The question whether infant colic can be effectively treated with manipulative therapies might seem rather trivial – after all, this is a benign condition which the infant quickly grows out of. However, the issue becomes a little more tricky, if we consider that it was one of the 6 paediatric illnesses which were at the centre of the famous libel case of the BCA against my friend and co-author Simon Singh. At the time, Simon had claimed that there was ‘not a jot of evidence’ for claiming that chiropractic was an effective treatment of infant colic, and my systematic review of the evidence strongly supported his statement. The BCA eventually lost their libel case and with it the reputation of chiropractic. Now a new article on this intriguing topic has become available; do we have to reverse our judgements?
The aim of this new systematic review was to evaluate the efficacy or effectiveness of manipulative therapies for infantile colic. Six RCTs of chiropractic, osteopathy or cranial osteopathy alone or in conjunction with other interventions were included with a total of 325 infants. Of the 6 included studies, 5 were “suggestive of a beneficial effect” and one found no evidence of benefit. Combining all the RCTs suggested that manipulative therapies had a significant effect. The average crying time was reduced by an average of 72 minutes per day. This effect was sustained for studies with a low risk of selection bias and attrition bias. When analysing only those studies with a low risk of performance bias (i.e. parental blinding) the improvement in daily crying hours was no longer statistically significant.
The quality of the studies was variable. There was a generally low risk of selection bias but a high risk of performance bias. Only one of the studies recorded adverse events and none were encountered.
From these data, the authors drew the following conclusion: Parents of infants receiving manipulative therapies reported fewer hours crying per day than parents whose infants did not and this difference was statistically significant. Most studies had a high risk of performance bias due to the fact that the assessors (parents) were not blind to who had received the intervention. When combining only those trials with a low risk of such performance bias the results did not reach statistical significance.
Does that mean that chiropractic does work for infant colic? No, it does not!
The first thing to point out is that the new systematic review included not just RCTs of chiropractic but also osteopathy and cranio-sacral therapy.
The second important issue is that the effects disappear, once performance bias is being accounted for which clearly shows that the result is false positive.
The third relevant fact is that the majority of the RCTs were of poor quality. The methodologically best studies were negative.
And the fourth thing to note is that only one study mentioned adverse effects, which means that the other 5 trials were in breach of one of rather elementary research ethics.
What makes all of this even more fascinating is the fact that the senior author of the new publication, George Lewith, is the very expert who advised the BCA in their libel case against Simon Singh. He seems so fond of his work that he even decided to re-publish it using even more misleading language than before. It is, of course, far from me to suggest that his review was an attempt to white-wash the issue of chiropractic ‘bogus’ claims. However, based on the available evidence, I would have formulated conclusions which are more than just a little different from his; something like this perhaps:
The current best evidence suggests that the small effects that emerge when we pool the data from mostly unreliable studies are due to bias and therefore not real. This systematic review therefore fails to show that manipulative therapies are effective. It furthermore points to a serious breach of research ethics by the majority of researchers in this field.
Imagine an area of therapeutics where 100% of all findings of hypothesis-testing research is positive, i.e. comes to the conclusion that the treatment in question is effective. Theoretically, this could mean that the therapy is a miracle cure which is useful for every single condition in every single setting. But sadly, there are no miracle cures. Therefore something must be badly and worryingly amiss with the research in an area that generates 100% positive results.
Acupuncture is such an area; we and others have shown that Chinese trials of acupuncture hardly ever produce a negative finding. In other words, one does not need to read the paper, one already knows that it is positive – even more extreme: one does not need to conduct the study, one already knows the result before the research has started. But you might not believe my research nor that of others. We might be chauvinist bastards who want to discredit Chinese science. In this case, you might perhaps believe Chinese researchers.
In this systematic review, all randomized controlled trials (RCTs) of acupuncture published in Chinese journals were identified by a team of Chinese scientists. A total of 840 RCTs were found, including 727 RCTs comparing acupuncture with conventional treatment, 51 RCTs with no treatment controls, and 62 RCTs with sham-acupuncture controls. Among theses 840 RCTs, 838 studies (99.8%) reported positive results from primary outcomes and two trials (0.2%) reported negative results. The percentages of RCTs concealment of the information on withdraws or sample size calculations were 43.7%, 5.9%, 4.9%, 9.9%, and 1.7% respectively.
The authors concluded that publication bias might be major issue in RCTs on acupuncture published in Chinese journals reported, which is related to high risk of bias. We suggest that all trials should be prospectively registered in international trial registry in future.
I applaud the authors’ courageous efforts to conduct this analysis, but I do not agree with their conclusion. The question why all Chinese acupuncture trials are positive has puzzled me since many years, and I have quizzed numerous Chinese colleagues why this might be so. The answer I received was uniformly that it would be very offensive for Chinese researchers to conceive a study that does not confirm the views held by their peers. In other words, acupuncture research in China is conducted to confirm the prior assumption that this treatment is effective. It seems obvious that this is an abuse of science which must cause confusion.
Whatever the reasons for the phenomenon, and we can only speculate about them, the fact has been independently confirmed several times and is now quite undeniable: acupuncture trials from China – and these constitute the majority of the evidence-base in this area – cannot be trusted. The only way to adequately deal with this problem that I can think of is to discard them outright.
The fact that practitioners of alternative medicine frequently advise their patients against immunising their children has been documented repeatedly. In particular, doctors of anthroposophy, chiropractors and homeopaths are implicated in thus endangering public health. Less is known about naturopaths attitude in this respect. Now new data have emerged which confirm some of our worst fears.
This survey aimed at assessing the attitudes, education, and sources of knowledge surrounding childhood vaccinations of 560 students at National College of Natural Medicine in Portland, US. Students were asked about demographics, sources of information about childhood vaccines, differences between mainstream and CAM education on childhood vaccines, alternative vaccine schedules, adverse effects, perceived efficacy, and credibility of information sources.
A total of 109 students provided responses (19.4% response rate). All students surveyed learned about vaccinations in multiple courses and through independent study. The information sources employed had varying levels of credibility. Only 26% of the responding students planned on regularly prescribing or recommending vaccinations for their patients; 82% supported the general concept of vaccinations for prevention of infectious diseases.
