Amongst all the implausible treatments to be found under the umbrella of ‘alternative medicine’, Reiki might be one of the worst, i. e. least plausible and outright bizarre (see for instance here, here and here). But this has never stopped enthusiasts from playing scientists and conducting some more pseudo-science.
This new study examined the immediate symptom relief from a single reiki or massage session in a hospitalized population at a rural academic medical centre. It was designed as a retrospective analysis of prospectively collected data on demographic, clinical, process, and quality of life for hospitalized patients receiving massage therapy or reiki. Hospitalized patients requesting or referred to the healing arts team received either a massage or reiki session and completed pre- and post-therapy symptom questionnaires. Differences between pre- and post-sessions in pain, nausea, fatigue, anxiety, depression, and overall well-being were recorded using an 11-point Likert scale.
Patients reported symptom relief with both reiki and massage therapy. Reiki improved fatigue and anxiety more than massage. Pain, nausea, depression, and well being changes were not different between reiki and massage encounters. Immediate symptom relief was similar for cancer and non-cancer patients for both reiki and massage therapy and did not vary based on age, gender, length of session, and baseline symptoms.
The authors concluded that reiki and massage clinically provide similar improvements in pain, nausea, fatigue, anxiety, depression, and overall well-being while reiki improved fatigue and anxiety more than massage therapy in a heterogeneous hospitalized patient population. Controlled trials should be considered to validate the data.
Don’t I just adore this little addendum to the conclusions, “controlled trials should be considered to validate the data” ?
The thing is, there is nothing to validate here!
The outcomes are not due to the specific effects of Reiki or massage; they are almost certainly caused by:
- the extra attention,
- the expectation of patients,
- the verbal or non-verbal suggestions of the therapists,
- the regression towards the mean,
- the natural history of the condition,
- the concomitant therapies administered in parallel,
- the placebo effect,
- social desirability.
Such pseudo-research only can only serve one purpose: to mislead (some of) us into thinking that treatments such as Reiki might work.
What journal would be so utterly devoid of critical analysis to publish such unethical nonsense?
Ahh … it’s our old friend the Journal of Alternative and Complementary Medicine
Say no more!
Since many months, I have noticed a proliferation of so-called pilot studies of alternative therapies. A pilot study (also called feasibility study) is defined as a small scale preliminary study conducted in order to evaluate feasibility, time, cost, adverse events, and improve upon the study design prior to performance of a full-scale research project. Here I submit that most of the pilot studies of alternative therapies are, in fact, bogus.
To qualify as a pilot study, an investigation needs to have an aim that is in line with the above-mentioned definition. Another obvious hallmark must be that its conclusions are in line with this aim. We do not need to conduct much research to find that even these two elementary preconditions are not fulfilled by the plethora of pilot studies that are currently being published, and that proper pilot studies of alternative medicine are very rare.
Three recent examples of dodgy pilot studies will have to suffice (but rest assured, there are many, many more).
The aim of this study was to evaluate the effects of foot reflexotherapy on pain and postural balance in elderly individuals with low back pain. And the conclusions drawn by its authors were that this study demonstrated that foot reflexotherapy induced analgesia but did not affect postural balance in elderly individuals with low back pain.
The aim of this study was to investigate the effect of Tai Chi training on dual-tasking performance that involved stepping down and compared it with that of conventional exercise among stroke survivors. And the conclusions read: These results suggest a beneficial effect of Tai Chi training on cognition among stroke survivors without compromising physical task performance in dual-tasking.
The aim of this study was to evaluate the efficacy [of acupuncture] over 12 weeks of treatment and 12 weeks of follow-up. And the conclusion: Acupuncture decreases WC, HC, HbA1c, TG, and TC values and blood pressure in MetS.
It is almost painfully obvious that these studies are not ‘pilot’ studies as defined above.
So, what are they, and why are they so popular in alternative medicine?
The way I see it, they are the result of amateur researchers conducting pseudo-research for publication in lamentable journals in an attempt to promote their pet therapies (I have yet to find such a study that reports a negative finding). The sequence of events that lead to the publication of such pilot studies is usually as follows:
- An enthusiast or a team of enthusiasts of alternative medicine decide that they will do some research.
- They have no or very little know-how in conducting a clinical trial.
- They nevertheless feel that such a study would be nice as it promotes both their careers and their pet therapy.
- They design some sort of a plan and start recruiting patients for their trial.
