could have been simple a typographical error, but than seems unlikely. Who’d boast about a 7% improvement?
Perhaps it is a question of relative versus absolute change. The Figure does not show the actual scores on the 100 point scale, but rather the change in score, relative to a questionnaire given just before starting treatment. If we look at the lower part of the Figure, restricted to those patients who stayed with the trail for 2 years (by this time 28% of the patients had dropped out), we see that there is a reduction in score (improvement) of about 10 points on the 100 point scale with hospital treatment (not a very impressive response). The improvement with those sent to private chiropractic clinics was about seven points bigger. So a change from 10 to 17 is a 70 percent change. What’s wrong with that?
What’s wrong is that it is highly misleading, as relative changes often are. Imagine that the hospital number had been 7 points and the chiropractic number had been 14 (both out of 100). That would mean that both treatments had provided very modest benefits to the patients. Would it then be fair to describe the chiropractic patients as have improved by 100 percent more than the hospital patients, when in fact neither got much benefit? Of course it would not. To present the results in this way would be highly deceptive.
Put another way, a 70% increase in a trivial effect is still pretty trivial.
That isn’t all either. The paper has been analysed in some detail on the ebm-first site. The seven point difference on a 100 point scale, though it may be real, is too small to be ‘clinically significant’ In other words the patient would scarcely notice such a small change. Another problem lies in the nature of the comparison. Patients were, quite properly, allocated at random to chiropractic or to hospital treatment. BUT the comparison was very from blind. one group was treated in hospital. The other group was sent to private chiropractic clinics. The trivial 7 point difference could easily be as much to do with the thickness of the carpets rather than any effect of spinal manipulation.
What this paper really tells you is that neither treatment is very effective and that there is little to choose between them.
It is really most unfortunate that the chairman of the GCC should show himself to be so careless about evidence at a time when the evidence for the claims of chiropractors is under inspection as never before. It does not add to their case for criticising Simon Singh and it does not add to one’s confidence in the judgement of the NICE guidance group.”
Article by Professor David Colquhoun, DC Science website. (12th June 2009)
NOTE:The General Chiropractic Council's website implies that the European Guidelines for the Management of Low Back Pain recommend chiropractic for the management of back pain. However, only a brief mention is made for spinal manipulation and not 'chiropractic'.
"Three brief comments on the excellent BEAM Trial.
My reading of the results is that the data are compatible with a non-specific effect caused by touch: exercise has a significantly positive effect on back pain which can be enhanced by touch. If this "devil's advocate" view is correct, the effects have little to do with spinal manipulation per se.
It would be relevant to know which of the three professional groups (chiropractors, osteopaths, physiotherapists) generated the largest effect size. This might significantly influence the referral pattern. A post-hoc analysis might answer this question.
It is regrettable that the study only monitored serious adverse effects. There is compelling data to demonstrate that minor adverse effects occur in about 50% of patients after spinal manipulation. If that is the case, such adverse events might also influence GP's referrals."
Professor Edzard Ernst, Director, Complementary Medicine, Peninsula Medical School, Exeter, UK. (British Medical Journal, 6th December 2004) [Full text available via free registration]
Spinal manipulation for the early management of persistent non-specific low back pain — a critique of the recent NICE guidelines
"The guidelines considered 'a total of seven RCTs on manipulation/mobilisation techniques' for evaluating effectiveness. A Cochrane review included 39 RCTs. The methods section of the guidelines informs us that 'articles not relevant to the subject in question were excluded'. It is unclear to me why so many RCTs of spinal manipulation were excluded from the NICE guidelines…
Perhaps more crucially, the risks were under-estimated. The risk of mild to moderate adverse effects is undisputed even by chiropractors: about 50% (!) of all patients suffer from such adverse effect after spinal manipulations (10). These effects (mostly local or referred pain) are usually gone after 1–2 days but, considering the very moderate benefit, they might already be enough to tilt the risk-benefit balance in the wrong direction. In addition, several hundred (I estimate 700) cases are on record of dramatic complications after spinal manipulation. Most frequently they are because of vertebral arterial dissection (5). Considering these adverse events, the risk-benefit balance would almost certainly fail to be positive. It is true, however, that the evidence as to a causal relationship is not entirely uniform. Yet applying the cautionary principle, one ought to err on the safe side and view these complications at least as possibly caused by spinal manipulations.
So why were these risks not considered more seriously? The guideline gives the following reason: ‘The review focussed on evidence relevant to the treatment of low back pain, hence cervical manipulation was outside our inclusion criteria’. It is true that serious complications occur mostly (not exclusively) after upper spinal manipulation. So the guideline authors felt that they could be excluded. This assumes that a patient with lower back pain will not receive manipulations of the upper spine. This is clearly not always the case.
Chiropractors view the spine as an entity. Where they diagnose ‘subluxations’, they will normally manipulate and ‘adjust’ them (11). And ‘subluxations’ will be diagnosed in the upper spine, even if the patient suffers from back pain. Thus many, if not most back pain patients receive upper spinal manipulations. It follows that the risks of this treatment should be included in any adequate risk assessment of spinal manipulation for back pain.
The guidelines have a number of serious flaws. I contend that they over-estimated the effectiveness of spinal manipulation and under-estimated the risks of this treatment. If evaluated on the basis of the best current evidence by applying the cautionary principle, one will arrive at the following conclusion: it is uncertain whether spinal manipulation generates more benefit than harm for patients suffering from back pain."
Edzard Ernst, Int J Clin Pract (18th August 2009) [No abstract or full text — reprints available from author]