MD, PhD, FMedSci, FRSB, FRCP, FRCPEd

osteoarthritis

Twenty years ago, I published a short article in the British Journal of Rheumatology. Its title was ALTERNATIVE MEDICINE, THE BABY AND THE BATH WATER. Reading it again today – especially in the light of the recent debate (with over 700 comments) on acupuncture – indicates to me that very little has since changed in the discussions about alternative medicine (AM). Does that mean we are going around in circles? Here is the (slightly abbreviated) article from 1995 for you to judge for yourself:

“Proponents of alternative medicine (AM) criticize the attempt of conducting RCTs because they view this is in analogy to ‘throwing out the baby with the bath water’. The argument usually goes as follows: the growing popularity of AM shows that individuals like it and, in some way, they benefit through using it. Therefore it is best to let them have it regardless of its objective effectiveness. Attempts to prove or disprove effectiveness may even be counterproductive. Should RCTs prove that a given intervention is not superior to a placebo, one might stop using it. This, in turn, would be to the disadvantage of the patient who, previous to rigorous research, has unquestionably been helped by the very remedy. Similar criticism merely states that AM is ‘so different, so subjective, so sensitive that it cannot be investigated in the same way as mainstream medicine’. Others see reasons to change the scientific (‘reductionist’) research paradigm into a broad ‘philosophical’ approach. Yet others reject the RCTs because they think that ‘this method assumes that every person has the same problems and there are similar causative factors’.

The example of acupuncture as a (popular) treatment for osteoarthritis, demonstrates the validity of such arguments and counter-arguments. A search of the world literature identified only two RCTs on the subject. When acupuncture was tested against no treatment, the experimental group of osteoarthritis sufferers reported a 23% decrease of pain, while the controls suffered a 12% increase. On the basis of this result, it might seem highly unethical to withhold acupuncture from pain-stricken patients—’if a patient feels better for whatever reason and there are no toxic side effects, then the patient should have the right to get help’.

But what about the placebo effect? It is notoriously difficult to find a placebo indistinguishable to acupuncture which would allow patient-blinded studies. Needling non-acupuncture points may be as close as one can get to an acceptable placebo. When patients with osteoarthritis were randomized into receiving either ‘real acupuncture or this type of sham acupuncture both sub-groups showed the same pain relief.

These findings (similar results have been published for other AMs) are compatible only with two explanations. Firstly acupuncture might be a powerful placebo. If this were true, we need to establish how safe acupuncture is (clearly it is not without potential harm); if the risk/benefit ratio is favourable and no specific, effective form of therapy exists one might still consider employing this form as a ‘placebo therapy’ for easing the pain of osteoarthritis sufferers. One would also feel motivated to research this powerful placebo and identify its characteristics or modalities with the aim of using the knowledge thus generated to help future patients.

Secondly, it could be the needling, regardless of acupuncture points and philosophy, that decreases pain. If this were true, we could henceforward use needling for pain relief—no special training in or equipment for acupuncture would be required, and costs would therefore be markedly reduced. In addition, this knowledge would lead us to further our understanding of basic mechanisms of pain reduction which, one day, might evolve into more effective analgesia. In any case the published research data, confusing as they often are, do not call for a change of paradigm; they only require more RCTs to solve the unanswered problems.

Conducting rigorous research is therefore by no means likely to ‘throw out the baby with the bath water’. The concept that such research could harm the patient is wrong and anti-scientific. To follow its implications would mean neglecting the ‘baby in the bath water’ until it suffers serious damage. To conduct proper research means attending the ‘baby’ and making sure that it is safe and well.

Highly diluted homeopathic remedies are pure placebos; at least this is what sceptics have been saying for about 200 years. This assumption is based on the fact that homeopathy’s plausibility is close to zero and that the totality of the reliable evidence fails to demonstrate that it works beyond placebo for any condition.

But, if this is true,  why do so many patients swear by homeopathy and experience benefit from it? This question has been answered many times: THE BENEFIT IS NOT DUE TO THE REMEDY BUT TO NON-SPECIFIC EFFECTS OF THE CONSULTATION.

More confirmation for this conclusion comes from an unexpected source.

Indian homeopaths recently published a trial of individualized homeopathy in osteoarthritis. To be more precise, it was a prospective, parallel-arm, double-blind, randomized, placebo-controlled pilot study which was conducted from January to October 2014 involving 60 patients (homeopathy, n = 30; placebo, n = 30). All patients were suffering from acute painful episodes of knee osteoarthritis and visiting the outpatient clinic of Mahesh Bhattacharyya Homeopathic Medical College and Hospital, West Bengal, India.