The vast majority (96%) of those who might recommend vaccinations reported that they would only recommend a schedule that differed from the standard CDC-ACIP schedule.
Many respondents were concerned about vaccines being given too early (73%), too many vaccines administered simultaneously (70%), too many vaccines overall (59%), and about preservatives and adjuvants in vaccines (72%). About 40% believed that a healthy diet and lifestyle was more important for prevention of infectious diseases than vaccines. 90% admitted that they were more critical of vaccines than mainstream pediatricians, medical doctors, and medical students.
These results speak for themselves and leave me (almost) speechless. The response rate was truly dismal, and it is fair to assume that the non-responding students held even more offensive views on vaccination than their responding colleagues. The findings seem to indicate that naturopaths are systematically trained to become anti-vaxers who believe that their naturopathic treatments offer better protection than vaccines. They are thus depriving many of their patients of arguably the most successful means of disease prevention that exists today. To put it bluntly: naturopaths seem to be brain-washed into becoming a danger to public health.
Today, there are several dozens of journals publishing articles on alternative medicine. ‘The Journal of Alternative and Complementary Medicine’ is one of the best known, and it has one of the highest impact factors of them all. The current issue holds a few ‘gems’ which might be worthy of a comment or two. Here I have selected three articles reporting clinical studies, and I reproduce their abstracts (almost) in full (in italics) and add my comments (for clarity in bold). All the articles are available electronically, and I have provided the links for those who want to investigate beyond the abstracts.
STUDY No 1
The first ‘pilot study‘ was aimed to demonstrate the potential of auricular acupuncture (AAT) for insomnia in maintenance haemodialysis (MHD) patients and to prepare for a future randomized controlled trial.
Eligible patients were enrolled into this descriptive pilot study and received AAT designed to manage insomnia for 4 weeks. Questionnaires that used the Pittsburgh sleep quality index (PSQI) were completed at baseline, after a 4-week intervention, and 1 month after completion of treatment. Sleep quality and other clinical characteristics, including sleeping pills taken, were statistically compared between different time points.
A total of 22 patients were selected as eligible participants and completed the treatment and questionnaires. The mean global PSQI score was significantly decreased after AAT intervention (p<0.05). Participants reported improved sleep quality (p<0.01), shorter sleep latency (p<0.05), less sleep disturbance (p<0.01), and less daytime dysfunction (p=0.01). They also exhibited less dependency on sleep medications, indicated by the reduction in weekly estazolam consumption from 6.98±4.44 pills to 4.23±2.66 pills (p<0.01). However, these improvements were not preserved 1 month after treatment.
Conclusions: In this single-center pilot study, complementary AAT for MHD patients with severe insomnia was feasible and well tolerated and showed encouraging results for sleep quality.
In alternative medicine research, it has become far too common (almost generally accepted) to call a flimsy trial a ‘pilot study’. The authors give their game away by stating that, by conducting this trial, they want to ‘demonstrate the potential of AAT’. This is not a legitimate aim of research; science is for TESTING hypotheses, not for PROVING them!
The results of this trial show that patients experienced improvements after receiving AAT which, however, did not last. As there was no placebo control group, the most likely explanation for these outcomes would be that AAT generated a short-lasting placebo effect.
A sample size of 22 is, of course, far to small to allow any conclusions about the safety of the intervention. Despite these obvious facts, the authors seem convinced that AAT is both safe and effective.
STUDY No 2
The aim of the second study was to compare the therapeutic effect of Yamamoto new scalp acupuncture (YNSA), a recently developed microcupuncture system, with traditional acupuncture (TCA) for the prophylaxis and treatment of migraine headache.
In a randomized clinical trial, 80 patients with migraine headache were assigned to receive YNSA or TCA. A pain visual analogue scale (VAS) and migraine therapy assessment questionnaire (MTAQ) were completed before treatment, after 6 and 18 sections of treatment, and 1 month after completion of therapy.
All the recruited patients completed the study. Baseline characteristics were similar between the two groups. Frequency and severity of migraine attacks, nausea, the need for rescue treatment, and work absence rate decreased similarly in both groups. Recovery from headache and ability to continue daily activities 2 hours after medical treatment showed similar improvement in both groups (p>0.05).
Conclusions: Classic acupuncture and YNSA are similarly effective in the prophylaxis and treatment of migraine headache and may be considered as alternatives to pharmacotherapy.
This is what is technically called an ‘equivalence trial’, i.e. a study that compares an experimental treatment (YNSA) to one that is (assumed to be) effective. To demonstrate equivalence, such trials need to have large sample sizes, and this study is woefully underpowered. As it stands, the results show nothing meaningful at all; if anything, they suggest that both interventions were similarly useless.
STUDY No 3
The third study determined whether injection with hypertonic dextrose and morrhuate sodium (prolotherapy) using a pragmatic, clinically determined injection schedule for knee osteoarthritis (KOA) results in improved knee pain, function, and stiffness compared to baseline status.
The participants were 38 adults who had at least 3 months of symptomatic KOA and who were in the control groups of a prior prolotherapy randomized controlled trial (RCT) (Prior-Control), were ineligible for the RCT (Prior-Ineligible), or were eligible but declined the RCT (Prior-Declined).
The injection sessions at occurred at 1, 5, and 9 weeks with as-needed treatment at weeks 13 and 17. Extra-articular injections of 15% dextrose and 5% morrhuate sodium were done at peri-articular tendon and ligament insertions. A single intra-articular injection of 6 mL 25% dextrose was performed through an inferomedial approach.
The primary outcome measure was the validated Western Ontario McMaster University Osteoarthritis Index (WOMAC). The secondary outcome measure was the Knee Pain Scale and postprocedure opioid medication use and participant satisfaction.
The Prior-Declined group reported the most severe baseline WOMAC score (p=0.02). Compared to baseline status, participants in the Prior-Control group reported a score change of 12.4±3.5 points (19.5%, p=0.002). Prior-Decline and Prior-Ineligible groups improved by 19.4±7.0 (42.9%, p=0.05) and 17.8±3.9 (28.4%, p=0.008) points, respectively; 55.6% of Prior-Control, 75% of Prior-Decline, and 50% of Prior-Ineligible participants reported score improvement in excess of the 12-point minimal clinical important difference on the WOMAC measure. Postprocedure opioid medication resulted in rapid diminution of prolotherapy injection pain. Satisfaction was high and there were no adverse events.
