MD, PhD, FMedSci, FRSB, FRCP, FRCPEd

methodology

In the realm of alternative medicine, we encounter many therapeutic claims that beggar belief. This is true for most modalities but perhaps for none more than chiropractic. Many chiropractors still adhere to Palmer’s gospel of the ‘inate’, ‘subluxation’ etc. and thus they believe that their ‘adjustments’ are a cure all. Readers of this blog will know all that, of course, but even they might be surprised by the notion that a chiropractic adjustment improves the voice of a choir singer.

This, however, is precisely the ‘hypothesis’ that was recently submitted to an RCT. To be precise, the study investigated the effect of spinal manipulative therapy (SMT) on the singing voice of male individuals.

Twenty-nine subjects were selected among male members of a local choir. Participants were randomly assigned to two groups: (A) a single session of chiropractic SMT and (B) a single session of non-therapeutic transcutaneous electrical nerve stimulation (TENS). Recordings of the singing voice of each participant were taken immediately before and after the procedures. After a 14-day wash-out period, procedures were switched between groups: participants who underwent SMT on the first occasion were now subjected to TENS and vice versa. Recordings were assessed via perceptual audio and acoustic evaluations. The same recording segment of each participant was selected. Perceptual audio evaluation was performed by a specialist panel (SP). Recordings of each participant were randomly presented thus making the SP blind to intervention type and recording session (before/after intervention). Recordings compiled in a randomized order were also subjected to acoustic evaluation.

No differences in the quality of the singing on perceptual audio evaluation were observed between TENS and SMT.

The authors concluded that no differences in the quality of the singing voice of asymptomatic male singers were observed on perceptual audio evaluation or acoustic evaluation after a single spinal manipulative intervention of the thoracic and cervical spine.

Laughable? Yes!

There is nevertheless an important point to be made here, I feel: some claims are just too silly to waste resources on. Or, to put it in more scientific terms, hypotheses require much more than a vague notion or hunch.

To set up, conduct and eventually publish an RCT as above requires expertise, commitment, time and money. All of this is entirely wasted, if the prior probability of a relevant result approaches zero. In the realm of alternative medicine, this is depressingly often the case. In the final analysis, this suggests that all too often research in this area achieves nothing other than giving science a bad name.

A paper entitled ‘Real world research: a complementary method to establish the effectiveness of acupuncture’ caught my attention recently. I find it quite remarkable and think it might stimulate some discussion on this blog.  Here is its abstract:

Acupuncture has been widely used in the management of a variety of diseases for thousands of years, and many relevant randomized controlled trials have been published. In recent years, many randomized controlled trials have provided controversial or less-than-convincing evidence that supports the efficacy of acupuncture. The clinical effectiveness of acupuncture in Western countries remains controversial.

Acupuncture is a complex intervention involving needling components, specific non-needling components, and generic components. Common problems that have contributed to the equivocal findings in acupuncture randomized controlled trials were imperfections regarding acupuncture treatment and inappropriate placebo/sham controls. In addition, some inherent limitations were also present in the design and implementation of current acupuncture randomized controlled trials such as weak external validity. The current designs of randomized controlled trials of acupuncture need to be further developed. In contrast to examining efficacy and adverse reaction in a “sterilized” environment in a narrowly defined population, real world research assesses the effectiveness and safety of an intervention in a much wider population in real world practice. For this reason, real world research might be a feasible and meaningful method for acupuncture assessment. Randomized controlled trials are important in verifying the efficacy of acupuncture treatment, but the authors believe that real world research, if designed and conducted appropriately, can complement randomized controlled trials to establish the effectiveness of acupuncture. Furthermore, the integrative model that can incorporate randomized controlled trial and real world research which can complement each other and potentially provide more objective and persuasive evidence.

