MD, PhD, FMedSci, FSB, FRCP, FRCPEd

clinical trial

1 2 3 9

Many proponents of alternative medicine seem somewhat suspicious of research; they have obviously understood that it might not produce the positive result they had hoped for; after all, good research tests hypotheses and does not necessarily confirm beliefs. At the same time, they are often tempted to conduct research: this is perceived as being good for the image and, provided the findings are positive, also good for business.

Therefore they seem to be tirelessly looking for a study design that cannot ‘fail’, i.e. one that avoids the risk of negative results but looks respectable enough to be accepted by ‘the establishment’. For these enthusiasts, I have good news: here is the study design that cannot fail.

It is perhaps best outlined as a concrete example; for reasons that will become clear very shortly, I have chosen reflexology as a treatment of diabetic neuropathy, but you can, of course, replace both the treatment and the condition as it suits your needs. Here is the outline:

  • recruit a group of patients suffering from diabetic neuropathy – say 58, that will do nicely,
  • randomly allocate them to two groups,
  • the experimental group receives regular treatments by a motivated reflexologist,
  • the controls get no such therapy,
  • both groups also receive conventional treatments for their neuropathy,
  • the follow-up is 6 months,
  • the following outcome measures are used: pain reduction, glycemic control, nerve conductivity, and thermal and vibration sensitivities,
  • the results show that the reflexology group experience more improvements in all outcome measures than those of control subjects,
  • your conclusion: This study exhibited the efficient utility of reflexology therapy integrated with conventional medicines in managing diabetic neuropathy.

Mission accomplished!

This method is fool-proof, trust me, I have seen it often enough being tested, and never has it generated disappointment. It cannot fail because it follows the notorious A+B versus B design (I know, I have mentioned this several times before on this blog, but it is really important, I think): both patient groups receive the essential mainstream treatment, and the experimental group receives a useless but pleasant alternative treatment in addition. The alternative treatment involves touch, time, compassion, empathy, expectations, etc. All of these elements will inevitably have positive effects, and they can even be used to increase the patients’ compliance with the conventional treatments that is being applied in parallel. Thus all outcome measures will be better in the experimental compared to the control group.

The overall effect is pure magic: even an utterly ineffective treatment will appear as being effective – the perfect method for producing false-positive results.

And now we hopefully all understand why this study design is so very popular in alternative medicine. It looks solid – after all, it’s an RCT!!! – and it thus convinces even mildly critical experts of the notion that the useless treatment is something worth while. Consequently the useless treatment will become accepted as ‘evidence-based’, will be used more widely and perhaps even reimbursed from the public purse. Business will be thriving!

And why did I employ reflexology for diabetic neuropathy? Is that example not a far-fetched? Not a bit! I used it because it describes precisely a study that has just been published. Of course, I could also have taken the chiropractic trial from my last post, or dozens of other studies following the A+B versus B design – it is so brilliantly suited for misleading us all.

On this blog, I have often pointed out how dismally poor most of the trials of alternative therapies frequently are, particularly those in the realm of chiropractic. A brand-new study seems to prove my point.

The aim of this trial was to determine whether spinal manipulative therapy (SMT) plus home exercise and advice (HEA) compared with HEA alone reduces leg pain in the short and long term in adults with sub-acute and chronic back-related leg-pain (BRLP).

Patients aged 21 years or older with BRLP for least 4 weeks were randomised to receive 12 weeks of SMT plus HEA or HEA alone. Eleven chiropractors with a minimum of 5 years of practice experience delivered SMT in the SMT plus HEA group. The primary outcome was subjective BRLP at 12 and 52 weeks. Secondary outcomes were self-reported low back pain, disability, global improvement, satisfaction, medication use, and general health status at 12 and 52 weeks.

Of the 192 enrolled patients, 191 (99%) provided follow-up data at 12 weeks and 179 (93%) at 52 weeks. For leg pain, SMT plus HEA had a clinically important advantage over HEA (difference, 10 percentage points [95% CI, 2 to 19]; P = 0.008) at 12 weeks but not at 52 weeks (difference, 7 percentage points [CI, -2 to 15]; P = 0.146). Nearly all secondary outcomes improved more with SMT plus HEA at 12 weeks, but only global improvement, satisfaction, and medication use had sustained improvements at 52 weeks. No serious treatment-related adverse events or deaths occurred.