Conclusions: Prolotherapy using dextrose and morrhuate sodium injections for participants with mild-to-severe KOA resulted in safe, significant, sustained improvement of WOMAC-based knee pain, function, and stiffness scores compared to baseline status.
This study had nothing that one might call a proper control group: all the three groups mentioned were treated with the experimental treatment. No attempt was made to control for even the most obvious biases: the observed effects could have been due to placebo or any other non-specific effects. The authors conclusions imply a causal relationship between the treatment and the outcome which is wrong. The notion that the experimental treatment is ‘safe’ is based on just 38 patients and therefore not reasonable.
All of this might seem rather trivial, and my comments could be viewed as a deliberate and vicious attempt to discredit one of the most respected journals of alternative medicine. Yet, considering that articles of this nature are more the rule than the exception in alternative medicine, I do think that this flagrant lack of scientific rigour is a relevant issue and has important implications.
As long as research in this area continues to be deeply flawed, as long as reviewers turn a blind eye to (or are not smart enough to detect) even the most obvious mistakes, as long as journal editors accept any rubbish in order to fill their pages, there is a great danger that we are being continuously being mislead about the supposed therapeutic value of alternative therapies.
Many who read this blog will, of course, have the capacity to think critically and might therefore not fall into the trap of accepting the conclusions of fatally flawed research. But many other people, including politicians, journalists and consumers, might not have the necessary appraisal skills and will thus not be able to tell that such studies can serve only one purpose: to popularise bogus treatments and thereby render health care less effective and more dangerous. Enthusiasts of alternative medicine are usually fully convinced that such studies amount to evidence and ram this pseudo-information down the throat of health care decision makers – the effects of such lobbying on public health can be disastrous.
And there is another downside to the publication of such dismal drivel: assuming (as I do) that not all of alternative medicine is completely useless, such embarrassingly poor research will inevitably have detrimental effects on the discipline of alternative medicine. After being exposed to a seemingly endless stream of pseudo-research, critics will eventually give up taking any of it seriously and might claim that none of it is worth the bother. In other words, those who conduct, accept or publish such nonsensical papers are not only endangering medical progress in general, they are also harming the very cause they try so desperately hard to advance.
A recent US study found that belief in conspiracy theories is rife in health care. The investigators presented people with 6 different conspiracy theories, and the one that was most widely believed was the following:
THE FOOD AND DRUG ADMINISTRATION IS DELIBERATELY PREVENTING THE PUBLIC FROM GETTING NATURAL CURES FOR CANCER AND OTHER DISEASES BECAUSE OF PRESSURE FROM DRUG COMPANIES.
A total of 37% agreed with this statement, 31% had no opinion on the matter, and 32% disagreed. What is more, the belief in this particular conspiracy correlated positively with the usage of alternative medicine.
Essentially, this implies that the current popularity of alternative medicine is at least partly driven by the conviction that there is a sinister plot by the FDA or more generally speaking ‘the establishment’ that prevents people from benefitting from the wonders of alternative treatments.
I think it was Woody Allen who noted that, just because you are paranoid does not mean that they are not following you. So, let’s look for evidence suggesting that the FDA or any similar organisation is suppressing alternative medicine.
A prime candidate is, of course, the often implicated, thoroughly evil ‘BIG PHARMA‘. I am not a fan of the pharmaceutical industry and I know few people who are. But where is the evidence for BIG PHARMA’s conspiracy against alternative medicine? In the many years of researching this sector, I have never come across a jot of evidence to support this notion. On the contrary, BIG PHARMA seems all to keen to jump on to the alternative bandwagon and make a few quick bucks from the gullibility of the consumer.
What about the rest of the medical establishment? All I see is that universities, hospitals, charities and other organisations in health care currently bend over backwards in order to accommodate as much alternative medicine as they possibly can get away with in view of the often embarrassing lack of convincing evidence for the treatments in question. Conspiracy against alternative medicine? I don’t think so.
The closer we look, the more we arrive at the conclusion that the conspiracy against alternative medicine is a myth and a figment of the imagination of those who religiously believe in alternative medicine. They seem to long for an explanation why their favourite therapy is not in even more wide-spread use. Cognitive dissonance seems to prevent them to consider that the lack of evidence has anything to do with this situation. Consequently, they prefer to invent a conspiracy theory.
And this is where an interesting question emerges, in my view: do people who believe that the FDA or other organisations prevent the public from getting more alternative medicine really need more alternative medicine, or do they perhaps just need an effective treatment for their paranoia?
I have often asked myself whether it is right/necessary to scientifically test things which are entirely implausible. Should we, for instance test the effectiveness of treatments which have a very low prior probability of generating a positive effect such as paranormal healing, homeopathy or Bach flower remedies? If you believe in the principles of evidence-based medicine you might focus on the clinical evidence and see biological plausibility as secondary. If you are a basic scientist, you are likely to do the reverse.
A recent article addressed this issue. The author points out that evaluating the absurd is absurd. Specifically, he noted that the empirical evaluation of a therapy would normally assume a plausible rationale regarding the mechanism of action. However, examination of the historical background and underlying principles for reflexology, iridology, acupuncture, auricular acupuncture, and some herbal medicines, reveals a rationale founded on the principle of analogical correspondences, which is a common basis for magical thinking and pseudoscientific beliefs such as astrology and chiromancy. Where this is the case, it is suggested that subjecting these therapies to empirical evaluation may be tantamount to evaluating the absurd.
This makes a lot of sense – but is it really entirely true? Are there no legitimate reasons at all for testing alternative treatments that lack biological plausibility? Ten or twenty years ago, I would have disagreed with the notion that plausibility is an essential prerequisite for scientific testing; today, I have changed my mind a little, but not as much as to agree completely with the assumption. In other words, I still see more than one good reason why evaluating the absurd might be reasonable or even advisable.
- Using plausibility as the only arbiter of scientific ‘evaluability’, assumes that we understand everything about plausibility there is to know. Yet it might just be possible that we mis-categorise something as implausible simply because we are not yet fully aware of all the facts.