In the article itself, the authors list seven criteria for what they consider good research into acupuncture:

  1. Acupuncture should be regarded as complex and individualized treatment;
  2. The study aim (whether to assess the efficacy of acupuncture needling or the effectiveness of acupuncture treatment) should be clearly defined and differentiated;
  3. Pattern identification should be clearly specified, and non-needling components should also be considered;
  4. The treatment protocol should have some degree of flexibility to allow for individualization;
  5. The placebo or sham acupuncture should be appropriate: knowing “what to avoid” and “what to mimic” in placebos/shams;
  6. In addition to “hard evidence”, one should consider patient-reported outcomes, economic evaluations, patient preferences and the effect of expectancy;
  7. The use of qualitative research (e.g., interview) to explore some missing areas (e.g., experience of practitioners and patient-practitioner relationship) in acupuncture research.

Furthermore, the authors list the advantages of their RWR-concept:

  1. In RWR, interventions are tailored to the patients’ specific conditions, in contrast to standardized treatment. As a result, conclusions based on RWR consider all aspects of acupuncture that affect the effectiveness.
  2. At an operational level, patients’ choice of the treatment(s) decreases the difficulties in recruiting and retaining patients during the data collection period.
  3. The study sample in RWR is much more representative of the real world situation (similar to the section of the population that receives the treatment). The study, therefore, has higher external validity.
  4. RWR tends to have a larger sample size and longer follow-up period than RCT, and thus is more appropriate for assessing the safety of acupuncture.

The authors make much of their notion that acupuncture is a COMPLEX INTERVENTION; specifically they claim the following: Acupuncture treatment includes three aspects: needling, specific non-needling components drove by acupuncture theory, and generic components not unique to acupuncture treatment. In addition, acupuncture treatment should be performed on the basis of the patient condition and traditional Chinese medicine (TCM) theory.

There is so much BS here that it is hard to decide where to begin refuting. As the assumption of acupuncture or other alternative therapies being COMPLEX INTERVENTIONS (and therefore exempt from rigorous tests) is highly prevalent in this field, let me try to just briefly tackle this one.

The last time I saw a patient and prescribed a drug treatment I did all of the following:

  • I greeted her, asked her to sit down and tried to make her feel relaxed.
  • I first had a quick chat about something trivial.
  • I then asked why she had come to see me.
  • I started to take notes.
  • I inquired about the exact nature and the history of her problem.
  • I then asked her about her general medical history, family history and her life-style.
  • I also asked about any psychological problems that might relate to her symptoms.
  • I then conducted a physical examination.
  • Subsequently we discussed what her diagnosis might be.
  • I told her what my working diagnosis was.
  • I ordered a few tests to either confirm or refute it and explained them to her.
  • We decided that she should come back and see me in a few days when her tests had come back.
  • In order to ease her symptoms in the meanwhile, I gave her a prescription for a drug.
  • We discussed this treatment, how and when she should take it, adverse effects etc.
  • We also discussed other therapeutic options, in case the prescribed treatment was in any way unsatisfactory.
  • I reassured her by telling her that her condition did not seem to be serious and stressed that I was confident to be able to help her.
  • She left my office.

The point I am trying to make is: prescribing an entirely straight forward drug treatment is also a COMPLEX INTERVENTION. In fact, I know of no treatment that is NOT complex.

Does that mean that drugs and all other interventions are exempt from being tested in rigorous RCTs? Should we allow drug companies to adopt the RWR too? Any old placebo would pass that test and could be made to look effective using RWR. In the example above, my compassion, care and reassurance would alleviate my patient’s symptoms, even if the prescription I gave her was complete rubbish.

So why should acupuncture (or any other alternative therapy) not be tested in proper RCTs? I fear, the reason is that RCTs might show that it is not as effective as its proponents had hoped. The conclusion about the RWR is thus embarrassingly simple: proponents of alternative medicine want double standards because single standards would risk to disclose the truth.

As promised, I will try with this post to explain my reservations regarding the new meta-analysis suggesting that individualised homeopathic remedies are superior to placebos. Before I start, however, I want to thank all those who have commented on various issues; it is well worth reading the numerous and diverse comments.