The authors conclude that, for patients with BRLP, SMT plus HEA was more effective than HEA alone after 12 weeks, but the benefit was sustained only for some secondary outcomes at 52 weeks.

This is yet another pragmatic trial following the notorious and increasingly popular A+B versus B design. As pointed out repeatedly on this blog, this study design can hardly ever generate a negative result (A+B is always more than B, unless A has a negative value [which even placebos don't have]). Thus it is not a true test of the experimental treatment but all an exercise to create a positive finding for a potentially useless treatment. Had the investigators used any mildly pleasant placebo with SMT, the result would have been the same. In this way, they could create results showing that getting a £10 cheque or meeting with pleasant company every other day, together with HEA, is more effective than HEA alone. The conclusion that the SMT, the cheque or the company have specific effects is as implicit in this article as it is potentially wrong.

The authors claim that their study was limited because patient-blinding was not possible. This is not entirely true, I think; it was limited mostly because it failed to point out that the observed outcomes could be and most likely are due to a whole range of factors which are not directly related to SMT and, most crucially, because its write-up, particularly the conclusions, wrongly implied cause and effect between SMT and the outcome. A more accurate conclusion could have been as follows: SMT plus HEA was more effective than HEA alone after 12 weeks, but the benefit was sustained only for some secondary outcomes at 52 weeks. Because the trial design did not control for non-specific effects, the observed outcomes are consistent with SMT being an impressive placebo.

No such critical thought can be found in the article; on the contrary, the authors claim in their discussion section that the current trial adds to the much-needed evidence base about SMT for subacute and chronic BRLP. Such phraseology is designed to mislead decision makers and get SMT accepted as a treatment of conditions for which it is not necessarily useful.

Research where the result is known before the study has even started (studies with a A+B versus B design) is not just useless, it is, in my view, unethical: it fails to answer a real question and is merely a waste of resources as well as an abuse of patients willingness to participate in clinical trials. But the authors of this new trial are in good and numerous company: in the realm of alternative medicine, such pseudo-research is currently being published almost on a daily basis. What is relatively new, however, that even some of the top journals are beginning to fall victim to this incessant stream of nonsense.

Kinesiology tape is all the rage. Its proponents claim that it increases cutaneous stimulation, which facilitates motor unit firing, and consequently improves functional performance. But is this just clever marketing, wishful thinking or is it true? To find out, we need reliable data.

The current trial results are sparse, confusing and contradictory. A recent systematic review indicated that kinesiology tape may have limited potential to reduce pain in individuals with musculoskeletal injury; however, depending on the conditions, the reduction in pain may not be clinically meaningful. Kinesiology tape application did not reduce specific pain measures related to musculoskeletal injury above and beyond other modalities compared in the context of included articles. 

The authors concluded that kinesiology tape may be used in conjunction with or in place of more traditional therapies, and further research that employs controlled measures compared with kinesiology tape is needed to evaluate efficacy.

This need for further research has just been met by Korean investigators who conducted a study testing the true effects of KinTape by a deceptive, randomized, clinical trial.

Thirty healthy participants performed isokinetic testing of three taping conditions: true facilitative KinTape, sham KinTape, and no KinTape. The participants were blindfolded during the evaluation. Under the pretense of applying adhesive muscle sensors, KinTape was applied to their quadriceps in the first two conditions. Normalized peak torque, normalized total work, and time to peak torque were measured at two angular speeds (60°/s and 180°/s) and analyzed with one-way repeated measures ANOVA.

Participants were successfully deceived and they were ignorant about KinTape. No significant differences were found between normalized peak torque, normalized total work, and time to peak torque at 60°/s or 180°/s (p = 0.31-0.99) between three taping conditions. The results showed that KinTape did not facilitate muscle performance in generating higher peak torque, yielding a greater total work, or inducing an earlier onset of peak torque.

The authors concluded that previously reported muscle facilitatory effects using KinTape may be attributed to placebo effects.

The claims that are being made for kinesiology taping are truly extraordinary; just consider what this website is trying to tell us:

Kinesiology tape is a breakthrough new method for treating athletic sprains, strains and sports injuries. You may have seen Olympic and celebrity athletes wearing multicolored tape on their arms, legs, shoulders and back. This type of athletic tape is a revolutionary therapeutic elastic style of support that works in multiple ways to improve health and circulation in ways that traditional athletic tapes can’t compare. Not only does this new type of athletic tape help support and heal muscles, but it also provides faster, more thorough healing by aiding with blood circulation throughout the body.

