MD, PhD, FMedSci, FRSB, FRCP, FRCPEd

bias

If we search on ‘Medline’ for ‘complementary alternative medicine’ (CAM), we currently get about 13000 hits. A little graph on the side of the page demonstrates that, during the last 4 years, the number of articles on this subject has grown exponentially.

Surely, this must be very good news: such intense research activity will soon tell us exactly which alternative treatments work for which conditions and which don’t.

I beg to differ. Let me explain why.

The same ‘Medline’ search informs us that the majority of the recent articles were published in an open access journal called ‘Evidence-Based Complementary and Alternative Medicine’ (eCAM). For example, of the 80 most recent articles listed in Medline (on 26/5/2014), 53 came from that journal. The publication frequency of eCAM and its increase in recent years beggars belief: in 2011, they published just over 500 articles which is already a high number, but, in 2012, the figure had risen to >800, and in 2013 it was >1300 (the equivalent 2013 figure for the BMJ/BMJ Open by comparison is 4, and that for another alt med journal, e.g. Forsch Komplement, is 10)

How do they do it? How can eCAM be so dominant in publishing alt med research? The trick seems to be fairly simple.

Let’s assume you are an alt med researcher and you have an article that you would like to see published. Once you submit it to eCAM, your paper is sent to one of the ~150 members of the editorial board. These people are almost all strong proponents of alternative medicine; critics are a true rarity in this group. At this stage, you are able to suggest the peer reviewers for your submission (all who ever accepted this task are listed on the website; they amount to several thousand!), and it seems that, with the vast majority of submissions, the authors’ suggestions are being followed.

It goes without saying that most researchers suggest colleagues for peer reviewing who are not going to reject their work (the motto seems to be “if you pass my paper, I will pass yours). Therefore even faily flimsy bits of research pass this peer review process and get quickly published online in eCAM.

This process explains a lot, I think: 1) the extraordinarily high number of articles published 2) why currently more than 50% of all alt med research originate from eCAM 3) why so much of it is utter rubbish.

Even the mere titles of some of the articles might demonstrate my point. A few examples have to suffice:

  • Color distribution differences in the tongue in sleep disorder
  • Wen-dan decoction improves negative emotions in sleep-deprived rats by regulating orexin-a and leptin expression.
  • Yiqi Huoxue Recipe Improves Heart Function through Inhibiting Apoptosis Related to Endoplasmic Reticulum Stress in Myocardial Infarction Model of Rats.
  • Protective Effects of Bu-Shen-Huo-Xue Formula against 5/6 Nephrectomy-Induced Chronic Renal Failure in Rats
  • Effects and Mechanisms of Complementary and Alternative Medicine during the Reproductive Process
  • Evidence-based medicinal plants for modern chronic diseases
  • Transforming Pain into Beauty: On Art, Healing, and Care for the Spirit

This system of uncritical peer review and fast online publication seems to suit many of the people involved in this process: the journal’s owners are laughing all the way to the bank; there is a publication charge of US$ 2000 per article, and, in 2013, the income of eCAM must therefore have been well over US$2 000 000. The researchers are equally delighted; they get even their flimsiest papers published (remember: ‘publish or perish’!). And the evangelic believers in alternative medicine are pleased because they can now claim that their field is highly research-active and that there is plenty of evidence to support the use of this or that therapy.

But there are others who are not served well by eCAM habit of publishing irrelevant, low quality articles:

  • professionals who would like to advance health care and want to see reliable evidence as to which treatments work and which don’t,
  • the public who, in one way or another, pay for all this and might assume that published research tends to be relevant and reliable,
  • the patients who have given their time to researchers in the hope that their gift will improve health care,
  • ill individuals who hope that alternative treatments might relieve their suffering,
  • politicians who rely on research to be reliable in order to arrive at the right decisions.

Come to think of it, the vast majority of people should be less than enchanted with eCAM and similar journals.

Boiron is the world’s biggest producer of homeopathic remedies. It also is a firm that is relatively active in research into homeopathy. Here is one of their investigations which I find most remarkable.