- At this point they notice that things are not as easy as they had imagined.
- They have too few funds and too little time to do anything properly.
- This does, however, not stop them to continue.
- The trial progresses slowly, and patient numbers remain low.
- After a while the would-be researchers get fed up and decide that their study has enough patients to stop the trial.
- They improvise some statistical analyses with their results.
- They write up the results the best they can.
- They submit it for publication in a 3rd class journal and, in order to get it accepted, they call it a ‘pilot study’.
- They feel that this title is an excuse for even the most obvious flaws in their work.
- The journal’s reviewers and editors are all proponents of alternative medicine who welcome any study that seems to confirm their belief.
- Thus the study does get published despite the fact that it is worthless.
Some might say ‘so what? no harm done!’
But I beg to differ: these studies pollute the medical literature and misguide people who are unable or unwilling to look behind the smoke-screen. Enthusiasts of alternative medicine popularise these bogus trials, while hiding the fact that their results are unreliable. Journalists report about them, and many consumers assume they are being told the truth – after all it was published in a ‘peer-reviewed’ medical journal!
My conclusions are as simple as they are severe:
- Such pilot studies are the result of gross incompetence on many levels (researchers, funders, ethics committees, reviewers, journal editors).
- They can cause considerable harm, because they mislead many people.
- In more than one way, they represent a violation of medical ethics.
- The could be considered scientific misconduct.
- We should think of stopping this increasingly common form of scientific misconduct.
In recent days, journalists across the world had a field day (mis)reporting that doctors practising integrative medicine were doing something positive after all. I think that the paper shows nothing of the kind – but please judge for yourself.
The authors of this article wanted to determine differences in antibiotic prescription rates between conventional General Practice (GP) surgeries and GP surgeries employing general practitioners (GPs) additionally trained in integrative medicine (IM) or complementary and alternative medicine (CAM) (referred to as IM GPs) working within National Health Service (NHS) England.
They conducted a retrospective study on antibiotic prescription rates per STAR-PU (Specific Therapeutic group Age–sex weighting Related Prescribing Unit) using NHS Digital data over 2016. Publicly available data were used on prevalence of relevant comorbidities, demographics of patient populations and deprivation scores. setting Primary Care. Participants were 7283 NHS GP surgeries in England. The association between IM GPs and antibiotic prescribing rates per STAR-PU with the number of antibiotic prescriptions (total, and for respiratory tract infection (RTI) and urinary tract infection (UTI) separately) as outcome. results IM GP surgeries (n=9) were comparable to conventional GP surgeries in terms of list sizes, demographics, deprivation scores and comorbidity prevalence.
Statistically significant fewer total antibiotics were prescribed at NHS IM GP surgeries compared with conventional NHS GP surgeries. In contrast, the number of antibiotics prescribed for UTI were similar between both practices.
The authors concluded that NHS England GP surgeries employing GPs additionally trained in IM/CAM have lower antibiotic prescribing rates. Accessibility of IM/CAM within NHS England primary care is limited. Main study limitation is the lack of consultation data. Future research should include the differences in consultation behaviour of patients self-selecting to consult an IM GP or conventional surgery, and its effect on antibiotic prescription. Additional treatment strategies for common primary care infections used by IM GPs should be explored to see if they could be used to assist in the fight against antimicrobial resistance.
The study was flimsy to say the least:
- It was retrospective and is therefore open to no end of confounders.
- There were only 9 surgeries in the IM group.
Moreover, the results were far from impressive. The differences in antibiotic prescribing between the two groups of GP surgeries were minimal or non-existent. Finally, the study was financed via an unrestricted grant of WALA Heilmittel GmbH, Germany (“approx. 900 different remedies conforming to the anthroposophic understanding of man and nature”) and its senior author has a long track record of publishing papers promotional for anthroposophic medicine.
Such pseudo-research seems to be popular in the realm of CAM, and I have commented before on similarly futile projects. The comparison, I sometimes use is that of a Hamburger restaurant:
Employees by a large Hamburger chain set out to study the association between utilization of Hamburger restaurant services and vegetarianism. The authors used a retrospective cohort design. The study population comprised New Hampshire residents aged 18-99 years, who had entered the premises of a Hamburger restaurant within 90 days for a primary purpose of eating. The authors excluded subjects with a diagnosis of cancer. They measured the likelihood of vegetarianism among recipients of services delivered by Hamburger restaurants compared with a control group of individuals not using meat-dispensing facilities. They also compared the cohorts with regard to the money spent in Hamburger restaurants. The adjusted likelihood of being a vegetarian was 55% lower among the experimental group compared to controls. The average money spent per person in Hamburger restaurants were also significantly lower among the Hamburger group.