Many athletes who have switched to using this new type of athletic tape report a wide variety of benefits including improved neuromuscular movement and circulation, pain relief and more. In addition to its many medical uses, Kinesiology tape is also used to help prevent injuries and manage pain and swelling, such as from edema. Unlike regular athletic taping, using elastic tape allows you the freedom of motion without restricting muscles or blood flow. By allowing the muscles a larger degree of movement, the body is able to heal itself more quickly and fully than before.

Whenever I read such over-enthusiastic promotion that is not based on evidence but on keen salesmanship, my alarm-bells start ringing and I see parallels to the worst type of alternative medicine hype. In fact, kinesiology tapes have all the hallmarks of alternative medicine and its promoters have, as far as I can see, all the characteristics of quacks. The motto seems to be: LET’S EARN SOME MONEY FAST AND IGNORE THE SCIENCE WHILE WE CAN.

Most of the underlying assumptions of alternative medicine (AM) lack plausibility. Whenever this is the case, so the argument put forward by an international team of researchers in a recent paper, there are difficulties involved in obtaining a valid statistical significance in clinical studies.

Using a mostly statistical approach, they argue that, since the prior probability of a research hypothesis is directly related to its scientific plausibility, the commonly used frequentist statistics, which do not account for this probability, are unsuitable for studies exploring matters in various degree disconnected from science. Any statistical significance obtained in this field should be considered with great caution and may be better applied to more plausible hypotheses (like placebo effect) than the specific efficacy of the intervention.

The researchers conclude that, since achieving meaningful statistical significance is an essential step in the validation of medical interventions, AM practices, producing only outcomes inherently resistant to statistical validation, appear not to belong to modern evidence-based medicine.

To emphasize their arguments, the researchers make the following additional points:

  • It is often forgotten that frequentist statistics, commonly used in clinical trials, provides only indirect evidence in support of the hypothesis examined.
  • The p-value inherently tends to exaggerate the support for the hypothesis tested, especially if the scientific plausibility of the hypothesis is low.
  • When the rationale for a clinical intervention is disconnected from the basic principles of science, as in case of complementary alternative medicines, any positive result obtained in clinical studies is more reasonably ascribable to hypotheses (generally to placebo effect) other than the hypothesis on trial, which commonly is the specific efficacy of the intervention.
  • Since meaningful statistical significance as a rule is an essential step to validation of a medical intervention, complementary alternative medicine cannot be considered evidence-based.

Further explanations can be found in the discussion of the article where the authors argue that the quality of the hypothesis tested should be consistent with sound logic and science and therefore have a reasonable prior probability of being correct. As a rule of thumb, assuming a “neutral” attitude towards the null hypothesis (odds = 1:1), a p-value of 0.01 or, better, 0.001 should suffice to give a satisfactory posterior probability of 0.035 and 0.005 respectively.

In the area of AM, hypotheses often are entirely inconsistent with logic and frequently fly in the face of science. Four examples can demonstrate this instantly and sufficiently, I think:

  • Homeopathic remedies which contain not a single ‘active’ molecule are not likely to generate biological effects.
  • Healing ‘energy’ of Reiki masters has no basis in science.
  • Meridians of acupuncture are pure imagination.
  • Chiropractic subluxation have never been shown to exist.

Positive results from clinical trials of implausible forms of AM are thus either due to chance, bias or must be attributed to more credible causes such as the placebo effect. Since the achievement of meaningful statistical significance is an essential step in the validation of medical interventions, unless some authentic scientific support to AM is provided, one has to conclude that AM cannot be considered as evidence-based.

Such arguments are by no means new; they have been voiced over and over again. Essentially, they amount to the old adage: IF YOU CLAIM THAT YOU HAVE A CAT IN YOUR GARDEN, A SIMPLE PICTURE MAY SUFFICE. IF YOU CLAIM THERE IS A UNICORN IN YOUR GARDEN, YOU NEED SOMETHING MORE CONVINCING. An extraordinary claim requires an extraordinary proof! Put into the context of the current discussion about AM, this means that the usual level of clinical evidence is likely to be very misleading as long as it totally neglects the biological plausibility of the prior hypothesis.

Proponents of AM do not like to hear such arguments. They usually insist on what we might call a ‘level playing field’ and fail to see why their assumptions require not only a higher level of evidence but also a reasonable scientific hypothesis. They forget that the playing field is not even to start with; to understand the situation better, they should read this excellent article. Perhaps its elegant statistical approach will convince them – but I would not hold my breath.