This study was designed to describe the sociodemographic and clinical characteristics of patients recommended allopathic and/or homeopathic medicines for influenza-like illness (ILI) or ear nose and throat ENT disorders by pharmacists in France and to investigate the effectiveness of these treatments.

The introduction of the article includes interesting information; it informs us that, although homeopathy is more popular in Europe than in the Unites States, sales of homeopathic medicines in the United States grew by more than 1,000% in the late 1970s and early 1980s and continue to grow. In parallel, the number of physicians specializing in homeopathy doubled between 1980 and 1982. In 2003, sales of homeopathic medicines in the United States were estimated to be between $300 and $450 million, with an average growth rate of approximately 8% per year. Homeopathic drugs are among the top 10 nonprescription products sold in the category of analgesics to treat coughs, colds, and flu. The sale of homeopathic medicines in the United States is controlled by the Food, Drug, and Cosmetic Act and regulations issued by the U.S Food and Drug Administration (FDA). Homeopathic medicines in the United States are subject to well-controlled regulatory processes that closely resemble those used for allopathic medicines. FDA regulations for the sale of homeopathic medicines in the United States state that they can only be sold without prescription if they are for self-limiting conditions such as the common cold…

Am I mistaken, or does that paragraph read a bit like a text written by the marketing team of Boiron wanting to establish their products in the US?

Anyway, the methodology and results of the study are described in the abstract as follows:

A prospective, observational, multicenter study was carried out in randomly selected pharmacies across the 8 IDREM medical regions of France. Pharmacies that agreed to participate recruited male or female patients who responded to the following inclusion criteria: age ≥ 12 years presenting with the first symptoms of an ILI or ENT disorder that were 
present for less than 36 hours prior to the pharmacy visit. All medicines recorded in the study were recommended by the pharmacists. The following data were recorded at inclusion and after 3 days of treatment: the intensity of 13 symptoms, global symptom score, and disease impact on daily activities and sleep. Two groups of patients were compared: those recommended allopathic medicine only (AT group) and those recommended homeopathic medicine with or without allopathic medicine (HAT group). The number and severity of symptoms, change in global symptom score, and disease impact on daily activities and sleep were compared in the 2 treatment groups after 3 days of treatment. Independent predictors of recommendations for homeopathic medicine were identified by multi-
factorial logistic regression analysis.

A total of 242 pharmacies out of 4,809 (5.0%) contacted agreed to participate in the study, and 133 (2.8%) included at least 1 patient; 573 patients were analyzed (mean age: 42.5 ± 16.2 years; 61.9% female). Of these, 428 received allopathic medicines only (74.7%; AT group), and 145 (25.3%) received homeopathic medicines (HAT group) alone (9/145, 1.6%) or associated with allopathy (136/145, 23.7%). At inclusion, HAT patients were significantly younger (39.6 ± 14.8 vs. 43.4 ± 16.1 years; P  less than  0.05), had a higher mean number of symptoms (5.2 ± 2.5 vs. 4.4 ± 2.5; P  less than  0.01), and more severe symptoms (mean global symptom score: 24.3 ± 5.5 vs. 22.3 ± 5.8; P = 0.0019) than AT patients. After 3 days, the improvement in symptoms and disease impact on daily activities and sleep was comparable in both groups of patients.

From these findings, the authors draw the following conclusions: Patients recommended homeopathic medicine by pharmacists were younger and had more severe symptoms than those recommended allopathic medicine. After 3 days of treatment, clinical improvement was comparable in both treatment groups. Pharmacists have an important role to play in the effective management of ILI and ENT disorders.

And, to make perfectly clear what all this is about, the first sentence of the ‘discussion’ puts it to the point by stating that homeopathic medicine, with or without allopathic medicine, appears to be effective at alleviating the symptoms of ILI or ENT disorders.

Oh really?

As I have heard it said that Boiron seems to have the nasty habit of threatening their critics with legal action, I ought to be quite cautious in my assessment of this ‘masterpiece of promotion’. Yet a few comments must surely be permitted.

