Twenty years ago, when I started my Exeter job as a full-time researcher of complementary/alternative medicine (CAM), I defined the aim of my unit as applying science to CAM. At the time, this intention upset quite a few CAM-enthusiasts. One of the most prevalent arguments of CAM-proponents against my plan was that the study of CAM with rigorous science was quite simply an impossibility. They claimed that CAM included mind and body practices, holistic therapies, and other complex interventions which cannot not be put into the ‘straight jacket’ of conventional research, e. g. a controlled clinical trial. I spent the next few years showing that this notion was wrong. Gradually and hesitantly CAM researchers seemed to agree with my view – not all, of course, but first a few and then slowly, often reluctantly the majority of them.
What followed was a period during which several research groups started conducting rigorous tests of the hypotheses underlying CAM. All too often, the results turned out to be disappointing, to say the least: not only did most of the therapies in question fail to show efficacy, they were also by no means free of risks. Worst of all, perhaps, much of CAM was disclosed as being biologically implausible. The realization that rigorous scientific scrutiny often generated findings which were not what proponents had hoped for led to a sharp decline in the willingness of CAM-proponents to conduct rigorous tests of their hypotheses. Consequently, many asked whether science was such a good idea after all.
But that, in turn, created a new problem: once they had (at least nominally) committed themselves to science, how could they turn against it? The answer to this dilemma was easier that anticipated: the solution was to appear dedicated to science but, at the same time, to argue that, because CAM is subtle, holistic, complex etc., a different scientific approach was required. At this stage, I felt we had gone ‘full circle’ and had essentially arrived back where we were 20 years ago - except that CAM-proponents no longer rejected the scientific method outright but merely demanded different tools.
A recent article may serve as an example of this new and revised stance of CAM-proponents on science. Here proponents of alternative medicine argue that a challenge for research methodology in CAM/ICH* is the growing recognition that CAM/IHC practice often involves complex combination of novel interventions that include mind and body practices, holistic therapies, and others. Critics argue that the reductionist placebo controlled randomized control trial (RCT) model that works effectively for determining efficacy for most pharmaceutical or placebo trial RCTs may not be the most appropriate for determining effectiveness in clinical practice for either CAM/IHC or many of the interventions used in primary care, including health promotion practices. Therefore the reductionist methodology inherent in efficacy studies, and in particular in RCTs, may not be appropriate to study the outcomes for much of CAM/IHC, such as Traditional Korean Medicine (TKM) or other complex non-CAM/IHC interventions—especially those addressing comorbidities. In fact it can be argued that reductionist methodology may disrupt the very phenomenon, the whole system, that the research is attempting to capture and evaluate (i.e., the whole system in its naturalistic environment). Key issues that surround selection of the most appropriate methodology to evaluate complex interventions are well described in the Kings Fund report on IHC and also in the UK Medical Research Council (MRC) guidelines for evaluating complex interventions—guidelines which have been largely applied to the complexity of conventional primary care and care for patients with substantial comorbidity. These reports offer several potential solutions to the challenges inherent in studying CAM/IHC. [* IHC = integrated health care]
Let’s be clear and disclose what all of this actually means. The sequence of events, as I see it, can be summarized as follows:
- We are foremost ALTERNATIVE! Our treatments are far too unique to be subjected to reductionist research; we therefore reject science and insist on an ALTERNATIVE.
- We (well, some of us) have reconsidered our opposition and are prepared to test our hypotheses scientifically (NOT LEAST BECAUSE WE NEED THE RECOGNITION THAT THIS MIGHT BRING).
- We are dismayed to see that the results are mostly negative; science, it turns out, works against our interests.
- We need to reconsider our position.
- We find it inconceivable that our treatments do not work; all the negative scientific results must therefore be wrong.
- We always said that our treatments are unique; now we realize that they are far too holistic and complex to be submitted to reductionist scientific methods.
- We still believe in science (or at least want people to believe that we do) - but we need a different type of science.
- We insist that RCTs (and all other scientific methods that fail to demonstrate the value of CAM) are not adequate tools for testing complex interventions such as CAM.