- Declaring something as plausible and another thing as implausible are not hard and fast verdicts but judgements which, at least to some degree, are subjective. Sceptics find the axioms of homeopathy utterly implausible, for instance – but ask a homeopath, and you will hear all sorts of explanations which, at least to them, sound plausible.
- If an implausible alternative treatment is in wide-spread use, we arguably have a responsibility to test it scientifically in order to demonstrate the truth about it (to those proponents of that therapy who are willing to accept that rigorous science can find the truth). If we fail to do this, it will be the enthusiasts of that therapy who conduct less than rigorous science and produce false positive results. In turn, this will give the impression that the treatment is effective and mislead consumers, politicians, journalists etc. Seen from this perspective, it might even be unethical to not do the science.
So, I am in two minds about this (which might be a reflection of the fact that, during different periods of my life, I have been a clinician, a basic scientist and a clinical researcher). I realise that plausibility and prior probability are important – much more so than I appreciated years ago. But I think they should not be the only criteria. The clinical evidence should not be pushed aside completely.
I’d be interested to learn your views on this tricky issue.
An article in the ‘Huffpost Healthy Living’ recently discussed “the top three things that surprise people about acupuncture”. On closer inspection, they turn out to be the top three untruths about acupuncture. Here is (in italics and slightly abbreviated) what the article said.
Acupuncture is not just for pain
…It’s true that acupuncture can work wonders on pain conditions…However, acupuncture can alleviate a wide variety of ailments that have nothing to do with physical pain. Whether you have digestive issues, gynecological conditions, emotional concerns such as anxiety and depression, asthma, seasonal allergies, you name it, acupuncture can help address your symptoms.
Acupuncturists go to school for a long time
People tend to be unaware of the extent to which acupuncturists train to become licensed in their profession. Many assume becoming an acupuncturist is similar to becoming a massage therapist or Reiki practitioner or yoga instructor… At minimum, a licensed acupuncturist in the United States has been to three years of graduate school. Four years is more common. They hold master’s degrees. Some acupuncturists with doctorates have studied at the graduate level for five-plus years. Upon graduating from an accredited school, all acupuncturists must pass multiple board exams to become licensed in their state. In addition to the academic and state requirements for practicing acupuncture, many acupuncturists seek hands-on training and mentorship in the form of apprenticeships and continuing education seminars.
Acupuncture is relaxing
Acupuncture needles are surprisingly thin. They do not bear any resemblance to needles that are used for injections or to draw blood… In most cases, the insertion of acupuncture needles does not hurt…Once the needles are in, they start working their magic, which is where the relaxation part comes in. Acupuncture helps shift your body out of sympathetic mode (fight or flight) and into parasympathetic mode (rest and digest). It mellows out the nervous system, decreases muscular tension, and helps quiet internal chatter…
AND NOW THE FACTS:
1) There is not a single condition for which the evidence is truly compelling demonstrating that acupuncture is more than a placebo. Certainly there is no good evidence that acupuncture works for digestive issues, gynecological conditions, emotional concerns such as anxiety and depression, asthma or seasonal allergies.
2) In most countries, anyone can call themselves an acupuncturist, regardless of background or training.
3) The relaxing element of an acupuncture session is foremost the fact that patients lie down and have to keep still for 20 minutes or so. The insertion of needles does cause mild pain in many patients, and the claim about parasympathetic mode is mostly phantasy.
I despair about the nonsense that is published about alternative medicine on a daily basis – not because I have an axe to grind, but because it misleads patients into making wrong therapeutic decisions.
Guest Post by Jan Willem Nienhuys
The so-called Swiss government report of 2011 on homeopathy was actually an expanded translation of a 2006 book, which in itself was an expanded version of a document submitted to a Swiss committee (PEK) in charge of evaluation of alternative medicine. It has been severely criticised. A summary of criticisms with links can be found on the RationalWiki item to which we may add the Zeno’s Blog. I present here the results of my scrutiny of chapter 10 (1), although I base my report on the original German edition.
This chapter by itself shows a familiar result: the better the investigation, the less evidence in favor of homeopathy it shows. It shows also how homeopaths systematically distort unfavorable results by mispresenting them. Chapter 10 deals with clinical investigations of homeopathy. The authors restrict their attention to an odd assortment of diseases such as acute rhinitis, allergic rhinitis, allergic asthma, sinusitis, adenoid vegetations, pharyngitis, tonsillitis, influenza-like infection and otitis media, together denoted as ‘upper respiratory tract infections/allergic reactions’ or URTI/A for short.
The number of papers reviewed is very small. The authors looked at much more than randomized clinical trials. Apparently their search did not extend further than 2003, but then they might have found over 150 papers, of which about one third double blind randomized trials that compared how well highly diluted homeopathy and placebo cured one of the indicated diseases. They managed to miss 25 papers mentioned in earlier meta-analyses and about four papers that are summarized in Pubmed.
Among the papers they missed is an extremely strong support for the claim ‘homeopathy works for URTI/A’. For example Riverón-Garrote et al. (2) did a placebo controlled double blind randomized clinical trial of homeopathy (apparently individualised) for asthma. Of about 33 verum patients 32 improved, whereas of about 30 placebo patients only 4 improved. The so-called p-value for such a result is less than 10–11. One wonders why this result wasn’t published in Science or Nature, but only in an obscure Spanish language homeopathic journal. Maybe the paper was excluded because it didn’t state that it was about allergic asthma, but note that in about three quarters of all asthma some kind of allergy is implicated.
Of course this pales in comparison to the paper by Friese and Zabalotnyi (3). Again a double blind randomised clinical trial with 72 sinusitis sufferers for both verum and placebo. But here 71 out of 72 verum patients were free of complaints after three weeks, or at least improved, whereas this was the case for only 8 of the placebo patients. Fisher’s Exact Test gives p = 2.47 times 10-29 (one tailed). A remarkable result, because it is well known that over 80% of sinusitis cases cures spontaneously within two weeks. Maybe placebos are dangerous in the hands of homeopaths. Again one wonders why Friese and Zabalotnyi didn’t share the Nobel prize in, say, 2008, and why it is necessary at all to meticulously analyse papers in which homeopathy shows a marginal advantage.