The results show statistically significant reduction in 3 visual analogue scales (measuring pain, stiffness, and loss of function) and Osteoarthritis Research Society International scores in both groups over 2 weeks (P < .05). However, group differences were not significant (P > .05).

The authors conclude that, overall, homeopathy did not appear to be superior to placebo; still, further rigorous evaluation in this design involving a larger sample size seems feasible in future.

Considering what I wrote above, I would alter these conclusion to something much more reasonable: further studies of homeopathy are certainly feasible. However, they are neither necessary nor desirable.

TO PUT IT DIFFERENTLY: HOMEOPATHY BELONGS IN THE BOOKS OF MEDICAL HISTORY.

An international team of researchers wanted to determine the efficacy of laser and needle acupuncture for chronic knee pain. They conducted a Zelen-design clinical trial (randomization occurred before informed consent), in Victoria, Australia (February 2010-December 2012). Community volunteers (282 patients aged ≥50 years with chronic knee pain) were treated by family physician acupuncturists.

The treatments consisted of A) no acupuncture (control group, n = 71), B) needle (n = 70), C) laser (n = 71), and D) sham laser (n = 70) acupuncture. Treatments were delivered for 12 weeks. Participants and acupuncturists were blinded to laser and sham laser acupuncture. Control participants were unaware of the trial.

Primary outcomes were average knee pain (numeric rating scale, 0 [no pain] to 10 [worst pain possible]; minimal clinically important difference [MCID], 1.8 units) and physical function (Western Ontario and McMaster Universities Osteoarthritis Index, 0 [no difficulty] to 68 [extreme difficulty]; MCID, 6 units) at 12 weeks. Secondary outcomes included other pain and function measures, quality of life, global change, and 1-year follow-up. Analyses were by intention-to-treat using multiple imputation for missing outcome data.

At 12 weeks and 1 year, 26 (9%) and 50 (18%) participants were lost to follow-up, respectively. Analyses showed neither needle nor laser acupuncture significantly improved pain (mean difference; -0.4 units; 95% CI, -1.2 to 0.4, and -0.1; 95% CI, -0.9 to 0.7, respectively) or function (-1.7; 95% CI, -6.1 to 2.6, and 0.5; 95% CI, -3.4 to 4.4, respectively) compared with sham at 12 weeks. Compared with control, needle and laser acupuncture resulted in modest improvements in pain (-1.1; 95% CI, -1.8 to -0.4, and -0.8; 95% CI, -1.5 to -0.1, respectively) at 12 weeks, but not at 1 year. Needle acupuncture resulted in modest improvement in function compared with control at 12 weeks (-3.9; 95% CI, -7.7 to -0.2) but was not significantly different from sham (-1.7; 95% CI, -6.1 to 2.6) and was not maintained at 1 year. There were no differences for most secondary outcomes and no serious adverse events.

The authors drew the following conclusions: In patients older than 50 years with moderate or severe chronic knee pain, neither laser nor needle acupuncture conferred benefit over sham for pain or function. Our findings do not support acupuncture for these patients.

This is one of the methodologically best acupuncture studies that I have seen so far.

  • its protocol has been published when the trial started thus allowing maximum transparency
  • it is adequately powered
  • it has a very clever study-design
  • it minimizes bias in all sorts of ways
  • it tests acupuncture for a condition that it is widely used for
  • it even manages to blind acupuncturists by using one treatment arm with laser acupuncture

The results show quite clearly that acupuncture does have mild effects on pain and function that entirely rely on a placebo response.

Will acupuncturists learn from this study and henceforward stop treating knee-patients? Somehow I doubt it! The much more likely scenario is that they will claim the trial was, for this or that reason, not valid. Acupuncture, like most of alternative medicine, seems unable to revise its dogma.

I find it always nice to see that people appreciate my work. Yet sometimes I am a little surprised to realise what some commercially interested firms make of it. Recently I came across a website that proudly used my research for advertising the use of magnetic bracelets against pain. Here is the text in question:

The extra strong magnets make this magnetic bracelet the fastest acting pain reliever. While wearing this magnetic bracelet customers with wrist and hand pain report significant pain relief….

What is a magnetic bracelet and what are the benefits? Magnetic bracelets are a piece of jewelry, worn for the therapeutic benefits of the magnetic field. Magnetic bracelets has been used successfully by many people for pain relief of inflammatory conditions such as arthritis, tendinitis and bursitis.