- We have determined that reductionist research methods disturb our subtle treatments.
- We need pragmatic trials and similarly ‘soft’ methods that capture ‘real life’ situations, do justice to CAM and rarely produce a negative result.
What all of this really means is that, whenever the findings of research fail to disappoint CAM-proponents, the results are by definition false-negative. The obvious solution to this problem is to employ different (weaker) research methods, preferably those that cannot possibly generate a negative finding. Or, to put it bluntly: in CAM, science is acceptable only as long as it produces the desired results.
Linus Carl Pauling (1901 – 1994), the American scientist, peace activist, author, and educator who won two Nobel prizes, was one of the most influential chemists in history and ranks among the most important scientists of the 20th century. Linus Pauling’s work on vitamin C, however, generated considerable controversy. Pauling wrote many papers and a popular book, Cancer and Vitamin C. Vitamin C, we know today, protects cells from oxidative DNA damage and might thereby block carcinogenesis. Pauling popularised the regular intake of vitamin C; eventually he published two studies of end-stage cancer patients; their results apparently showed that vitamin C quadrupled survival times. A re-evaluation, however, found that the vitamin C groups were less sick on entry to the study. Later clinical trials concluded that there was no benefit to high-dose vitamin C. Since then, the established opinion is that the best evidence does not support a role for high dose vitamin C in the treatment of cancer. Despite all this, high dose IV vitamin C is in unexpectedly wide use by CAM practitioners.
Yesterday, new evidence has been published in the highly respected journal ‘Nature’; does it vindicate Pauling and his followers?
Chinese oncologists conducted a meta-analysis to assess the association between vitamin C intake and the risk to acquire lung cancer. Pertinent studies were identified by a searches of several electronic databases through December of 2013. Random-effect model was used to combine the data for analysis. Publication bias was estimated using Begg’s funnel plot and Egger’s regression asymmetry test.
Eighteen articles reporting 21 studies involving 8938 lung cancer cases were included in this meta-analysis. Pooled results suggested that highest vitamin C intake level versus lowest level was significantly associated with the risk of lung cancer. The effect was largest in investigations from the United States and in prospective studies. A linear dose-response relationship was found, with the risk of lung cancer decreasing by 7% for every 100 mg/day increase in the intake of vitamin C . No publication bias was found.
The authors conclude that their analysis suggested that the higher intake of vitamin C might have a protective effect against lung cancer, especially in the United States, although this conclusion needs to be confirmed.
Does this finding vindicate Pauling’s theory? Not really.
Even though the above-quoted conclusions seem to suggest a causal link, we are, in fact, far from having established one. The meta-analysis pooled mainly epidemiological data from various studies. Such investigations are doubtlessly valuable but they are fraught with uncertainties and cannot prove causality. For instance, there could be dozens of factors that have confounded these data in such a way that they produce a misleading result. The simplest explanation of the meta-analytic results might be that people who have a very high vitamin C intake tend to have generally healthier life-styles than those who take less vitamin C. When conducting a meta-analysis, one does, of course, try to account for such factors; but in many cases the necessary information to do that is not available, and therefore uncertainty persists.
In other words, the authors were certainly correct when stating that their findings needed to be confirmed. Pauling’s theory cannot be vindicated by such reports – in fact, the authors do not even mention Pauling with one word.
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:
- 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:
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.
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:
- Take the findings from the existing trials that are devoid of patient-blinding with more than just a pinch of salt.
- Discourage the funding of future studies that fail to include patient-blinding.
- If patient-blinding is truly and demonstrably impossible – which is not often the case – make sure that the trialists at least include blinding of the assessors of the primary outcome measures.
There must be well over 10 000 clinical trials of acupuncture; Medline lists ~5 000, and many more are hidden in the non-Medline listed literature. That should be good news! Sadly, it isn’t.
It should mean that we now have a pretty good idea for what conditions acupuncture is effective and for which illnesses it does not work. But we don’t! Sceptics say it works for nothing, while acupuncturists claim it is a panacea. The main reason for this continued controversy is that the quality of the vast majority of these 10 000 studies is not just poor, it is lousy.