Instead, Maxion-Bergemann et al. include in their survey a paper by Bahemann (4). We quote the summary of the paper from the internet: ‘In homeopathic practice, Kalium bromatum is known as a remedy in the case of paranoid delusions, e. g. if someone suffers from the delusion of being the object of divine revenge, of being damned, or of being pursued. It is also a very important remedy in the case of nocturnal fears in children as well as in the case of convulsions, when they are hereditary, when they occur in childbed, or during teething. The following case demonstrates the successful treatment of a severe mononucleosis after studying the Materia medica.’ Mononucleosis isn’t even mentioned in the list given that specifies URTI/A. Maybe it was included because one of the symptoms of mononucleosis is a sore throat. Apparently the mononucleosis patient was given Kalium Bromatum (Maxion-Bergemann et al. state that it is Kalium Chromatum 200C, presumably Chromatum and Bromatum don’t differ too much to bother) because of something remarkable the patient said during the anamnesis. The reason for giving Kalium bromatum 200C in cases of paranoia might be that an overdose of bromide can induce psychoses. The homeopathic Materia Medica contains quite a few ‘symptoms’ from accidental poisonings reported in old medical literature; potassium bromide was liberally used in the nineteenth century for the calming of seizure and nervous disorders, according to Wikipedia.
More impressive in the list of 13 RCTs of Maxion-Bergemann are two of the largest ‘homeopathic’ trials known, namely of the remedy Oscillococcinum. These trials cannot be taken seriously. The first one, by Ferley et al. (5), has one glaring fault. They started with 478 ‘influenza’-patients (237 verum), tried to make 149 family physicians note down when the patients recovered, and then elected to restrict their attention to the 63 patients (39 verum) that recovered within 48 hours and therefore probably didn’t have flu at all. Coincidentally this was the only possibility out of 14 that gave a ‘significant’ result: correctly computed, p is just below 0.05. (Ferley et al. based their computation on 462 patients with 228 verum and applied a chi-squared test without continuity correction). It is hardly credible that they set this 48-hour criterion in advance, because even if the remedy worked, the risk of having too few subjects to get a significant result would have been considerable. But if one picks out one result among many possibilities, one should correct for multiple outcome. So the Ferley et al. investigation is at most an exploratory result in need of independent confirmation.
This ‘confirmation’ was undertaken soon afterwards, namely in the beginning of 1991, but the results were only published in 1998 and cannot be found on Pubmed (6). In this paper the definitions are somewhat different, but Papp et al. report that of 334 patients (167 verum) a total of 57 (32 verum) were cured in 48 hours. Now 25 versus 32 is not remarkable at all. One doesn’t need any elaborate computation for this. Calculation gives p=0.4. So one might think that the Ferley hypothesis was soundly refuted. But Papp et al. used something they call ‘the Krauth test’, probably some kind of automated post hoc fishing trip to select the best criteria to distinguish the placebo and verum groups. They claim that this ‘test’ gives p=0.0028. They specifically refer to ‘the null hypothesis (the number of patients free of symptoms after 48 hours is equal in both treatment groups)’, so their computation is wrong. The most remarkable thing about Papp et al. is that nobody seems to have to have noticed the large discrepancy between what the numbers say and the claim of the paper.
Another paper with ‘positive’ results is the 1994 study of Reilly et al. (7), number 28 in Maxion-Bergemann et al. The group of Reilly investigated allergic diseases treated by what they called homeopathy. The typical Reilly experiment consists of administering a highly diluted causative agent such as pollen or house dust mite or cat hairs or bird feathers to persons suffering from pollen allergy (seasonal rhinitis) or allergic asthma. However for true homeopathy one uses a substance that has been the subject of a so-called proving, and the remedy is chosen of the totality of all patient ‘symptoms’ – including things like sleeping position and fear of thunderstorms – sufficiently matches the symptoms of the proving. Let me call Reilly’s method ultra-isopathy. Reilly was already discussing this study on a symposium in 1990, but that paper is not clear. It is about 28 asthma patients, and only 24 were analysed. This small number in itself is already reason enough not to consider it. The main analysis was by comparing a subjective measure of wellbeing, the Visual Analog Scale (VAS). Here we find a significant difference (p=0.003) in favor of ultra-isopathy. However, in the small print we see that change in the very important FEV1-value (Forced Expiratory Volume in 1 second) was non-significant (p=0.08) but this refers only to the 18 patients that took such a test before and after the experiment.
Reilly attracted more attention with his first experiment in this vein (8). He started out with 79 patients in both the verum and the placebo group. The treatment was ultradiluted grass pollen for hay fever. The analysis was only about 56 verum and 52 placebo (in a diagram 53 placebo are shown). Such a large dropout (32%) is not good. On basis of the VAS-scores Reilly found p=0.02. VAS is only an ordinal scale and it is not at all clear that one person’s 60 mm means the same as another person’s 60 mm, and also not that two patients with respectively 40 mm and 80 mm together can be considered as equivalent to two other patients with 60 mm each. If we distinguish only better / equal / worse, then the numbers for the verum group were 34 / 9 / 13 and for the placebo group 27 / 5 / 21. One can analyse this in various ways: as a 3 by 2 contingency table (p=0.15), or as a 2 by 2 table, namely by joining the middle group either to the right (p=0.10) or to the left (p=0.34). In this manner the difference is less impressive.
Maxion-Bergemann et al. collected 29 articles. I take the liberty of removing from these everything that is not a double blind RCT that compares how well highly diluted homeopathy and placebo cures an URTI/A disease. We also remove all research with 50 or less patients. The more or less openly fraudulent or at least grossly mistaken Oscillococcinum trials I also leave out. In order of appearance we have then Wiesenauer 1985 (9)  Reilly 1986 (8)  Wiesenauer 1989 (10)  De Lange-de Klerk 1994 (11)  Aabel 2000 (12)  Jacobs 2001 (13)  Friese 2001 (14)  Lewith 2002 (15)  White 2003 (16)  The square brackets refer to the numbering in Maxion-Bergemann et al. A short review of these nine articles follows.