To remind us of the actual meta-analysis, it might be useful to re-publish its abstract (the full article is also available online):

BACKGROUND:

A rigorous and focused systematic review and meta-analysis of randomised controlled trials (RCTs) of individualised homeopathic treatment has not previously been undertaken. We tested the hypothesis that the outcome of an individualised homeopathic treatment approach using homeopathic medicines is distinguishable from that of placebos.

METHODS:

The review’s methods, including literature search strategy, data extraction, assessment of risk of bias and statistical analysis, were strictly protocol-based. Judgment in seven assessment domains enabled a trial’s risk of bias to be designated as low, unclear or high. A trial was judged to comprise ‘reliable evidence’ if its risk of bias was low or was unclear in one specified domain. ‘Effect size’ was reported as odds ratio (OR), with arithmetic transformation for continuous data carried out as required; OR > 1 signified an effect favouring homeopathy.

RESULTS:

Thirty-two eligible RCTs studied 24 different medical conditions in total. Twelve trials were classed ‘uncertain risk of bias’, three of which displayed relatively minor uncertainty and were designated reliable evidence; 20 trials were classed ‘high risk of bias’. Twenty-two trials had extractable data and were subjected to meta-analysis; OR = 1.53 (95% confidence interval (CI) 1.22 to 1.91). For the three trials with reliable evidence, sensitivity analysis revealed OR = 1.98 (95% CI 1.16 to 3.38).

CONCLUSIONS:

Medicines prescribed in individualised homeopathy may have small, specific treatment effects. Findings are consistent with sub-group data available in a previous ‘global’ systematic review. The low or unclear overall quality of the evidence prompts caution in interpreting the findings. New high-quality RCT research is necessary to enable more decisive interpretation.

Since my team had published an RCTs of individualised homeopathy, it seems only natural that my interest focussed on why the study (even though identified by Mathie et al) had not been included in the meta-analysis. Our study had provided no evidence that adjunctive homeopathic remedies, as prescribed by experienced homeopathic practitioners, are superior to placebo in improving the quality of life of children with mild to moderate asthma in addition to conventional treatment in primary care.

I was convinced that this trial had been rigorous and thus puzzled why, despite receiving ‘full marks’ from the reviewers, they had not included it in their meta-analysis. I thus wrote to Mathie, the lead author of the meta-analysis, and he explained: For your trial (White et al. 2003), under domain V of assessment, we were unable to extract data for meta-analysis, and so it was attributed high risk of bias, as specified by the Cochrane judgmental criteria. Our designated main outcome was the CAQ, for which we needed to know (or could at least estimate) a mean and SD for both the baseline and the end-point of the study. Since your paper reported only the change from baseline in Table 3 or in the main text, it is not possible to derive the necessary end-point for analysis.

It took a while and several further emails until I understood: our study did report both the primary (Table 2 quality of life) and secondary outcome measure (Table 3 severity of symptoms). The primary outcome measure was reported in full detail such that a meta-analysis would have been possible. The secondary outcome measure was also reported but not in full detail, and the data provided by us would not lend themselves to meta-analyses. By electing not our primary but our secondary outcome measure for their meta-analysis, Mathie et al were able to claim that they were unable to use our study and reject it for their meta-analysis.

Why did they do that?

The answer is simple: in their methods section, they specify that they used outcome measures “based on a pre-specified hierarchical list in order of greatest to least importance, recommended by the WHO“. This, I would argue is deeply flawed: the most important outcome measure of a study is usually the one for which the study was designed, not the one that some guys at the WHO feel might be important (incidentally, the WHO list was never meant to be applied to meta-analyses in that way).

By following rigidly their published protocol, the authors of the meta-analysis managed to exclude our negative trial. Thus they did everything right – or did they?

Well, I think they committed several serious mistakes.

  • Firstly, they wrote the protocol, which forced them to exclude our study. Following a protocol is not a virtue in itself; if the protocol is nonsensical it even is the opposite. Had they proceeded as is normal in such cases and used our primary outcome measure in their meta-analyses, it is most likely that their overall results would not have been in favour of homeopathy.
  • Secondly, they awarded our study a malus point for the criterium ‘selective outcome reporting’. This is clearly a wrong decision: we did report the severity-outcome, albeit not in sufficient detail for their meta-analysis. Had they not committed this misjudgment, our RCT would have been the only one with an ‘A’ rating. This would have very clearly highlighted the nonsense of excluding the best-rated trial from meta-analysis.