“Where is the evidence for this outraging statement???” – I hear the acupuncture-enthusiasts shout. Well, how about my own experience as editor-in-chief of FACT? No? Far too anecdotal?
How about looking at Cochrane reviews then; they are considered to be the most independent and reliable evidence in existence? There are many such reviews (most, if not all [co-]authored by acupuncturists) and they all agree that the scientific rigor of the primary studies is fairly awful. Here are the crucial bits of just the last three; feel free to look for more:
Or how about providing an example? Good idea! Here is a new trial which could stand for numerous others:
This study was performed to compare the efficacy of acupuncture versus corticosteroid injection for the treatment of Quervain’s tendosynovitis (no, you do not need to look up what condition this is for understanding this post). Thirty patients were treated in two groups. The acupuncture group received 5 acupuncture sessions of 30 minutes duration. The injection group received one methylprednisolone acetate injection in the first dorsal compartment of the wrist. The degree of disability and pain was evaluated by using the Quick Disabilities of the Arm, Shoulder, and Hand (Q-DASH) scale and the Visual Analogue Scale (VAS) at baseline and at 2 weeks and 6 weeks after the start of treatment. The baseline means of the Q-DASH and the VAS scores were 62.8 and 6.9, respectively. At the last follow-up, the mean Q-DASH scores were 9.8 versus 6.2 in the acupuncture and injection groups, respectively, and the mean VAS scores were 2 versus 1.2. Thus there were short-term improvements of pain and function in both groups.
The authors drew the following conclusions: Although the success rate was somewhat higher with corticosteroid injection, acupuncture can be considered as an alternative option for treatment of De Quervain’s tenosynovitis.
The flaws of this study are exemplary and numerous:
- This should have been a study that compares two treatments – the technical term is ‘equivalence trial – and such studies need to be much larger to produce a meaningful result. Small sample sizes in equivalent trials will always make the two treatments look similarly effective, even if one is a pure placebo.
- There is no gold standard treatment for this condition. This means that a comparative trial makes no sense at all. In such a situation, one ought to conduct a placebo-controlled trial.
- There was no blinding of patients; therefore their expectation might have distorted the results.
- The acupuncture group received more treatments than the injection group; therefore the additional attention might have distorted the findings.
- Even if the results were entirely correct, one cannot conclude from them that acupuncture was effective; the notion that it was similarly ineffective as the injections is just as warranted.
These are just some of the most fatal flaws of this study. The sad thing is that similar criticisms can be made for most of the 10 000 trials of acupuncture. But the point here is not to nit-pick nor to quack-bust. My point is a different and more serious one: fatally flawed research is not just a ‘poor show’, it is unethical because it is a waste of scarce resources and, even more importantly, an abuse of patients for meaningless pseudo-science. All it does is it misleads the public into believing that acupuncture might be good for this or that condition and consequently make wrong therapeutic decisions.
In acupuncture (and indeed in most alternative medicine) research, the problem is so extremely wide-spread that it is high time to do something about it. Journal editors, peer-reviewers, ethics committees, universities, funding agencies and all others concerned with such research have to work together so that such flagrant abuse is stopped once and for all.
We all know, I think, that chronic low back pain (CLBP) is common and causes significant suffering in individuals as well as cost to society. Many treatments are on offer but, as we have seen repeatedly on this blog, not one is convincingly effective and some, like chiropractic, is associated with considerable risks.
Enthusiasts claim that hypnotherapy works well, but too little is known about the minimum dose needed to produce meaningful benefits, the roles of home practice and hypnotizability on outcome, or the maintenance of treatment benefits beyond 3 months. A new trial was aimed at addressing these issues.
One hundred veterans with CLBP participated in a randomized, four parallel group study. The groups were (1) an eight-session self-hypnosis training intervention without audio recordings for home practice; (2) an eight-session self-hypnosis training intervention with recordings; (3) a two-session self-hypnosis training intervention with recordings and brief weekly reminder telephone calls; and (4) an eight-session active (biofeedback) control intervention.