A randomized, placebo controlled trial with three parallel groups, came to the conclusion : Pain from osteoarthritis of the hip and knee decreases when wearing magnetic bracelets. It is uncertain whether this response is due to specific or non-specific (placebo) effects. Tim Harlow, general practitioner, Colin Greaves, research fellow, Adrian White, senior research fellow, Liz Brown, research assistant, Anna Hart, statistician, Edzard Ernst, professor of complementary medicine.

The entrepreneurs seem to have forgotten a few things which we tried to make clear in our paper:

  • this article was published in the Christmas issue of the BMJ which specialises in publishing unusual and odd findings with a high entertainment value,
  • in our paper, we point out that “the contamination of group B with stronger magnets prevented a more objective estimation of any-placebo effect”,
  • and stressed that “there were problems with the weak magnets”,
  • and that “a per-specification analysis suggested (but could not confirm) a specific effect of magnetic bracelets over and above placebo”.

Most importantly, this was just one trial, and surely one swallow does not make a summer! We should always consider the totality of the reliable evidence. Being conscientious researchers, at the time, we did exactly that and conducted a systematic review. Here is the abstract in its full beauty:

BACKGROUND:

Static magnets are marketed with claims of effectiveness for reducing pain, although evidence of scientific principles or biological mechanisms to support such claims is limited. We performed a systematic review and meta-analysis to assess the clinical evidence from randomized trials of static magnets for treating pain.

METHODS:

Systematic literature searches were conducted from inception to March 2007 for the following data sources: MEDLINE, EMBASE, AMED (Allied and Complementary Medicine Database), CINAHL, Scopus, the Cochrane Library and the UK National Research Register. All randomized clinical trials of static magnets for treating pain from any cause were considered. Trials were included only if they involved a placebo control or a weak magnet as the control, with pain as an outcome measure. The mean change in pain, as measured on a 100-mm visual analogue scale, was defined as the primary outcome and was used to assess the difference between static magnets and placebo.

RESULTS:

Twenty-nine potentially relevant trials were identified. Nine randomized placebo-controlled trials assessing pain with a visual analogue scale were included in the main meta-analysis; analysis of these trials suggested no significant difference in pain reduction (weighted mean difference [on a 100-mm visual analogue scale] 2.1 mm, 95% confidence interval -1.8 to 5.9 mm, p = 0.29). This result was corroborated by sensitivity analyses excluding trials of acute effects and conditions other than musculoskeletal conditions. Analysis of trials that assessed pain with different scales suggested significant heterogeneity among the trials, which means that pooling these data is unreliable.

INTERPRETATION:

The evidence does not support the use of static magnets for pain relief, and therefore magnets cannot be recommended as an effective treatment. For osteoarthritis, the evidence is insufficient to exclude a clinically important benefit, which creates an opportunity for further investigation.

So, would I, on the basis of the current best evidence, recommend magnetic bracelets to people who suffer from pain? No! In my view, only charlatans would do such a thing.

One of the questions I hear regularly is ‘HOW DO THE EFFECTS OF THIS ALTERNATIVE TREATMENT COMPARE TO THOSE OF CONVENTIONAL OPTIONS’? Take acupuncture in the management of osteoarthritis, for instance. There is some encouraging evidence suggesting it might help. The most recent systematic review that I know of concluded that “acupuncture provided significantly better relief from knee osteoarthritis pain and a larger improvement in function than sham acupuncture, standard care treatment, or waiting for further treatment.” However, in order to estimate its value in practice, we ought to know whether it is as good as or perhaps even better than standard treatments. In other words, what we really want to know is its relative effectiveness.

Data to evaluate the relative effectiveness of acupuncture or other alternative therapies are hard to come by. Ideally, one would require clinical trials which provide direct comparisons between the alternative and the conventional therapy. Sadly, such studies are scarce or even non-existent. Therefore we might have to rely on more indirect evidence. A new paper could be a step in the right direction.

The aim of this systematic review was to critically evaluate existing osteoarthritis (OA) management guidelines to better understand potential issues and barriers.

A systematic review of the literature in MEDLINE published from January 1, 2000 to April 1, 2013 was performed and supplemented by bibliographic reviews, following PRISMA guidelines and a written protocol. Following initial title and abstract screening, two authors independently reviewed full-text articles; a third settled disagreements. Two independent reviewers extracted data into a standardized form. Two authors independently assessed guideline quality; three generated summary recommendations based on the extracted guideline data.