Bach Flower Remedies are the brain child of Dr Edward Bach who, as an ex-homeopath, invented his very own highly diluted remedies. Like homeopathic medicines, they are devoid of active molecules and are claimed to work via some non-defined ‘energy’. Consequently, the evidence for these treatments is squarely negative: my systematic review analysed the data of all 7 RCTs of human patients or volunteers that were available in 2010. All but one were placebo-controlled. All placebo-controlled trials failed to demonstrate efficacy. I concluded that the most reliable clinical trials do not show any differences between flower remedies and placebos.

But now, a new investigation has become available. The aim of this study was to evaluate the effect of Bach flower Rescue Remedy on the control of risk factors for cardiovascular disease in rats.

A randomized longitudinal experimental study was conducted on 18 Wistar rats which were randomly divided into three groups of six animals each and orogastrically dosed with either 200μl of water (group A, control), or 100μl of water and 100μl of Bach flower remedy (group B), or 200μl of Bach flower remedy (group C) every 2 days, for 20 days. All animals were fed standard rat chow and water ad libitum.

Urine volume, body weight, feces weight, and food intake were measured every 2 days. On day 20, tests of glycemia, hyperuricemia, triglycerides, high-density lipoprotein (HDL) cholesterol, and total cholesterol were performed, and the anatomy and histopathology of the heart, liver and kidneys were evaluated. Data were analyzed using Tukey’s test at a significance level of 5%.

No significant differences were found in food intake, feces weight, urine volume and uric acid levels between groups. Group C had a significantly lower body weight gain than group A and lower glycemia compared with groups A and B. Groups B and C had significantly higher HDL-cholesterol and lower triglycerides than controls. Animals had mild hepatic steatosis, but no cardiac or renal damage was observed in the three groups.

From these results, the authors conclude that Bach flower Rescue Remedy was effective in controlling glycemia, triglycerides, and HDL-cholesterol and may serve as a strategy for reducing risk factors for cardiovascular disease in rats. This study provides some preliminary “proof of concept” data that Bach Rescue Remedy may exert some biological effects.

If ever there was a bizarre study, it must be this one:

  • As far as I know, nobody has ever claimed that Rescue Remedy modified cardiovascular risk factors.
  • It seems debatable whether the observed changes are all positive as far as the cardiovascular risk is concerned.
  • It seems odd that a remedy that does not contain active molecules is associated with some sort of dose-effect response.
  • The modification of cardiovascular risk factors in rats might be of little relevance for humans.
  • A strategy for reducing cardiovascular risk factors in rats seems a strange idea.
  • Even the authors cannot offer a mechanism of action [other than pure magic].

Does this study tell us anything of value? The authors are keen to point out that it provides a preliminary proof of concept for Rescue Remedy having biological effects. Somehow, I doubt that this conclusion will convince many of my readers.

Dodgy science abounds in alternative medicine; this is perhaps particularly true for homeopathy. A brand-new trial seems to confirm this view.

The aim of this study was to test the hypothesis that homeopathy (H) enhances the effects of scaling and root planing (SRP) in patients with chronic periodontitis (CP).

The researchers, dentists from Brazil, randomised 50 patients with CP to one of two treatment groups: SRP (C-G) or SRP + H (H-G). Assessments were made at baseline and after 3 and 12 months of treatment. The local and systemic responses to the treatments were evaluated after one year of follow-up. The results showed that both groups displayed significant improvements, however, the H-G group performed significantly better than C-G group.

The authors concluded that homeopathic medicines, as an adjunctive to SRP, can provide significant local and systemic improvements for CP patients.

Really? I am afraid, I disagree!

Homeopathic medicines might have nothing whatsoever to do with this result. Much more likely is the possibility that the findings are caused by other factors such as:

  • placebo-effects,
  • patients’ expectations,
  • improved compliance with other health-related measures,
  • the researchers’ expectations,
  • the extra attention given to the patients in the H-G group,
  • disappointment of the C-G patients for not receiving the additional care,
  • a mixture of all or some of the above.

