MD, PhD, FMedSci, FSB, FRCP, FRCPEd

false positive

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

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

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

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

Really? I am afraid, I disagree!

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

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

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

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

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

Readers of this blog will know that few alternative treatments are more controversial and less plausible than homeopathy. Therefore they might be interested to read about the latest attempt of homeopathy-enthusiasts to convince the public that, despite all the clinical evidence to the contrary, homeopathy does work.

The new article was published in German by Swiss urologist and is a case-report describing a patient suffering from paralytic ileus. This condition is a typical complication of ileocystoplasty of the bladder, the operation the patient had undergone. The patient had also been suffering from a spinal cord injury which, due to a pre-existing neurogenic bowel dysfunction, increases the risk of paralytic ileus.

The paraplegic patient developed a massive paralytic ileus after ileocystoplasty and surgical revision. Conventional stimulation of bowel function was unsuccessful. But after adjunctive homeopathic treatment normalization of bowel function was achieved.

The authors conclude that adjunctive homeopathic therapy is a promising treatment option in patients with complex bowel dysfunction after abdominal surgery who do not adequately respond to conventional treatment.

YES, you did read correctly: homeopathic therapy is a promising treatment

In case anyone doubts that this is more than a trifle too optimistic, let me suggest three much more plausible reasons why the patient’s bowel function finally normalised:

  • It could have been a spontaneous recovery (in most cases, even severe ones, this is what happens).
  • It could have been all the conventional treatments aimed at stimulating bowel function.
  • It could have been a mixture of the two.

The article made me curious, and I checked whether the authors had previously published other material on homeopathy. Thus I found two further articles in a very similar vein:

Article No 2 (dated 2014):

We present the clinical course of a patient with an epididymal abscess caused by multiresistant bacteria. As the patient declined surgical intervention, a conservative approach was induced with intravenous antibiotic treatment. As the clinical findings did not ameliorate, adjunctive homeopathic treatment was used. Under combined treatment, laboratory parameters returned to normal, and the epididymal abscess was rapidly shrinking. After 1 week, merely a subcutaneous liquid structure was detected. Fine-needle aspiration revealed sterile purulent liquid, which was confirmed by microbiological testing when the subcutaneous abscess was drained. Postoperative course was uneventful.

As the risk for recurrent epididymitis is high in persons with spinal cord injury, an organ-preserving approach is justified even in severe cases. Homeopathic treatment was a valuable adjunctive treatment in the above-mentioned case. Therefore, prospective studies are needed to further elucidate the future opportunities and limitations of classical homeopathy in the treatment of urinary tract infections.

Article No 3 (dated 2012):

Recurrent urinary tract infections (UTI) in patients with spinal cord injury are a frequent clinical problem. Often, preventive measures are not successful. We present the case reports of five patients with recurrent UTI who received additional homeopathic treatment. Of these patients, three remained free of UTI, whereas UTI frequency was reduced in two patients. Our initial experience with homeopathic prevention of UTI is encouraging. For an evidence-based evaluation of this concept, prospective studies are required.

It seems clear that all of the three more plausible explanations for the patients’ recovery listed above also apply to these two cases.

One might not be far off speculating that J Pannek, the first author of all these three articles, is a fan of homeopathy (this suspicion is confirmed by a link between him and the HOMEOPATHY RESEARCH INSTITUE: Prof Jürgen Pannek on the use of homeopathy for prophylaxis of UTI’s in patients with neurogenic bladder dysfunction). If that is so, I wonder why he does not conduct a controlled trial, rather than publishing case-report after case-report of apparently successful homeopathic treatments. Does he perhaps fear that his effects might dissolve into thin air under controlled conditions?

Case-reports of this nature can, of course, be interesting and some might even deserve to be published. But it would be imperative to draw the correct conclusions. Looking at the three articles above, I get the impression that, as time goes by, the conclusions of Prof Pannek et al (no, I know nobody from this group of authors personally) are growing more and more firm on less and less safe ground.

In my view, responsible authors should have concluded much more cautiously and reasonably. In the case of the paralytic ileus, for instance, they should not have gone further than stating something like this: adjunctive homeopathic therapy might turn out to be a promising treatment option for such patients. Despite the implausibility of homeopathy, this case-report might deserve to be followed up with a controlled clinical trial. Without such evidence, firm conclusions are clearly not possible.

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

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

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

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

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

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

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

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

When someone has completed a scientific project, it is customary to publish it ['unpublished science is no science', someone once told me many years ago]. To do so, he needs to write it up and submit it to a scientific journal. The editor of this journal will then submit it to a process called ‘peer review’.

What does ‘peer review’ entail? Well, it means that 2-3 experts are asked to critically assess the paper in question, make suggestions as to how it can be improved and submit a recommendation as to whether or not the article deserves to be published.