Wiesenauer 1985: one standard remedy for hayfever. Randomised 213 patients, analysed only 164. “no statistical significance was achieved” says the abstract on Pubmed. Reilly 1986: this we have discussed already. Ultra-isopathy for hayfever. Randomised 158 patients, analysed 108. Statistically significant, but barely so. Wiesenauer 1989: four groups, each with their own standard remedy or placebo for sinusitis, 152 patients. “There was no remarkable difference in the therapeutic success among the investigated homeopathic drug combinations nor between the active drugs and placebo”, according to the abstract in Pubmed De Lange-de Klerk 1994: this research was reported more extensively in the lead author’s dissertation (17). Individualised homeopathy for recurrent URTI in children. 175 children were randomised and 170 analysed after following them for a year. 128 different remedies/potencies were prescribed and all together 1042 different prescriptions were handed out. The result was a non-significant difference between homeopathy and placebo. One striking aspect of this investigation is that only after all computations were done, it was revealed which of the two groups was the placebo group and which the verum group. So the author or her thesis advisors deliberately made it impossible to fall for the temptation to start a fishing expedition in the data after the code was completely broken. See also Pubmed. Aabel 2000: ultra-isopathy for birch pollen allergy. Strictly speaking this investigation shouldn’t be in this short list because it was partly prophylactic. From Pubmed: “Surprisingly, the verum treated patients fared worse than the placebo group”. No measure of statistical significance is mentioned. Remarkably this article is preceded by a similar article (18) that Maxion-Bergemann et al. apparently weren’t able to locate. Jacobs 2001: 75 children with otitis media were treated with individualised homeopathy or placebo. Pubmed: “differences were not statistically significant”. It seems that Jacobs has indulged in a fishing trip because she mentions a “significant decrease in symptoms at 24 and 64 h after treatment in favor of homeopathy”. But that is wrong. Significance only can have a meaning if it refers to a single outcome that was planned before any patients were seen. Just picking out two results out of many and stating they are ‘significant’ betrays a fundamental ignorance of research methodology. Friese 2001: this article is also published elsewhere (19), at least the numbers are exactly the same according to Pubmed. 97 children randomized for either individual homeopathic treatment or placebo treatment of adenoid vegetations, 82 analysed. Apparently these 82 comprised 41 placebo and 41 verum, and of these 12 and 9 respectively required an operation in the end. This allegedly corresponds to p=0.64, “These results show no statistical significance.” Incidentally, this is the same Friese as reference 3. Lewith 2002: again ultra-isopathy, now for asthma, 242 patients randomised, 202 completed all clinical assessments. The full article can be accessed via Pubmed and elsewhere. The main conclusion is “Homoeopathic immunotherapy is not effective in the treatment of patients with asthma.” The authors notice that the averages in both groups behave somewhat erratic, and they have no explanation for this. White 2003: individualised homeopathy compared to placebo for 96 children with asthma, who are followed for 12 months. The conclusion is that there is no evidence that this kind of homeopathy is better than placebo. In other words, out of nine investigations only one (Reilly 1986) obtains a barely significant result.
But the interpretation of Maxion-Bergemann et al. is totally different: “If only the placebo-controlled, randomized trials with the highest EBM evidence are considered, 12 of 16 trials show a positive result for the homeopathically treated group (significantly positive 8/16 and trend 4/16).” Even in the more restricted subset of nine discussed above they are overly optimistic. They mark Wiesenauer (1985), De Lange-de Klerk (1994), Jacobs (2001) as showing a ‘trend for homeopathy’ and Lewith (2002) is even marked ‘significant’. The meticulous and high quality research of De Lange (1993, 1994) is judged ‘trend for homeopathy’.
In case of De Lange it seems clear where this judgement comes from. De Lange had several outcomes (number of sick periods, total duration of sick periods, sum of all dayscores etc., and all these showed roughly the same small non-significant difference in favor of homeopathy. This is not really strange, because these outcomes all measure about the same phenomenon. It is not remarkable that there is a small difference between the averages of the two groups that can only be noticed if the children are followed for a full year. There is not even the beginning of a reason that this has anything to do with the treatment. For example the homeopathy group had ‘significantly’ less pets at home. This might serve as an explanation why they as a group were slightly less sick. One might also speculate that this was retroactively caused by the homeopathic treatment. This is not really more improbable than highly diluted stuff (more than 95% D6 and higher) having an effect.
By convention ‘statistically significant’ is the lower limit where weak conclusions such as ‘worth investigating further’ can be justified, and we repeat: only if it refers to a single outcome measure or endpoint chosen before any data collection has started. De Lange chose recurrent URTI because homeopathy was reputed to be most effective for this type of complaints, especially after investigations such as those of Reilly (1986). If following 170 children for a full year cannot show a clear advantage, then that is simply a negative result. In the case of Lewith the ‘significant for homeopathy’ is probably based on partial results such as that in week 3 ‘homeopathy’ fared better in the asthma VAS. One can just as well point to week 16 where the FEV1 of the placebo group seems much better than in the homeopathy group.
Maxion-Bergemann et al. seem to have been singularly inept in collecting papers on homeopathic trials, and for no apparent reason they decided to look also at a large number of case reports and investigations without control group or blinding, even after investigators as early as 1991 have remarked that henceforth only well designed large double blind RCTs were worth considering. If we restrict our attention to the properly blinded controlled investigations, we see the same thing as in other meta-analyses of homeopathy: there is lots of rubbish in favor of homeopathy, but the good trials say plainly and clearly: homeopathy is ineffective, precisely what can be predicted from the fact that there is nothing in it.
Homeopaths nowadays have a lot to say about RCTs and how they prove homeopathy. RCTs are subtle and complicated scientific tools. It is somewhat strange to see how homeopaths resolutely ignore two centuries of basic science but then argue their cause on the basis of complicated statistics.
Homeopathy is an assortment of wildly different practices and theories. We have seen ultra-isopathy, individualised homeopathy and the practice of giving one standardised remedy for one diagnosis without asking too many personal details from the patient. These standard remedies are often branded mixtures of highly diluted ‘classical’ homeopathy, quite contrary to the opinions of homeopathy’s inventor Hahnemann. There are many more variants of homeopathy and the homeopaths themselves cannot agree which are the correct ones.