I should stress that it would not have been difficult to plan the study in such a way that these factors were eliminated as sources of bias or confounding. But this study was conducted according to the A+B versus B design which we have discussed repeatedly on this blog. In such trials, A is the experimental treatment (homeopathy) and B is the standard care (scaling and root planning). Unless A is an overtly harmful therapy, it is simply not conceivable that A+B does not generate better results than B alone. The simplest way to comprehend this argument is to imagine A and B are two different amounts of money: it is impossible that A+B is not more that B!

It is unclear to me what relevant research question such a study design actually does answer (if anyone knows, please tell me). It seems obvious, however, that it cannot test the hypothesis that homeopathy (H) enhances the effects of scaling and root planing (SRP). This does not necessarily mean that the design is necessarily useless.  But at the very minimum, one would need an adequate research question (one that matches this design) and adequate conclusions based on the findings.

The fact that the conclusions drawn from a dodgy trial are inadequate and misleading could be seen as merely a mild irritation. The facts that, in homeopathy, such poor science and misleading conclusions emerge all too regularly, and that journals continue to publish such rubbish are not just mildly irritating; they are annoying and worrying – annoying because such pseudo-science constitutes an unethical waste of scarce resources; worrying because it almost inevitably leads to wrong decisions in health care.

“If ever there was a permanent cure for migraine, homeopathic medicines are the only one that can do this miracle. It may sound like an overstatement and quite quackerish, but it’s true. Long term treatment with homeopathy has an excellent cure for migraine headaches.” Statements like this can be found by the thousands on the internet, not just in relation to migraine but also about osteoarthritis. Both migraine and osteoarthritis are important domains for homeopathy, and most homeopaths would not doubt for a second that they can treat these conditions effectively. This is why it is so important to highlight the few sources which are not misleading consumers into making the wrong therapeutic decisions.

‘Healthcare Improvement Scotland’ (HCIS) have just published advice for patients suffering from migraine and osteoarthritis (the full document with all the evidence can be found here). I think it is worth having a close look and I therefore cite it in full:

Homeopathic remedies are prepared by repeated dilution and vigorous shaking of substances in water. Remedies are prepared from substances that in healthy people cause the signs and symptoms of the condition being treated. The more dilute the remedy is the more potent it becomes so that the most potent remedies are unlikely to contain any of the original substance.

People in Scotland have access to homeopathy through some GPs or a referral to homeopaths in the private sector, regional NHS clinics or the Centre for Integrative Care (CIC) (formerly Glasgow Homeopathic Hospital). Not all NHSScotland health boards provide funding for homeopathy; investment varies widely among those that do, and individual boards have begun to review funding for homeopathy services.

Clinical effectiveness

  • Evidence of clinical effectiveness was reviewed from systematic reviews of four placebo controlled randomised trials of homeopathy for migraine published between 1991 and 1997; and systematic reviews of four active treatment controlled randomised trials of homeopathy for osteoarthritis published between 1983 and 2000. The quality of the evidence was low to moderate.
  • Homeopathy for migraine has not been compared with active treatment in randomised controlled trials (RCTs). Of four RCTs comparing homeopathy with placebo, only one found homeopathy to be superior.
  • Three RCTs in osteoarthritis comparing homeopathy with medicines for pain relief found either no difference between the interventions, or that analgesic treatment had a better effect than homeopathy. A further RCT comparing intra-articular injection of a homeopathic remedy with hyaluronic acid injections showed similar pain reduction in both groups.

Safety

  • Published systematic reviews of homeopathy for migraine and osteoarthritis contain insufficient information to inform conclusions about safety.

Cost effectiveness

  • No evidence on the cost effectiveness of homeopathy for migraine was identified; and the evidence from a single cost-minimisation analysis of one homeopathic preparation for osteoarthritis is not generalisable to the UK.

Context/conclusion

  • Homeopathy for migraine has not been compared with standard care in RCTs and no evidence of cost effectiveness has been identified..
  • There is insufficient evidence to determine whether or not homeopathic treatment for osteoarthritis is clinically effective compared with standard care, and no relevant evidence of cost effectiveness has been identified.
  • The evidence does not support treating migraine or osteoarthritis with homeopathy.

Before the fans of homeopathy start shouting “THIS IS ALL RUBBISH AND DISREGARDS IMPORTANT EVIDENCE!!!”, I should mention that the top experts in homeopathy were asked to contribute their evidence and were unable to find any convincing data that would have changed this negative verdict. And it is important to point out that HCIS is a respected, independent organisation that issues statements based on thorough, unbiased reviews of the evidence.