Peer review has many pitfalls but, so far, nobody has come up with a solution that is convincingly better. Many scientists are under pressure to publish ['publish or perish'], and therefore some people resort to cheating. A most spectacular case of fraudulent peer review has been reported recently in this press release:

SAGE statement on Journal of Vibration and Control

London, UK (08 July 2014) – SAGE announces the retraction of 60 articles implicated in a peer review and citation ring at the Journal of Vibration and Control (JVC). The full extent of the peer review ring has been uncovered following a 14 month SAGE-led investigation, and centres on the strongly suspected misconduct of Peter Chen, formerly of National Pingtung University of Education, Taiwan (NPUE) and possibly other authors at this institution.

In 2013 the then Editor-in-Chief of JVC, Professor Ali H. Nayfeh,and SAGE became aware of a potential peer review ring involving assumed and fabricated identities used to manipulate the online submission system SAGE Track powered by ScholarOne Manuscripts™. Immediate action was taken to prevent JVC from being exploited further, and a complex investigation throughout 2013 and 2014 was undertaken with the full cooperation of Professor Nayfeh and subsequently NPUE.

In total 60 articles have been retracted from JVC after evidence led to at least one author or reviewer being implicated in the peer review ring. Now that the investigation is complete, and the authors have been notified of the findings, we are in a position to make this statement.

While investigating the JVC papers submitted and reviewed by Peter Chen, it was discovered that the author had created various aliases on SAGE Track, providing different email addresses to set up more than one account. Consequently, SAGE scrutinised further the co-authors of and reviewers selected for Peter Chen’s papers, these names appeared to form part of a peer review ring. The investigation also revealed that on at least one occasion, the author Peter Chen reviewed his own paper under one of the aliases he had created.

Unbelievable? Perhaps, but sadly it is true; some scientists seem to be criminally ingenious when it comes to getting their dodgy articles into peer-reviewed journals.

And what does this have to do with ALTERNATIVE MEDICINE, you may well ask. The Journal of Vibration and Control is not even medical and certainly would never consider publishing articles on alternative medicine. Such papers go to one of the many [I estimate more that 1000] journals that cover either alternative medicine in general or any of the modalities that fall under this wide umbrella. Most of these journals, of course, pride themselves with being peer-reviewed – and, at least nominally, that is correct.

I have been on the editorial board of most of the more important journals in alternative medicine, and I cannot help thinking that their peer review process is not all that dissimilar from the fraudulent scheme set up by Peter Chen and disclosed above. What happens in alternative medicine is roughly as follows:

  • a researcher submits a paper for publication,
  • the editor sends it out for peer review,
  • the peer reviewers are either those suggested by the original author or members of the editorial board of the journal,
  • in either case, the reviewers are more than likely to be uncritical and recommend publication,
  • in the end, peer review turns out to be a farcical window dressing exercise with no consequence,
  • thus even very poor research and pseudo-research are being published abundantly.

The editorial boards of journals of alternative medicine tend to be devoid of experts who are critical about the subject at hand. If you think that I am exaggerating, have a look at the editorial board members of ‘HOMEOPATHY’ (or any other journal of alternative medicine) and tell me who might qualify as a critic of homeopathy. When the editor, Peter Fisher, recently fired me from his board because he felt I had tarnished the image of homeopathy, this panel lost the only person who understood the subject matter and, at the same time, was critical about it (the fact that the website still lists me as an editorial board member is merely a reflection of how slow things are in the world of homeopathy: Fisher fired me more than a year ago).

The point I am trying to make is simple: peer review is never a perfect method but when it is set up to be deliberately uncritical, it cannot possibly fulfil its function to prevent the publication of dodgy research. In this case, the quality of the science will be inadequate and generate false-positive messages that mislead the public.

Reiki is a Japanese technique which, according to a proponent, … is administered by “laying on hands” and is based on the idea that an unseen “life force energy” flows through us and is what causes us to be alive. If one’s “life force energy” is low, then we are more likely to get sick or feel stress, and if it is high, we are more capable of being happy and healthy…

A treatment feels like a wonderful glowing radiance that flows through and around you. Reiki treats the whole person including body, emotions, mind and spirit creating many beneficial effects that include relaxation and feelings of peace, security and wellbeing. Many have reported miraculous results.

Reiki is a simple, natural and safe method of spiritual healing and self-improvement that everyone can use. It has been effective in helping virtually every known illness and malady and always creates a beneficial effect. It also works in conjunction with all other medical or therapeutic techniques to relieve side effects and promote recovery [my emphasis].

Many websites give much more specific information about the health effects of Reiki:

Some Of The Reiki Healing Health Benefits 

  • Creates deep relaxation and aids the body to release stress and tension,
  • It accelerates the body’s self-healing abilities,
  • Aids better sleep,
  • Reduces blood pressure
  • Can help with acute (injuries) and chronic problems (asthma, eczema, headaches, etc.) and aides the breaking of addictions,
  • Helps relieve pain,
  • Removes energy blockages, adjusts the energy flow of the endocrine system bringing the body into balance and harmony,
  • Assists the body in cleaning itself from toxins,
  • Reduces some of the side effects of drugs and helps the body to recover from drug therapy after surgery and chemotherapy,
  • Supports the immune system,
  • Increases vitality and postpones the aging process,
  • Raises the vibrational frequency of the body,
  • Helps spiritual growth and emotional clearing.