Moreover, if a treatment or trial doesn’t work out, then a number of additional hypotheses about homeopathy can be invoked, which is what Maxion-Bergemann et al. do. Homeopathic remedies supposedly are counteracted by lots of regular medications and even by strong tasting or smelling food, such as coffee, parsley, garlic and peppermint. Hahnemann even disapproved of reading in bed and long afternoon naps and prolonged suckling of infants (Organon, section 260). Poor performance of homeopathy can be blamed on something called ‘initial aggravation’ or else on lack of experience of the poorly performing homeopath.
But that these factors are relevant at all is unknown, just like there is no proof at all for the similia principle, nor for the hundred thousands or even millions of ‘symptoms’ associated with highly diluted materials in the homeopathic Materia Medica. If homeopaths really want scientists to share homeopathic beliefs, they should not think up lame excuses for ‘failed’ tests, but for starters they might try to present proofs for all or at least some of their ‘symptoms’. They don’t try very hard and in so far it has been tried, it also has failed (20).
I would like to thank Willem Betz for helpful remarks.
I am a retired mathematician with no other interest than a desire to promote science.
1. Stefanie Maxion-Bergemann, Gudrun Bornhöft, Denise Bloch, Christina Vogt-Frank, Marco Righetti, André Thurneysen. (2011) Clinical Studies on the Effectiveness of Homeopathy for URTI/A (Upper Respiratory Tract Infections and Allergic Reactions) in: Homeopathy in Healthcare – Effectiveness, Appropriateness, Safety, Costs. G. Bornhöft and P.F. Mattheiesen (eds.), Berlin etc., Springer 2011, p. 18-157.
2. Riverón-Garrote, M., Fernandez-Argüelles, R.; Morán-Rodríquez, F.; Campistrou-Labaut, J.L. (1998) Ensayo clínico controlado aleatorízado del tratamiento homeopático del asma bronquial, Boletín Mexicano de Homepatía 1998; 31(2):54-61.
3. Friese, K.-H., Zabalotnyi, D.I. (2007) Homöopathie bei akuter Rhinosinusitis, Eine doppelblinde, placebokontrollierte Studie belegt die Wirksamkeit und Verträglichkeit eines homöopathischen Kombinationsarzneimittels, HNO 55(4):271-277.
4. Bahemann A. (2002) Kalium bromatum bei infektiöser Mononukleose. Zeitschrift für Klassische Homöopathie 46:232–233.
5. Ferley J.P., Zmirou D., D’Adhemar D., Balducci F. (1989). A controlled evaluation of a homoeopathic preparation in the treatment of influenza like syndromes. British Journal of Clinical Pharmacology 27:329-335.
6. Papp R., Schuback G., Beck E., Burkard G., Bengel J., Lehrl S., Belon P. (1998). Oscillococcinum in patients with influenza-like syndromes: a placebo-controlled double-blind evaluation. British Homeopathic Journal 87:69-76.
7. Reilly, D.T., Taylor, M.A., Beattie, N.G.M., Campbell, J.H., McSharry C., Aitchison T.C., Carter R., Stevenson R. (1994) Is evidence for homoeopathy reproducible?, Lancet 1994 344:1601-1606.
8. Reilly, D.T., Taylor, M.A., McSharry, C., Aitchison, T. (1986) Is Homoeopathy a Placebo Response?, Controlled Trial of Homoeopathic Potency – With Pollen in Hayfever as Model, Lancet II.2:881-886.
9. Wiesenauer, M., Gaus, W. (1985) Double-blind Trial Comparing the Effectiveness of Galphimia Potentisation D6 (Homoeopathic Preparation), Galphimia Dilution 10-6 and Placebo on Pollinosis, Arzneimittelforschung 35(11):1745-1747.
10. Wiesenauer M, Gaus W, Bohnacker U, Häussler S (1989) Wirksamkeitsprüfung von homöopathischen Kombinationspräparaten bei Sinusitis: Ergebnisse einer randomisierten Doppelblindstudie unter Praxisbedingungen. Arzneimittelforschung 39:620-625.
11. de Lange-de Klerk E.S.M., Blommers J., Kuik D.J., Bezemer P.D., Feenstra L. (1994). Effects of homoeopathic medicines on daily burden of symptoms in children with recurrent upper respiratory tract infections. BMJ 309:1329-1332.
12. Aabel, S. (2000) No beneficial effect of isopathic prophylactic treatment for birch pollen allergy during a low-pollen season, A double-blind, placebo-controlled clinical trial of homeopathic Betula 30c. British Homeopathic Journal 89(4):169-173.
13. Jacobs, J., Springer, D.A., Crothers, D. (2001) Homeopathic treatment of acute otitis media in children, A preliminary randomized placebo-controlled trial. The Pediatric Infectious Disease Journal 20(2):177-183.
14. Friese K.H., Feuchter U., Lüdtke R., Moeller H. (2001) Results of a randomised prospective double-blind trial on the homeopathic treatment of adenoid vegetations. European Journal of General Practice 7:48-54.
15. Lewith, G.T., Watkins, A.D.; Hyland, M.E.; Shaw, S.; Broomfield, J.A.; Dolan, G.; Holgate, S.T. (2002) Use of ultramolecular potencies of allergen to treat asthmatic people allergic to house dust mite: double blind randomised controlled clinical trial, BMJ 324:520-523.
16. White, A., Slade, P.; Hunt, C.; Hart, A.; Ernst, E. (2003) Individualised homeopathy as an adjunct in the treatment of childhood asthma, A randomised placebo controlled trial. Thorax 58(4):317-321
17. Lange-de Klerk, E.S.M. de, Effects of homoeopathic medicines on children with recurrent upper respiratory tract infections. Vrije Universiteit Amsterdam, 1993 (Dissertation).
18. Aabel, S., Laerum, E.; Dölvik, S.; Djupesland, P. (2000) Is homeopathic ‘immunotherapy’ effective?, A double-blind, placebo-controlled trial with the isopathic remedy Betula 30c for patients with birch pollen allergy. British Homeopathic Journal 89(4):161-168.