As I reported a while ago, the Australian ‘NATIONAL HEALTH AND MEDICAL RESEARCH COUNCIL’ has assessed the effectiveness of homeopathy. The evaluation looks like the most comprehensive and most independent in the history of homeopathy. Its draft report  concluded that “the evidence from research in humans does not show that homeopathy is effective for treating the range of health conditions considered.”

So, the HCIS is in excellent company and I have no doubt whatsoever that this new statement is correct – but I also have little doubt that homeopaths will dispute it.

 

Blinding patients in clinical trials is a key methodological procedure for minimizing bias and thus making sure that the results are reliable. In alternative medicine, blinding is not always straight forward, and many studies are therefore not patient-blinded. We all know that this can introduce bias into a trial, but how large is its effect on study outcomes?

This was the research question addressed by a recent systematic review of randomized clinical trials with one sub-study (i.e. experimental vs control) involving blinded patients and another, otherwise identical, sub-study involving non-blinded patients. Within each trial, the researchers compared the difference in effect sizes (i.e. standardized mean differences) between the two sub-studies. A difference <0 indicates that non-blinded patients generated a more optimistic effect estimate. The researchers then pooled the differences with random-effects inverse variance meta-analysis, and explored reasons for heterogeneity.

The main analysis included 12 trials with a total of 3869 patients. Ten of these RCTs were studies of acupuncture. The average difference in effect size for patient-reported outcomes was -0.56 (95% confidence interval -0.71 to -0.41), (I(2 )= 60%, P = 0.004), indicating that non-blinded patients exaggerated the effect size by an average of 0.56 standard deviation, but with considerable variation. Two of the 12 trials also used observer-reported outcomes, showing no indication of exaggerated effects due lack of patient blinding.

There was an even larger effect size difference in the 10 acupuncture trials [-0.63 (-0.77 to -0.49)], than in the two non-acupuncture trials [-0.17 (-0.41 to 0.07)]. Lack of patient blinding was also associated with increased attrition rates and the use of co-interventions: ratio of control group attrition risk 1.79 (1.18 to 2.70), and ratio of control group co-intervention risk 1.55 (0.99 to 2.43).

The authors conclude that this study provides empirical evidence of pronounced bias due to lack of patient blinding in complementary/alternative randomized clinical trials with patient-reported outcomes.

This is a timely, rigorous and important analysis. In alternative medicine, we currently see a proliferation of trials that are not patient-blinded. We always suspected that they are at a high risk of generating false-positive results – now we know that this is, in fact, the case.

What should we do with this insight? In my view, the following steps would be wise:

  1. Take the findings from the existing trials that are devoid of patient-blinding with more than just a pinch of salt.
  2. Discourage the funding of future studies that fail to include patient-blinding.
  3. If patient-blinding is truly and demonstrably impossible – which is not often the case – make sure that the trialists at least include blinding of the assessors of the primary outcome measures.

There must be well over 10 000 clinical trials of acupuncture; Medline lists ~5 000, and many more are hidden in the non-Medline listed literature. That should be good news! Sadly, it isn’t.

It should mean that we now have a pretty good idea for what conditions acupuncture is effective and for which illnesses it does not work. But we don’t! Sceptics say it works for nothing, while acupuncturists claim it is a panacea. The main reason for this continued controversy is that the quality of the vast majority of these 10 000 studies is not just poor, it is lousy.

“Where is the evidence for this outraging statement???” – I hear the acupuncture-enthusiasts shout. Well, how about my own experience as editor-in-chief of FACT? No? Far too anecdotal?

How about looking at Cochrane reviews then; they are considered to be the most independent and reliable evidence in existence? There are many such reviews (most, if not all [co-]authored by acupuncturists) and they all agree that the scientific rigor of the primary studies is fairly awful. Here are the crucial bits of just the last three; feel free to look for more:

All of the studies had a high risk of bias

All included trials had a high risk of bias…

The studies were not judged to be free from bias…

Or how about providing an example? Good idea! Here is a new trial which could stand for numerous others:

This study was performed to compare the efficacy of acupuncture versus corticosteroid injection for the treatment of Quervain’s tendosynovitis (no, you do not need to look up what condition this is for understanding this post). Thirty patients were treated in two groups. The acupuncture group received 5 acupuncture sessions of 30 minutes duration. The injection group received one methylprednisolone acetate injection in the first dorsal compartment of the wrist. The degree of disability and pain was evaluated by using the Quick Disabilities of the Arm, Shoulder, and Hand (Q-DASH) scale and the Visual Analogue Scale (VAS) at baseline and at 2 weeks and 6 weeks after the start of treatment. The baseline means of the Q-DASH and the VAS scores were 62.8 and 6.9, respectively. At the last follow-up, the mean Q-DASH scores were 9.8 versus 6.2 in the acupuncture and injection groups, respectively, and the mean VAS scores were 2 versus 1.2. Thus there were short-term improvements of pain and function in both groups.