With such remarkable claims being made, I had to look into this extraordinary treatment.

In 2008, I had a co-worker in my team who was (still is, I think) a Reiki healer. He also happened to be a decent scientist, and we thus decided to conduct a systematic review summarising the evidence for the effectiveness of Reiki. We searched the literature using 23 databases from their respective inceptions through to November 2007 (search again 23 January 2008) without language restrictions. Methodological quality was assessed using the Jadad score. The searches identified 205 potentially relevant studies. Nine randomised clinical trials (RCTs) met our inclusion criteria. Two RCTs suggested beneficial effects of Reiki compared with sham control on depression, while one RCT did not report intergroup differences. For pain and anxiety, one RCT showed intergroup differences compared with sham control. For stress and hopelessness, a further RCT reported effects of Reiki and distant Reiki compared with distant sham control. For functional recovery after ischaemic stroke there were no intergroup differences compared with sham. There was also no difference for anxiety between groups of pregnant women undergoing amniocentesis. For diabetic neuropathy there were no effects of reiki on pain. A further RCT failed to show the effects of Reiki for anxiety and depression in women undergoing breast biopsy compared with conventional care.

Overall, the trial data for any one condition were scarce and independent replications were not available for any condition. Most trials suffered from methodological flaws such as small sample size, inadequate study design and poor reporting. We therefore concluded that the evidence is insufficient to suggest that Reiki is an effective treatment for any condition. Therefore the value of Reiki remains unproven.

But this was in 2008! In the meantime, the evidence might have changed. Here are two recent publications which, I think, are worth having a look at:

The first article is a case-report of a nine-year-old female patient with a history of perinatal stroke, seizures, and type-I diabetes was treated for six weeks with Reiki. At the end of this treatment period, there was a decrease in stress in both the child and the mother, as measured by a modified Perceived Stress Scale and a Perceived Stress Scale, respectively. No change was noted in the child’s overall sense of well-being, as measured by a global questionnaire. However, there was a positive change in sleep patterns on 33.3% of the nights as reported on a sleep log kept by the mother. The child and the Reiki Master (a Reiki practitioner who has completed all three levels of Reiki certification training, trains and certifies individuals in the practice of Reiki, and provides Reiki to individuals) experienced warmth and tingling sensations on the same area of the child during the Reiki 7 minutes of each session. There were no reports of seizures during the study period.

The author concluded that Reiki is a useful adjunct for children with increased stress levels and sleep disturbances secondary to their medical condition. Further research is warranted to evaluate the use of Reiki in children, particularly with a large sample size, and to evaluate the long-term use of Reiki and its effects on adequate sleep.

In my view, this article is relevant because it typifies the type of research that is being done in this area and the conclusions that are being drawn from it. It should be clear to anyone who has the slightest ability of critical thinking that a case report of this nature tells us as good as nothing about the effectiveness of a therapy. Considering that Reiki is just about the least plausible intervention anyone can think of, the child’s condition in all likelihood improved not because of the Reiki healing but because of a myriad of unrelated factors; just think of placebo-effects, regression towards the mean, natural history of the condition, concomitant treatments, etc.

The plausibility of energy/biofield/spiritual healing such as Reiki is also the focus of the second remarkable article that was just published. It reports a systematic review of studies designed to examine whether bio-field therapists undergo physiological changes as they enter the healing state (remember: the Reiki healer in the above study experienced ‘warmth and tingling sensations’ during therapies). If reproducible changes could be identified, the authors argue, they might serve as markers to reveal events that correlate with the healing process.

Databases were searched for controlled or non-controlled studies of bio-field therapies in which physiological measurements were made on practitioners in a healing state. Design and reporting criteria, developed in part to reflect the pilot nature of the included studies, were applied using a yes (1.0), partial (0.5), or no (0) scoring system.

Of 67 identified studies, the inclusion criteria were met by 22, 10 of which involved human patients. Overall, the studies were of moderate to poor quality and many omitted information about the training and experience of the healer. The most frequently measured biomarkers were electroencephalography (EEG) and heart rate variability (HRV). EEG changes were inconsistent and not specific to bio-field therapies. HRV results suggest an aroused physiology for Reconnective Healing, Bruyere healing, and Hawaiian healing, but no changes were detected for Reiki or Therapeutic Touch.

The authors of this paper concluded that despite a decades-long research interest in identifying healing-related biomarkers in bio-field healers, little robust evidence of unique physiological changes has emerged to define the healers׳ state.

Now, let me guess why this is so. One does not need to be a rocket scientist to come up with the suggestion that no robust evidence for Reiki and all the other nonsensical forms of healing can be found for one disarmingly simple reason: NO SUCH EFFECTS EXIST.

There is some (albeit not compelling) evidence to suggest that chiropractic spinal manipulation might be effective for treating non-specific back pain. But what about specific back pain, such as the one caused by a herniated disc? Some experts believe that, in patients suffering from such a condition, manipulations are contra-indicated (because the latter can cause the former), while others think that manipulation might be an effective treatment option (although the evidence is far from compelling). Who is correct? The issue can only be resolved with data from well-designed clinical investigations. A new trial might therefore enlighten us.