Overall, 16 articles were included in the final review. There was broad agreement on recommendations by the various organizations. For non-pharmacologic modalities, education/self-management, exercise, weight loss if overweight, walking aids as indicated, and thermal modalities were widely recommended. For appropriate patients, joint replacement was recommended; arthroscopy with debridement was not recommended for symptomatic knee OA. Pharmacologic modalities most recommended included acetaminophen/paracetamol for first line treatment and oral or topical NSAIDs for second line therapy. Intra-articular corticosteroids were generally recommended for hip and knee OA. Controversy remains about the use of acupuncture, knee braces, heel wedges, intra-articular hyaluronans, and glucosamine/chondroitin.

I think that this tells us fairly clearly that, compared to other options, acupuncture is not considered to be an overwhelmingly effective treatment for osteoarthritis by those who understand that condition best. Several other therapies seem to be preferable because the evidence is clearer and stronger and their effect sizes is larger. This, I think begs the question whether it is in the best interest of patients or indeed ethical to ignore this knowledge and recommend acupuncture as a treatment of osteoarthritis.

More generally speaking, we should always bear in mind that it is not enough proving a therapy to be effective; we usually also need to consider what else is on offer. And if you think that this is rather complex, you are, of course, correct – but wait until someone mentions issues such as safety and cost of all the relevant therapeutic options.

A recently published study by Danish researchers aimed at comparing the effectiveness of a patient education (PEP) programme with or without the added effect of chiropractic manual therapy (MT) to a minimal control intervention (MCI). Its results seem to indicate that chiropractic MT is effective. Is this the result chiropractors have been waiting for?

To answer this question, we need to look at the trial and its methodology in more detail.

A total of 118 patients with clinical and radiographic unilateral hip osteoarthritis (OA) were randomized into one of three groups: PEP, PEP+ MT or MCI. The PEP was taught by a physiotherapist in 5 sessions. The MT was delivered by a chiropractor in 12 sessions, and the MCI included a home stretching programme. The primary outcome measure was the self-reported pain severity on an 11-box numeric rating scale immediately following the 6-week intervention period. Patients were subsequently followed for one year.

The primary analyses included 111 patients. In the PEP+MT group, a statistically and clinically significant reduction in pain severity of 1.9 points was noted compared to the MCI of 1.90. The number needed to treat for PEP+MT was 3. No difference was found between the PEP and the MCI groups. At 12 months, the difference favouring PEP+MT was maintained.

The authors conclude that for primary care patients with osteoarthritis of the hip, a combined intervention of manual therapy and patient education was more effective than a minimal control intervention. Patient education alone was not superior to the minimal control intervention.

This is an interesting, pragmatic trial with a result suggesting that chiropractic MT in combination with PEP is effective in reducing the pain of hip OA. One could easily argue about the small sample size, the need for independent replication etc. However, my main concern is the fact that the findings can be interpreted in not just one but in at least two very different ways.

The obvious explanation would be that chiropractic MT is effective. I am sure that chiropractors would be delighted with this conclusion. But how sure can we be that it would reflect the truth?

I think an alternative explanation is just as (possibly more) plausible: the added time, attention and encouragement provided by the chiropractor (who must have been aware what was at stake and hence highly motivated) was the effective element in the MT-intervention, while the MT per se made little or no difference. The PEP+MT group had no less than 12 sessions with the chiropractor. We can assume that this additional care, compassion, empathy, time, encouragement etc. was a crucial factor in making these patients feel better and in convincing them to adhere more closely to the instructions of the PEP. I speculate that these factors were more important than the actual MT itself in determining the outcome.

In my view, such critical considerations regarding the trial methodology are much more than an exercise in splitting hair. They are important in at least two ways.

Firstly, they remind us that clinical trials, whenever possible, should be designed such that they allow only one interpretation of their results. This can sometimes be a problem with pragmatic trials of this nature. It would be wise, I think, to conduct pragmatic trials only of interventions which have previously been proven to work.  To the best of my knowledge, chiropractic MT as a treatment for hip OA does not belong to this category.

Secondly, it seems crucial to be aware of such methodological issues and to consider them carefully before research findings are translated into clinical practice. If not, we might end up with  therapeutic decisions (or guidelines) which are quite simply not warranted.

I would not be in the least surprised, if chiropractic interest groups were to use the current findings for promoting chiropractic in hip-OA. But what, if the MT per se was ineffective, while the additional care, compassion and encouragement was? In this case, we would not need to recruit (and pay for) chiropractors and put up with the considerable risks chiropractic treatments can entail; we would merely need to modify the PE programme such that patients are better motivated to adhere to it.

As it stands, the new study does not tell us much that is of any practical use. In my view, it is a pragmatic trial which cannot readily be translated into evidence-based practice. It might get interpreted as good news for chiropractic but, in fact, it is not.

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