The authors drew the following conclusions: Although the success rate was somewhat higher with corticosteroid injection, acupuncture can be considered as an alternative option for treatment of De Quervain’s tenosynovitis.

The flaws of this study are exemplary and numerous:

  • This should have been a study that compares two treatments – the technical term is ‘equivalence trial – and such studies need to be much larger to produce a meaningful result. Small sample sizes in equivalent trials will always make the two treatments look similarly effective, even if one is a pure placebo.
  • There is no gold standard treatment for this condition. This means that a comparative trial makes no sense at all. In such a situation, one ought to conduct a placebo-controlled trial.
  • There was no blinding of patients; therefore their expectation might have distorted the results.
  • The acupuncture group received more treatments than the injection group; therefore the additional attention might have distorted the findings.
  • Even if the results were entirely correct, one cannot conclude from them that acupuncture was effective; the notion that it was similarly ineffective as the injections is just as warranted.

These are just some of the most fatal flaws of this study. The sad thing is that similar criticisms can be made for most of the 10 000 trials of acupuncture. But the point here is not to nit-pick nor to quack-bust. My point is a different and more serious one: fatally flawed research is not just a ‘poor show’, it is unethical because it is a waste of scarce resources and, even more importantly, an abuse of patients for meaningless pseudo-science. All it does is it misleads the public into believing that acupuncture might be good for this or that condition and consequently make wrong therapeutic decisions.

In acupuncture (and indeed in most alternative medicine) research, the problem is so extremely wide-spread that it is high time to do something about it. Journal editors, peer-reviewers, ethics committees, universities, funding agencies and all others concerned with such research have to work together so that such flagrant abuse is stopped once and for all.

We all know, I think, that chronic low back pain (CLBP) is common and causes significant suffering in individuals as well as cost to society. Many treatments are on offer but, as we have seen repeatedly on this blog, not one is convincingly effective and some, like chiropractic, is associated with considerable risks.

Enthusiasts claim that hypnotherapy works well, but too little is known about the minimum dose needed to produce meaningful benefits, the roles of home practice and hypnotizability on outcome, or the maintenance of treatment benefits beyond 3 months. A new trial was aimed at addressing these issues.

One hundred veterans with CLBP participated in a randomized, four parallel group study. The groups were (1) an eight-session self-hypnosis training intervention without audio recordings for home practice; (2) an eight-session self-hypnosis training intervention with recordings; (3) a two-session self-hypnosis training intervention with recordings and brief weekly reminder telephone calls; and (4) an eight-session active (biofeedback) control intervention.

Participants in all four groups reported significant pre- to post-treatment improvements in pain intensity, pain interference and sleep quality. The three hypnotherapy groups combined reported significantly more pain intensity reduction than the control group. There was no significant difference among the three hypnotherapy groups. Over half of the participants who received hypnotherapy reported clinically meaningful (≥30%) reductions in pain intensity, and they maintained these benefits for at least 6 months after treatment. Neither hypnotizability nor amount of home practice was associated significantly with treatment outcome.

The authors conclude that two sessions of self-hypnosis training with audio recordings for home practice may be as effective as eight sessions of hypnosis treatment. If replicated in other patient samples, the findings have important implications for the application of hypnosis treatment for chronic pain management.

Even though this trial has several important limitations, I do agree with the authors: these results would be worth an independent replication – not least because self-hypnosis is cheap and does not carry great risks. What would be interesting, in my view, are studies that compare several alternative LBP therapies (e.g. chiropractic, osteopathy, acupuncture, massage, various form of exercise and hypnotherapy) in terms of cost, risks, long-term effectiveness and patients’ preference. I somehow feel that the results of such comparative trials might overturn the often issued recommendations for spinal manipulation, i.e. chiropractic or osteopathy.

1 2 3 9
Recent Comments
Click here for a comprehensive list of recent comments.
Categories