‘To describe the sociodemographic and clinical characteristics of patients recommended allopathic and/or homeopathic medicines’ is not what I personally find an interesting subject of research, nor is it anything that will affect health care meaningfully, I think. Yet ‘to investigate the effectiveness of these treatments’ is certainly interesting and important. I will therefore focus on this second aim of the study.

Hold on, was this really a ‘study’? On closer inspection, it seemed much more like a survey. People who felt that they were suffering from ILI and ENT disorders and thus went to a pharmacy to buy something for their problem were offered either homeopathic or conventional medicines. Those who accepted either of the recommendations were asked to fill out some self-assessment forms and received a phone call three days later to check their symptoms. 94% of all patients in the homeopathy group took homeopathic medicine in combination with ‘allopathic’ medicine (it is interesting, perhaps even telling, that this term used by the authors was invented by Hahnemann as an insult to conventional medicine!). There was no examination by a doctor to verify what condition the survey-participants were truly suffering from, and there was no verification that the information provided during the follow-up telephone call was in any way real. The most frequently recommended homeopathic medicine was Anas barbariae 200C (Oscillococcinum) which is Boiron’s famous homeopathically diluted (about one molecule per universe, I guess) duck-liver heavily promoted in France against colds and similar conditions.

As it turns out, those survey-participants who accepted the homeopathic recommendation were significantly younger than those who accepted the recommendation for a conventional treatment (many surveys confirm that younger people are more prone to trying alternative medicine than older ones). It stands to reason, that the younger (and therefore fitter) patients were in better general health and therefore might recover quicker than the older ones. But, in fact, they did not!

Could this be due to the homeopathic remedies actually delaying recovery? Of course not! Who would be silly enough to claim that homeopathy could have this (or any other) effect? According to the authors, it is due to the fact that this group ‘had more severe symptoms than those recommended allopathic medicine’. But, as I said, we have to take their word for it; there is no independent verification of this. It would, of course, be quite ridiculous to postulate that those survey-participants accepting homeopathy were also a little more introspective or concerned about their own health (perhaps even more gullible) and thus claimed more severe symptoms!

And what about the authors’ conclusion that clinical improvement was comparable in both treatment groups? Well, this is more than a little problematic, in my view: first, we have no independent verification of the ‘improvement’ in either group. Second, we don’t know that the conventional treatments actually worked, and it could well be that both approaches were similarly ineffective, and that the observed outcomes are merely a reflection of the natural history of the condition. And third, one might expect the homeopathic (younger) group to do not similarly well but slightly better, simply because the natural history of the illness would tend to be more benign in younger people.

Before I finish,I should make a brief comment about the authors’ courageous statement that  homeopathic medicine, with or without allopathic medicine, appears to be effective at alleviating the symptoms of ILI or ENT disorders. I think, for the reasons I already provided, this is extremely doubtful. In my view, more critical scientists would have phrased the conclusions differently:

THIS SURVEY SHOWS THAT EVALUATING THE EFFECTIVENESS OF MEDICAL INTERVENTIONS REQUIRES A MORE RIGOROUS METHODOLOGY THAN THAT OF A SURVEY.

But perhaps this would be asking a little too much of the authors; after all, at the end of the article, we find this telling footnote: Laboratoires Boiron provided financial support for the study. Cognet-Dementhon, Thevenard, Duru, and Allaert received consulting fees from Laboratoires Boiron for this study. Danno and Bordet are employees of Laboratoires Boiron.

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.

My comments:

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.

My comments:

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.

My Comments:

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.

IMPLICATION

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.

  1. 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.
  2. 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.
  3. 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) [8] Reilly 1986 (8) [6] Wiesenauer 1989 (10) [10] De Lange-de Klerk 1994 (11) [1] Aabel 2000 (12) [4] Jacobs 2001 (13) [22] Friese 2001 (14) [24] Lewith 2002 (15) [25] White 2003 (16) [29] 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.

References

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.

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