The stated purposes of this study were:

  1. to evaluate patients with low-back pain (LBP) and leg pain due to magnetic resonance imaging-confirmed disc herniation treated with high-velocity, low-amplitude spinal manipulation in terms of their short-, medium-, and long-term outcomes of self-reported global impression of change and pain levels
  2. to determine if outcomes differ between acute and chronic patients using.

The researchers conducted a ‘prospective cohort outcomes study‘ with 148 patients with LBP, leg pain, and physical examination abnormalities with concordant lumbar disc herniations. Baseline numerical rating scale (NRS) data for LBP, leg pain, and the Oswestry questionnaire were obtained. The specific lumbar spinal manipulation was dependent upon whether the disc herniation was intraforaminal or paramedian as seen on the magnetic resonance images and was performed by a chiropractor. Outcomes included the patient’s global impression of change scale for overall improvement, the NRS for LBP, leg pain, and the Oswestry questionnaire at 2 weeks, 1, 3, and 6 months, and 1 year. The proportion of patients reporting “improvement” on the patient’s global impression of change scale was calculated for all patients and for acute vs chronic patients. Pre-treatment and post-treatment NRS scores were compared using the paired t test. Baseline and follow-up Oswestry scores were compared using the Wilcoxon test. Numerical rating scale and Oswestry scores for acute vs chronic patients were compared using the unpaired t test for NRS scores and the Mann-Whitney U test for Oswestry scores.

Significant improvements for all outcomes at all time points were reported. At 3 months, 91% of patients were “improved”, and 88% were “improved” after 1 year. Acute patients improved faster by 3 months than did chronic patients. 81.8% of chronic patients 89.2% felt “improved” at 1 year. No adverse events were reported.

The researchers concluded that a large percentage of acute and importantly chronic lumbar disc herniation patients treated with chiropractic spinal manipulation reported clinically relevant improvement.

Does this new study meaningfully contribute to our knowledge about the effectiveness of chiropractic manipulation for back pain caused by herniated discs? The short answer to this question is NO.

A longer answer might be that the report does tell us something relevant about the quality of this research project. We know from countless studies that ~50% of patients experience adverse effects after spinal manipulations by a chiropractor. This means that any report claiming that NO ADVERSE EFFECTS WERE REPORTED is puzzling to a degree that we have to seriously question its quality or even honesty. In this context, it is relevant to mention that a recent review of the evidence concluded that a cause-effect relationship exists between the manipulative treatment and the development of disc herniation.

The positive outcomes reported in this new study could, of course, be due to a range of factors which are unrelated to the manipulations administered by the chiropractors:

  1. placebo-effects
  2. natural history of disc herniation
  3. regression towards the mean
  4. other treatments employed by the patients
  5. social desirability

To be able to say with any degree of certainty that the manipulations had anything to do with the observed positive outcomes would require an entirely different study-design. Should we assume that this is not known in the world of chiropractic? Or should we consider that chiropractors shy away from rigorous research because they fear its results?

The term prospective cohort outcomes study, seems to be a chiropractic invention (cohort studies are by definition prospective, and observational studies are usually prospective). It seems that, behind this long and impressive word, one can easily hide the fact that this study design fails to make the slightest attempt of controlling for non-specific effects; the term sounds scientific – but when we analyse what it means, we discover that this methodology is little more than a self-serving consumer survey. Most scientists would call such an investigation quite simply an OBSERVATIONAL STUDY.

I think it is time that chiropractors start doing proper research which actually does answer some of the many open questions regarding spinal manipulation.

A remarkable article about homeopathy and immunisation entitled THE IMMUNISATION DILEMMA came to my attention recently. Its abstract promised: “evidence quantifying the effectiveness of vaccination and HP (homeoprophylaxis) will be examined. New international research describing and analysing HP interventions will be reported. An evidence-based conclusion will be reached.”

Sounds interesting? Let’s see what the article really offers. Here is the relevant text:

…evidence does exist to support claims regarding the effectiveness of homeopathic immunisation is undeniable.

I was first invited to visit Cuba in December 2008 to present at an international conference hosted by the Finlay Institute, which is a W. H. O.-accredited vaccine manufacturer. The Cubans described their use of HP to control an outbreak of leptospirosis (Weilʼs syndrome – a potentially fatal, water-born bacterial disease) in 2007 among the residents of the three eastern provinces which were most severely damaged by a severe hurricane – over 2.2 million people [7]. 2008 was an even worse year involving three hurricanes, and the countryʼs food production was only just recovering at the time of the conference. The HP program had been repeated in 2008, but data was not available at the conference regarding that intervention.

I revisited Cuba in 2010 and 2012, each time to work with the leader of the HP interventions, Dr. Bracho, to analyse the data available. Dr. Bracho is not a homeopath; he is a published and internationally recognised expert in the manufacture of vaccine adjuvants. He worked in Australia at Flinders University during 2004 with a team trying to develop an antimalarial vaccine.