There are several other oddities as well. For instance, Mathie et al judge our study to be NOT free of vested interest. I asked Mathie why they had done this and was told it is because we accepted free trial medication from a homeopathic pharmacy. I would argue that my team was far less plagued by vested interest than the authors of their three best (and of course positive) trials who, as I happen to know, are consultants for homeopathic manufacturers.

And all of this is just in relation to our own study. Norbert Aust has uncovered similar irregularities with other trials and I take the liberty of quoting his comments posted previously again here:

I have reason to believe that this review and metaanalysis in biased in favor of homeopathy. To check this, I compared two studies (1) Jacobs 1994 about the treatment of childhood diarrhea in Nicaragua, (2) Walach 1997 about homeopathic threatment of headaches. The Jacobs study is one of the three that provided ‘reliable evidence’, Walach’s study earned a poor C2.2 rating and was not included in the meta-analyses. Jacobs’ results were in favour of homeopathy, Walach’s not.

For the domains where the rating of Walach’s study was less than that of the Jacobs study, please find citations from the original studies or my short summaries for the point in question.

Domain I: Sequence generation:
Walach:
“The remedy selected was then mailed to a notary public who held a stock of placebos. The notary threw a dice and mailed either the homeopathic remedy or an appropriate placebo. The notary was provided with a blank randomisation list.”
Rating: UNCLEAR (Medium risk of bias)

Jacobs:
“For each of these medications, there was a box of tubes in sequentially numbered order which had been previously randomized into treatment or control medication using a random numbers table in blocks of four”
Rating: YES (Low risk of bias)

Domain IIIb: Blinding of outcome assessor
Walach:
“The notary was provided with a blank randomization list which was an absolutely unique document. It was only handed out after the biometrician (WG) had deposited all coded original data as a printout at the notary’s office. (…) Data entry was performed blindly by personnel not involved in the study. ”
Rating: UNCLEAR (Medium risk of bias)

Jacobs:
“All statistical analyses were done before breaking the randomisation code, using the program …”
Rating: YES (Low risk of bias)

Domain V: Selective outcome reporting

Walach:
Study protocol was published in 1991 prior to enrollment of participants, all primary outcome variables were reported with respect to all participants and the endpoints.
Rating: NO (high risk of bias)

Jacobs:
No prior publication of protocol, but a pilot study exists. However this was published in 1993 only after the trial was performed in 1991. Primary outcome defined (duration of diarrhea), reported but table and graph do not match, secondary outcome (number of unformed stools on day 3) seems defined post hoc, for this is the only one point in time, this outcome yielded a significant result.
Rating: YES (low risk of bias)

Domain VI: Other sources of bias:

Walach:
Rating: NO (high risk of bias), no details given

Jacobs:
Imbalance of group properties (size, weight and age of children), that might have some impact on course of disease, high impact of parallel therapy (rehydration) by far exceeding effect size of homeopathic treatment
Rating: YES (low risk of bias), no details given

In a nutshell: I fail to see the basis for the different ratings in the studies themselves. I assume bias of the authors of the review.

Conclusion

So, what about the question posed in the title of this article? The meta-analysis is clearly not a ‘proof of concept’. But is it proof for misconduct? I asked Mathie and he answered as follows: No, your statement does not reflect the situation at all. As for each and every paper, we selected the main outcome measure for your trial using the objective WHO classification approach (in which quality of life is clearly of lower rank than severity). This is all clearly described in our prospective protocol. Under no circumstances did we approach this matter retrospectively, in the way you are implying. 

Some nasty sceptics might have assumed that the handful of rigorous studies with negative results were well-known to most researchers of homeopathy. In this situation, it would have been hugely tempting to write the protocol such that these studies must be excluded. I am thrilled to be told that the authors of the current new meta-analysis (who declared all sorts of vested interests at the end of the article) resisted this temptation.