Participants in all four groups reported significant pre- to post-treatment improvements in pain intensity, pain interference and sleep quality. The three hypnotherapy groups combined reported significantly more pain intensity reduction than the control group. There was no significant difference among the three hypnotherapy groups. Over half of the participants who received hypnotherapy reported clinically meaningful (≥30%) reductions in pain intensity, and they maintained these benefits for at least 6 months after treatment. Neither hypnotizability nor amount of home practice was associated significantly with treatment outcome.
The authors conclude that two sessions of self-hypnosis training with audio recordings for home practice may be as effective as eight sessions of hypnosis treatment. If replicated in other patient samples, the findings have important implications for the application of hypnosis treatment for chronic pain management.
Even though this trial has several important limitations, I do agree with the authors: these results would be worth an independent replication – not least because self-hypnosis is cheap and does not carry great risks. What would be interesting, in my view, are studies that compare several alternative LBP therapies (e.g. chiropractic, osteopathy, acupuncture, massage, various form of exercise and hypnotherapy) in terms of cost, risks, long-term effectiveness and patients’ preference. I somehow feel that the results of such comparative trials might overturn the often issued recommendations for spinal manipulation, i.e. chiropractic or osteopathy.
Niacin – also known as vitamin B3 or nicotinic acid - is a natural compound (formula C
2 ) and an essential nutrient for humans. It is water-soluble, which means it is not stored in the body. Excess amounts of the vitamin leave the body through the urine. That means we need a continuous supply of niacin in your diet.
Niacin is found in variety of foods, including liver, chicken, beef, fish, cereal, peanuts and legumes. It can also be synthesized from tryptophan, an essential amino acid found in protein. Niacin has long been an accepted treatment for high cholesterol. It is well-documented to increase the levels of high-density cholesterol (HDL or “good cholesterol”) and to decrease the levels of low-density cholesterol (LDL or “bad cholesterol”).
But what do these effects really mean? Do they translate into true health benefits? A brand-new study casts doubt on the value of niacin therapy:
After a pre-randomization run-in phase to standardize the background statin-based LDL cholesterol-lowering therapy and to establish participants’ ability to take extended-release niacin without clinically significant adverse effects, the researchers randomly assigned 25,673 adults with vascular disease to receive 2 g of extended-release niacin and 40 mg of laropiprant or a matching placebo daily. The primary outcome was the first major vascular event (non-fatal myocardial infarction, death from coronary causes, stroke, or arterial revascularization).
During a median follow-up period of 3.9 years, participants who were assigned to extended-release niacin-laropiprant had an LDL cholesterol level that was 10 mg per deciliter (0.25 mmol/l) lower and an HDL cholesterol level that was 6 mg per deciliter (0.16 mmol/l) higher than the levels in those assigned to placebo. Thus the lipid-effects of previous studies were confirmed.
However, assignment to niacin-laropiprant, as compared with assignment to placebo, had no significant effect on the incidence of major vascular events Niacin-laropiprant was associated with an increased incidence of disturbances in diabetes control that were considered to be serious and with an increased incidence of diabetes diagnoses as well as increases in serious adverse events associated with the gastrointestinal system, the musculoskeletal system, the skin and infections and bleeding.
Based of these data, the authors arrived at the following conclusion: among participants with atherosclerotic vascular disease, the addition of extended-release niacin-laropiprant to statin-based LDL cholesterol-lowering therapy did not significantly reduce the risk of major vascular events but did increase the risk of serious adverse events.
This extremely well-done trial is a poignant reminder of the fact that, in health care, we must never take our assumptions for granted. Here the underlying assumption was that the Niacin-induced lipid changes lead to a reduction of cardiovascular risks. Not only it proved to be erroneous but, through serious adverse effects, Niacin actually decreased patients’ health status.
The lessons from all this are straight forward, I think:
- ‘Natural’ does not necessarily mean safe.
- Long-established does not necessarily mean efficacious.
- Assumptions are merely assumptions, nothing more; if we want to make sure that they hold, we need to test them.
- When we finally do test assumptions, we better do it rigorously.
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:
- 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:
- 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
- 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:
- natural history of disc herniation
- regression towards the mean
- other treatments employed by the patients
- 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.