In 2012 we accessed the raw leptospirosis surveillance data, comprising weekly reports from 15 provinces over 9 years (2000 to 2008) reporting 21 variables. This yielded a matrix with 147 420 possible entries. This included data concerning possible confounders, such as vaccination and chemoprophylaxis, which allowed a careful examination of possible distorting effects. With the permission of the Cubans, I brought this data back to Australia and it is being examined by mathematicians at an Australian university to see what other information can be extracted. Clearly, there is objective data supporting claims regarding the effectiveness of HP.

The 2008 result was remarkable, and could only be explained by the effectiveness of the HP intervention. Whilst the three hurricanes caused immense damage throughout the country it was again worse in the east, yet the three homeopathically immunised provinces experienced a negligible increase in cases whilst the rest of the country showed significant increases until the dry season in January 2009 [8].

This is but one example – there are many more. It is cited to show that there is significant data available, and that orthodox scientists and doctors have driven the HP interventions, in the Cuban case. Many people internationally now know this, so once again claims by orthodox authorities that there is no evidence merely serves to show that either the authorities are making uninformed/unscientific statements, or that they are aware but are intentionally withholding information. Either way, confidence is destroyed and leads to groups of people questioning what they are told…

Final Conclusions

The attacks against homeopathy in general and HP in particular will almost certainly continue. If we can achieve a significant level of agreement then we would be able to answer challenges to HP with a single, cohesive, evidence-based, and generally united response. This would be a significant improvement to the existing situation.

 

Reference 7 is the following article: Bracho G, Varela E, Fernández R et al. Large-scale application of highly-diluted bacteria for Leptospirosis epidemic control. Homeopathy 2010; 99: 156-166. The crucial bit if this paper are as follows:

A homeoprophylactic formulation was prepared from dilutions of four circulating strains of Leptospirosis. This formulation was administered orally to 2.3 million persons at high risk in an epidemic in a region affected by natural disasters. The data from surveillance were used to measure the impact of the intervention by comparing with historical trends and non-intervention regions.

After the homeoprophylactic intervention a significant decrease of the disease incidence was observed in the intervention regions. No such modifications were observed in non-intervention regions. In the intervention region the incidence of Leptospirosis fell below the historic median. This observation was independent of rainfall.

The homeoprophylactic approach was associated with a large reduction of disease incidence and control of the epidemic. The results suggest the use of HP as a feasible tool for epidemic control, further research is warranted.

The paper thus describes little more than an observational study. It shows that one region was less affected than another. I think it is quite clear that this could have many reasons which are unrelated to the homeopathic immunisation. Even the authors are cautious and speak in their conclusions not of a causal effect but of an “association”.

The 2012 data cited in the text remains unpublished; until it is available for public scrutiny, it is impossible to confirm that it is sound and meaningful.

Reference 8 refers to this article: Golden I, Bracho G. Adaptability of homœoprophylaxis in endemic, epidemic and stable background conditions. Homœopathic Links 2009; 22: 211-213. I have no access to this paper (if someone does, please fill us in) but, judging from both its title and the way it is described in the text, it does not seem to show reliable data about the efficacy of homeopathic immunisation.

So, is it true that “evidence does exist to support claims regarding the effectiveness of homeopathic immunisation”?

I do not think so!

Immunisation is by no means a trivial matter; wrong decisions in this area have the potential to cost the lives of millions. Therefore proofs of efficacy need to be published in peer-reviewed journals of high standing. These findings need then be criticised, replicated and re-criticised and re-replicated. Only when there is a wide consensus about the efficacy/safety or lack of efficacy/safety of a new form of immunisation, can it be generally accepted and implemented into clinical practice.

The current consensus about homeopathic immunisation is that it is nothing less than dangerous phantasy. Those who promote this quackery should be publicly exposed as charlatans of the worst kind.

Some practitioners of alternative medicine (doctors, naturopaths, chiropractors and others) earn a lot of money with the claim that chelation therapy (an effective mainstream treatment for acute heavy metal poisoning) is an effective means to  treat cardiovascular disease. However, the notion is controversial and implausible. Several systematic reviews of the best evidence concluded less than optimistically:

…more controlled studies are required to determine the efficacy of chelation therapy in cardiovascular disease before it can be used broadly in the clinical setting.

The best available evidence does not support the therapeutic use of EDTA chelation therapy in the treatment of cardiovascular disease.

Given the potential of chelation therapy to cause severe adverse effects, this treatment should now be considered obsolete.

The available data do not support the use of chelation in cardiovascular diseases.

More recently, important new evidence has emerged. The largest study of chelation therapy (TACT) ever conducted cost ~ $ 30 million and concluded that among stable patients with a history of MI, use of an intravenous chelation regimen with disodium EDTA, compared with placebo, modestly reduced the risk of adverse cardiovascular outcomes, many of which were revascularization procedures. These results provide evidence to guide further research but are not sufficient to support the routine use of chelation therapy for treatment of patients who have had an MI.