On this blog and elsewhere, I have repeatedly cast doubt on the efficacy of homeopathy – not because I have ‘an axe to grind’, as some seem to believe, but because

  1. the assumptions which underpin homeopathy fly in the face of science,
  2. the clinical evidence fails to show that it works beyond a placebo effect.

But was I correct?

A new systematic review and meta-analysis seems to indicate that I was mistaken. It tested the hypothesis that the outcome of an individualised homeopathic treatment (homeopaths would argue that this is the only true approach to homeopathy) is distinguishable from that with placebos.

The review’s methods, including literature search strategy, data extraction, assessment of risk of bias and statistical analysis, were strictly protocol-based. Judgment in seven assessment domains enabled a trial’s risk of bias to be designated as low, unclear or high. A trial was judged to comprise ‘reliable evidence’ if its risk of bias was low or was unclear in one specified domain. ‘Effect size’ was reported as odds ratio (OR), with arithmetic transformation for continuous data carried out as required; OR > 1 signified an effect favouring homeopathy.

Thirty-two eligible RCTs studied 24 different medical conditions in total. Twelve trials were classed ‘uncertain risk of bias’, three of which displayed relatively minor uncertainty and were designated reliable evidence; 20 trials were classed ‘high risk of bias’. Twenty-two trials had extractable data and were subjected to meta-analysis; OR = 1.53 (95% confidence interval (CI) 1.22 to 1.91). For the three trials with reliable evidence, sensitivity analysis revealed OR = 1.98 (95% CI 1.16 to 3.38).

The authors arrived at the following conclusion: medicines prescribed in individualised homeopathy may have small, specific treatment effects. Findings are consistent with sub-group data available in a previous ‘global’ systematic review. The low or unclear overall quality of the evidence prompts caution in interpreting the findings. New high-quality RCT research is necessary to enable more decisive interpretation.

One does not need to be a prophet to predict that the world of homeopathy will declare this article as the ultimate proof of homeopathy’s efficacy beyond placebo. Already the ‘British Homeopathic Association’ has issued the following press release:

Clinical evidence for homeopathy published

Research into the effectiveness of homeopathy as an individualised treatment has produced results that may surprise many from the worlds of science and medicine. The conclusions are reported cautiously, but the new publication is the first of its type to present evidence that medicines prescribed in individualised homeopathy may have specific effects.

The paper, published in the peer-reviewed journal Systematic Reviews,1 reports a rigorous systematic review and meta-analysis of 32 randomised controlled trials (RCTs) in which homeopathic medicines were prescribed on an individual basis to each participant, depending on their particular symptoms.

The overall quality of the RCT evidence was found to be low or unclear, preventing the researchers from reaching decisive conclusions. Three RCTs were identified as “reliable evidence”.

The study was led by Dr Robert Mathie, research development adviser for the British Homeopathic Association, in partnership with a number of collaborators, including colleagues at the Robertson Centre for Biostatistics, University of Glasgow, who independently verified the statistical methods and findings.

“What we found from the statistics,” says Dr Mathie, “is that the effect of individualised treatment using homeopathic medicines was significantly greater than placebos, and that this effect was retained when we included only the three trials with reliable evidence. This tentatively provides proof of concept that homeopathic medicines have clinical treatment effects.”

Surprised? I was stunned and thus studied the article in much detail (luckily the full text version is available online). Then I entered into an email exchange with the first author who I happen to know personally (to his credit, he responded regularly). In the end, this conversation helped me to better understand the review’s methodology; but it also resulted in me being very much underwhelmed by the reliability of the authors’ conclusion.

Normally I would now explain why. But, in this particular case, I thought it would be interesting and helpful to give others the opportunity to examine the article and come up with their own comments. Subsequently I will add my criticisms.

SO PLEASE TAKE SOME TIME TO STUDY THIS PAPER AND TELL US WHAT YOU THINK.

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.

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