19. Friese K.-H., Feuchter U., Möller H. (1997). Die homöopathische Behandling von adenoiden Vegetationen. HNO; 45:618–624.
20. Brien S., Lewith G., Bryant, T. (2003) Ultramolecular homeopathy has no observable clinical effects. A randomized, double-blind, placebo-controlled proving trial of Belladonna 30C.
A recent meta-analysis evaluated the efficacy of acupuncture for treatment of irritable bowel syndrome (IBS) and arrived at bizarrely positive conclusions.
The authors state that they searched 4 electronic databases for double-blind, placebo-controlled trials investigating the efficacy of acupuncture in the management of IBS. Studies were screened for inclusion based on randomization, controls, and measurable outcomes reported.
Six RCTs were included in the meta-analysis, and 5 articles were of high quality. The pooled relative risk for clinical improvement with acupuncture was 1.75 (95%CI: 1.24-2.46, P = 0.001). Using two different statistical approaches, the authors confirmed the efficacy of acupuncture for treating IBS and concluded that acupuncture exhibits clinically and statistically significant control of IBS symptoms.
As IBS is a common and often difficult to treat condition, this would be great news! But is it true? We do not need to look far to find the embarrassing mistakes and – dare I say it? – lies on which this result was constructed.
The largest RCT included in this meta-analysis was neither placebo-controlled nor double blind; it was a pragmatic trial with the infamous ‘A+B versus B’ design. Here is the key part of its methods section: 116 patients were offered 10 weekly individualised acupuncture sessions plus usual care, 117 patients continued with usual care alone. Intriguingly, this was the ONLY one of the 6 RCTs with a significantly positive result!
The second largest study (as well as all the other trials) showed that acupuncture was no better than sham treatments. Here is the key quote from this trial: there was no statistically significant difference between acupuncture and sham acupuncture.
So, let me re-write the conclusions of this meta-analysis without spin, lies or hype: These results of this meta-analysis seem to indicate that:
- currently there are several RCTs testing whether acupuncture is an effective therapy for IBS,
- all the RCTs that adequately control for placebo-effects show no effectiveness of acupuncture,
- the only RCT that yields a positive result does not make any attempt to control for placebo-effects,
- this suggests that acupuncture is a placebo,
- it also demonstrates how misleading studies with the infamous ‘A+B versus B’ design can be,
- finally, this meta-analysis seems to be a prime example of scientific misconduct with the aim of creating a positive result out of data which are, in fact, negative.
Homeopathy is a deeply puzzling subject for many observers. Perhaps it gets a little easier to understand, if we consider the three main perspectives on homeopathy. For the purpose of this post, I take the liberty of exaggerating, almost caricaturizing, these perspectives in order to contrast them as clearly as possible.
THE SCEPTICS’ PERSPECTIVE
Sceptics take a brief look at the two main assumptions which underpin homeopathy (like cures like and potentiation/dilution/water memory) and henceforward are convinced that homeopathic remedies are pure placebos. Homeopathy flies in the face of science; if homeopathy is right, several laws of nature must be wrong, they love to point out. As this is most unlikely, they reject homeopathy outright, usually even without looking in any detail at what homeopaths consider to be evidence in support of their trade. If sceptics are forced to consider a positive study of homeopathy, they know before they have seen it that its results are wrong – due to an error caused by chance, faulty study design or fabrication. The sceptics’ conclusion on homeopathy: it is a placebo-therapy, no doubt about it; and further investment into research is a waste of scarce resources which must be stopped.
THE BELIEVERS’ PERSPECTIVE
The believers in homeopathy know from experience that homeopathy works. They therefore feel that they have no choice but to reject almost every word the sceptics might tell them. They cling on to the gospel of Hahnemann and elaborate on the modern but vague theories that might support the theoretical assumptions of homeopathy. They point to positive clinical trials and outcome studies, to 200 years of experience, and to the endorsement of homeopathy by VIPs. When confronted with the weaknesses of their arguments, they find even weaker ones, such as ‘much of conventional medicine is also not based on good evidence, and the mechanism of action of many mainstream drugs is also not fully understood’. Alternatively, they employ the phoniest argument of them all: ‘even if it works via a placebo effect, it still helps patients and therefore is a useful therapy’. When even this fails, they tend to resort to ad hominem attacks against their opponents. The believers’ conclusion on homeopathy: it is unquestionably a valuable type of therapy regardless of what anyone else might say; research is merely needed to confirm their belief.
THE PERSPECTIVE OF THE ADVOCATES OF EVIDENCE-BASED MEDICINE (EBM)
The perspective of EBM-advocates is pragmatic; they simply say: “show me the evidence!” If the majority of the most reliable clinical trials of homeopathic remedies (or anything else) suggests an effect beyond placebo, they conclude that they are effective. If that is not the case, they doubt the effectiveness. If the evidence is highly contradictory or incomplete, they are likely to advocate more rigorous research. Advocates of EBM are usually not all that concerned by the lack of plausibility of the interventions they evaluate. If it works, it works, they think – and if a plausible mechanism is currently not available, it might be found in due course. The advocates of EBM have no preconceived ideas about homeopathy. Their conclusion on homeopathy goes exactly where the available best evidence leads them.
The arguments and counter-arguments originating from the various perspectives would surely continue for another 200 years – unless, of course, two of the three perspectives merge and arrive at the same or very similar conclusions. And this is precisely what has now happened. As I have pointed out in a recent post, the most thorough and independent evaluation of homeopathy according to rigorous EBM-standards has concluded that “the evidence from research in humans does not show that homeopathy is effective for treating the range of health conditions considered.”
In other words, two of the three principal perspectives have now drawn conclusions which are virtually identical: there is a consensus between the EBM-advocates and the sceptics. This isolates the believers and renders their position no longer tenable. If we furthermore consider that the believers are heavily burdened with obvious conflicts of interest, while the other two groups are by definition much more independent and objective, it appears more and more as though homeopathy is fast degenerating into a cult characterised by the unquestioning commitment and unconditional submission of its members who are too heavily brain-washed to realize that their fervour has isolated them from the rational sections of society. And a cult is hardly what we need in heath care, I should think.
It seems to me therefore that these intriguing developments might finally end the error that homeopathy represented for nearly 200 years.
Progress at last?