At the time, the TACT trial was heavily and rightly criticised for a whole host of reasons. For instance, because of the result of the FDA inspection of the highest accruing TACT site:

  • The investigators didn’t conduct the investigation in accordance with the signed statement and investigational plan. Several examples were given of shoddy procedures, prefilled forms, and failure to train personnel.
  • Failure to report promptly to the IRB all unanticipated problems involving risk to human subjects or others. Examples are given, including failure to report the deaths of patients on the study in a timely fashion (in one case the death wasn’t reported to the IRB until four months later; in another case it was never reported at all). In other cases, adverse event reports were not submitted to the IRB.
  • Failure to prepare or maintain adequate case histories with respect to observations and data pertinent to the investigation.
  • Investigational drug disposition records are not adequate with respect to dates, quantity, and use by subjects.

Despite these problems, the study was published in JAMA, albeit with a very critical editorial:

Differential dropout in TACT suggests unmasking, but the problem of intentional unblinding is more concerning. The sponsors of the trial, the National Heart, Lung, and Blood Institute (NHLBI) and the National Center for Complementary and Alternative Medicine (NCCAM), were unblinded throughout the trial. The National Institutes of Health policy unwisely allows the sponsor access to unblinded trial data, and both organizations sent observers to the closed sessions of the data monitoring committee. This gave them access to confidential data during each of the 11 interim analyses. The unblinding of the study sponsor represents a serious deviation from acceptable standards of conduct for supervision of clinical trials. If a pharmaceutical company sponsoring a trial were allowed access to actual outcome data during the study, there would be major objections. Like any sponsor, the NHLBI and NCCAM cannot be considered unbiased observers. These agencies made major financial commitments to the trial and may intentionally or inadvertently influence study conduct if inappropriately unblinded during the study…

Given the numerous concerns with this expensive, federally funded clinical trial, including missing data, potential investigator or patient unmasking, use of subjective end points, and intentional unblinding of the sponsor, the results cannot be accepted as reliable and do not demonstrate a benefit of chelation therapy. The findings of TACT should not be used as a justification for increased use of this controversial therapy.

Orac, makes several further critical points about the published trial:

First, the primary endpoint (i.e., the aggregated serious cardiovascular events) did indeed show a modest difference, namely 30% of placebo subjects versus 26.5% of the EDTA chelation subjects (hazard ratio 0.82 for chelation). However, one notes that the result is just barely statistically significant, p = 0.035, with the 99% confidence interval for the hazard ratio ranging from 0.69 to 0.99. (The predetermined level for statistical significance for purposes of this study was 0.036; so this is statistically significant by the barest margin.) More importantly, if you look at the individual endpoints that make up that aggregate, there was no statistically significant difference in death, myocardial infarction, stroke, coronary revascularization, and hospitalization for angina. Subgroup analysis (always a questionable analysis that requires replication, even when preplanned, as in TACT) purported to show a much greater benefit for diabetics, with a hazard ratio of 0.61 (p=0.002), while patients without diabetes showed no statistically significant difference in any of the outcome measures, including the aggregated total bad outcomes.

Now a paper that has just emerged describes the intent-to-treat comparison of this trial in patients with diabetes.

This was a double-blind, placebo-controlled, 2 × 2 factorial multicenter randomized trial of 1,708 post-myocardial infarction (MI) patients ≥50 years of age and with creatinine ≤2.0 mg/dL randomized to receive 40 EDTA chelation or placebo infusions plus 6 caplets daily of a 28-component multivitamin-multimineral mixture or placebo. The primary end point was a composite of total mortality, MI, stroke, coronary revascularization, or hospitalization for angina.

Median age was 65 years, 18% were female, 94% were Caucasian, 37% were diabetic, 83% had prior coronary revascularization, and 73% were on statins. Five-year Kaplan-Meier estimates for the primary end point was 31.9% in the chelation + high-dose vitamin group, 33.7% in the chelation + placebo vitamin group, 36.6% in the placebo infusion + active vitamin group, and 40.2% in the placebo infusions + placebo vitamin group. The reduction in primary end point by double active treatment compared with double placebo was significant (hazard ratio 0.74, 95% CI 0.57-0.95, P = .016). In patients with diabetes, the primary end point reduction of double active compared with double placebo was more pronounced (hazard ratio 0.49, 95% CI 0.33-0.75, P < .001).

The authors conclude that in stable post-MI patients on evidence-based medical therapy, the combination of oral high-dose vitamins and chelation therapy compared with double placebo reduced clinically important cardiovascular events to an extent that was both statistically significant and of potential clinical relevance.

I fear that these conclusions are erroneous and misleading: the marginally positive finding might have nothing to do with chelation per se; most likely they are due to the fact that the ‘vitamin’ mixture administered along with chelation contained ingredients like heparin and procaine which are potentially beneficial for cardiovascular conditions. Moreover, the placebo contained a considerable amount of glucose which could easily explain the better outcome of the diabetic subgroup receiving the verum – in other words, the verum generated better results not because it was effective but because the ‘placebo’ had detrimental effects.

Yesterday, BBC NEWS published the following interesting text about a BBC4 broadcast entitled ‘THE ROYAL ACTIVIST’ aired on the same day:

Prince Charles has been a well-known supporter of complementary medicine. According to a… former Labour cabinet minister, Peter Hain, it was a topic they shared an interest in.

“He had been constantly frustrated at his inability to persuade any health ministers anywhere that that was a good idea, and so he, as he once described it to me, found me unique from this point of view, in being somebody that actually agreed with him on this, and might want to deliver it.”
Mr Hain added: “When I was Secretary of State for Northern Ireland in 2005-7, he was delighted when I told him that since I was running the place I could more or less do what I wanted to do.***
“I was able to introduce a trial for complementary medicine on the NHS, and it had spectacularly good results, that people’s well-being and health was vastly improved.

“And when he learnt about this he was really enthusiastic and tried to persuade the Welsh government to do the same thing and the government in Whitehall to do the same thing for England, but not successfully,” added Mr Hain.

*** obviously there is no homeopathic remedy for megalomania (but that’s a different story)

Oh really?

A TRIAL?

SPECTACULARLY GOOD RESULTS?

NO KIDDING?

Let’s have a look at the ‘trial’ and its results. An easily accessible report provides the following details about it:

From February 2007 to February 2008, Get Well UK ran the UK’s first government-backed complementary therapy pilot. Sixteen practitioners provided treatments including acupuncture, osteopathy and aromatherapy, to more than 700 patients at two GP practices in Belfast and Derry.   

The BBC made an hour long documentary following our trials and tribulations, which was broadcast on BBC1 NI on 5 May 2008.

Following the successful completion of the pilot, the results were analysed by Social and Market Research and recommendations were made to the Health Minister

Aims and Objectives 

The aim of the project was to pilot services integrating complementary medicine into existing primary care services in Northern Ireland. Get Well UK provided this pilot project for the Department for Health, Social Services and Public Safety (DHSSPS) during 2007.

The objectives were:

  • To measure the health outcomes of the service and monitor health improvements.
  • To redress inequalities in access to complementary medicine by providing therapies through the NHS, allowing access regardless of income.
  • To contribute to best practise in the field of delivering complementary therapies through primary care.
  • To provide work for suitably skilled and qualified practitioners.
  • To increase patient satisfaction with quick access to expert care.
  • To help patients learn skills to improve and retain their health.
  • To free up GP time to work with other patients.
  • To deliver the programme for 700 patients.

Results 

The results of the pilot were analysed by Social and Market Research, who produced this report.

The findings can be summarised as follows: 

Following the pilot, 80% of patients reported an improvement in their symptoms, 64% took less time off work and 55% reduced their use of painkillers.

In the pilot, 713 patients with a range of ages and demographic backgrounds and either physical or mental health conditions were referred to various complementary and alternative medicine (CAM) therapies via nine GP practices in Belfast and Londonderry. Patients assessed their own health and wellbeing pre and post therapy and GPs and CAM practitioners also rated patients’ responses to treatment and the overall effectiveness of the scheme.

Health improvement
• 81% of patients reported an improvement in their physical health
• 79% reported an improvement in their mental health
• 84% of patients linked an improvement in their health and wellbeing directly to their CAM treatment
• In 65% of patient cases, GPs documented a health improvement, correlating closely to patient-reported improvements
• 94% of patients said they would recommend CAM to another patient with their condition
• 87% of patient indicated a desire to continue with their CAM treatment

Painkillers and medication
• Half of GPs reported prescribing less medication and all reported that patients had indicated to them that they needed less
• 62% of patients reported suffering from less pain
• 55% reported using less painkillers following treatment
• Patients using medication reduced from 75% before treatment to 61% after treatment
• 44% of those taking medication before treatment had reduced their use afterwards

Health service and social benefits
• 24% of patients who used health services prior to treatment (i.e. primary and secondary care, accident and emergency) reported using the services less after treatment
• 65% of GPs reported seeing the patient less following the CAM referral
• Half of GPs said the scheme had reduced their workload and 17% reported a financial saving for their practice
• Half of GPs said their patients were using secondary care services less.

Impressed? Well, in case you are, please consider this:

  • there was no control group
  • therefore it is not possible to attribute any of the outcomes to the alternative therapies offered
  • they could have been due to placebo-effects
  • or to the natural history of the disease
  • or to regression towards the mean
  • or to social desirability
  • or to many other factors which are unrelated to the alternative treatments provided
  • most outcome measures were not objectively verified
  • the patients were self-selected
  • they would all have had conventional treatments in parallel
  • this ‘trial’ was of such poor quality that its findings were never published in a peer-reviewed journal
  • this was not a ‘trial’ but a ‘pilot study’
  • pilot studies are not normally for measuring outcomes but for testing the feasibility of a proper trial
  • the research expertise of the investigators was close to zero
  • the scientific community merely had pitiful smiles for this ‘trial’ when it was published
  • neither Northern Ireland nor any other region implemented the programme despite its “spectacularly good results”.

So, is the whole ‘trial’ story an utterly irrelevant old hat?

Certainly not! Its true significance does not lie in the fact that a few amateurs are trying to push bogus treatments into the NHS via the flimsiest pseudo-research of the century. The true significance, I think, is that it shows how Prince Charles, once again, oversteps the boundaries of his constitutional role.

If you are pregnant, a ‘breech presentation’ is not good news. It occurs when the fetus presents ‘bottom-down’ in the uterus. There are three types:

  • Breech with extended legs (frank) – 85% of cases
  • Breech with fully flexed legs (complete)
  • Footling (incomplete) with one or both thighs extended

The significance of breech presentation is its association with higher perinatal mortality and morbidity when compared to cephalic presentations. This is due both to pre-existing congenital malformation, increased incidence of breech in premature deliveries and increased risk of intrapartum trauma or asphyxia. Caesarean section has been adopted as the ‘normal’ mode of delivery for term breech presentations in Europe and the USA, as the consensus is that this reduces the risk of birth-related complications.

But Caesarian section is also not a desirable procedure. Something far less invasive would be much more preferable, of course. This is where the TCM-practitioners come in. They claim they have the solution: moxibustion, i.e. the stimulation of acupuncture points by heat. But does it really work? Can it turn the fetus into the correct position?

This new study aimed to assess the efficacy of moxibustion (heating of the acupuncture needle with an igniting charcoal moxa stick) with acupuncture for version of breech presentations to reduce their rate at 37 weeks of gestation and at delivery. It was a randomized, placebo-controlled, single-blind trial including 328 pregnant women recruited in a university hospital center between 33 4/7 and 35 4/7 weeks of gestation. Moxibustion with acupuncture or inactivated laser (placebo) treatment was applied to point BL 67 for 6 sessions. The principal endpoint was the percentage of fetuses in breech presentation at 37 2/7 weeks of gestation.

The results show that the percentage of fetuses in breech presentation at 37 2/7 weeks of gestation was not significantly different in both groups (72.0 in the moxibustion with acupuncture group compared with 63.4% in the placebo group).

The authors concluded that treatment by moxibustion with acupuncture was not effective in correcting breech presentation in the third trimester of pregnancy.

You might well ask why on earth anyone expected that stimulating an acupuncture point would turn a fetus in the mother’s uterus into the optimal position that carries the least risk during the process of giving birth. This is what proponents of this technique say about this approach:

During a TCM consultation to turn a breech baby the practitioner will take a comprehensive case history, make a diagnosis and apply the appropriate acupuncture treatment.  They will assess if moxibustion might be helpful. Practitioners will then instruct women on how to locate the appropriate acupuncture points and demonstrate how to safely apply moxa at home. The acupuncture point UB 67 is the primary point selected for use because it is the most dynamic point to activate the uterus.  Its forte is in turning malpositioned babies.  It is located on the outer, lower edge of both little toenails. According to TCM theory, moxa has a tonifying and warming effect which promotes movement and activity.  The nature of heat is also rising.  This warming and raising effect is utilised to encourage the baby to become more active and lift its bottom up in order to gain adequate momentum to summersault into the head down position. This technique can also be used to reposition transverse presentation, a situation where the baby’s has its shoulder or back pointing down, or is lying sideways across the abdomen.

Not convinced? I can’t say I blame you!

Clearly, we need to know what the totality of the most reliable evidence shows; and what better than a Cochrane review to inform us about it? Here is what it tells us:

Moxibustion was not found to reduce the number of non-cephalic presentations at birth compared with no treatment (P = 0.45). Moxibustion resulted in decreased use of oxytocin before or during labour for women who had vaginal deliveries compared with no treatment (risk ratio (RR) 0.28, 95% confidence interval (CI) 0.13 to 0.60). Moxibustion was found to result in fewer non-cephalic presentations at birth compared with acupuncture (RR 0.25, 95% CI 0.09 to 0.72). When combined with acupuncture, moxibustion resulted in fewer non-cephalic presentations at birth (RR 0.73, 95% CI 0.57 to 0.94), and fewer births by caesarean section (RR 0.79, 95% CI 0.64 to 0.98) compared with no treatment. When combined with a postural technique, moxibustion was found to result in fewer non-cephalic presentations at birth compared with the postural technique alone (RR 0.26, 95% CI 0.12 to 0.56).

In other words, there is indeed some encouraging albeit not convincing evidence! How can this be? There is no plausible explanation why this treatment should work!

But there is a highly plausible explanation why the results of many of the relevant trials are false-positive thus rendering a meta-analysis false-positive as well. I have repeatedly pointed out on this blog that practically all Chinese TCM-studies report (false) positive results; and many of the studies included in this review were done in China. The Cochrane review provides a strong hint about the lack of rigor in its ‘plain language summary’:

The included trials were of moderate methodological quality, sample sizes in some of the studies were small, how the treatment was applied differed and reporting was limited. While the results were combined they should be interpreted with caution due to the differences in the included studies. More evidence is needed concerning the benefits and safety of moxibustion.

So, would I recommend moxibustion for breech conversion? I don’t think so!

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