To me, it is obvious that such analyses must produce a seemingly favourable result for CAM. In the present case, there are several reasons for this:
- GPs who volunteer to be trained in CAM tend to be in favour of ‘natural’ treatments and oppose synthetic drugs such as antibiotics.
- Education in CAM would only re-inforce this notion.
- Similarly, patients electing to consult IM GPs tend to be in favour of ‘natural’ treatments and oppose synthetic drugs such as antibiotics.
- Such patients might be less severely ill that the rest of the patient population (the data from the present study do in fact imply this to be true).
- These phenomena work in concert to generate less antibiotic prescribing in the IM group.
In the final analysis, all this finding amounts to is a self-fulfilling prophecy: grocery shops sell less meat than butchers! You don’t believe me? Perhaps you need to read a previous post then; it concluded that physicians practicing integrative medicine (the 80% who did not respond to the survey were most likely even worse) not only use and promote much quackery, they also tend to endanger public health by their bizarre, irrational and irresponsible attitudes towards vaccination.
What is upsetting with the present paper, in my view, are the facts that:
- a reputable journal published this junk,
- the international press has a field-day reporting this study implying that CAM is a good thing.
The fact is that it shows nothing of the kind. Imagine we send GPs on a course where they are taught to treat all their patients with blood-letting. This too would result in less prescription of antibiotics, wouldn’t it? But would it be a good thing? Of course not!
True, we prescribe too much antibiotics. Nobody doubts that. And nobody doubts that it is a big problem. The solution to this problem is not more CAM, but less antibiotics. To realise the solution we do not need to teach GPs CAM but we need to remind them of the principles of evidence-based practice. And the two are clearly not the same; in fact, they are opposites.
As I often said, I find it regrettable that sceptics often say THERE IS NOT A SINGLE STUDY THAT SHOWS HOMEOPATHY TO BE EFFECTIVE (or something to that extent). This is quite simply not true, and it gives homeopathy-fans the occasion to suggest sceptics wrong. The truth is that THE TOTALITY OF THE MOST RELIABLE EVIDENCE FAILS TO SUGGEST THAT HIGHLY DILUTED HOMEOPATHIC REMEDIES ARE EFFECTIVE BEYOND PLACEBO. As a message for consumers, this is a little more complex, but I believe that it’s worth being well-informed and truthful.
And that also means admitting that a few apparently rigorous trials of homeopathy exist and some of them show positive results. Today, I want to focus on this small set of studies.
How can a rigorous trial of a highly diluted homeopathic remedy yield a positive result? As far as I can see, there are several possibilities:
- Homeopathy does work after all, and we have not fully understood the laws of physics, chemistry etc. Homeopaths favour this option, of course, but I find it extremely unlikely, and most rational thinkers would discard this possibility outright. It is not that we don’t quite understand homeopathy’s mechanism; the fact is that we understand that there cannot be a mechanism that is in line with the laws of nature.
- The trial in question is the victim of some undetected error.
- The result has come about by chance. Of 100 trials, 5 would produce a positive result at the 5% probability level purely by chance.
- The researchers have cheated.
When we critically assess any given trial, we attempt, in a way, to determine which of the 4 solutions apply. But unfortunately we always have to contend with what the authors of the trial tell us. Publications never provide all the details we need for this purpose, and we are often left speculating which of the explanations might apply. Whatever it is, we assume the result is false-positive.
Naturally, this assumption is hard to accept for homeopaths; they merely conclude that we are biased against homeopathy and conclude that, however, rigorous a study of homeopathy is, sceptics will not accept its result, if it turns out to be positive.
But there might be a way to settle the argument and get some more objective verdict, I think. We only need to remind ourselves of a crucially important principle in all science: INDEPENDENT REPLICATION. To be convincing, a scientific paper needs to provide evidence that the results are reproducible. In medicine, it unquestionably is wise to accept a new finding only after it has been confirmed by other, independent researchers. Only if we have at least one (better several) independent replications, can we be reasonably sure that the result in question is true and not false-positive due to bias, chance, error or fraud.
And this is, I believe, the extremely odd phenomenon about the ‘positive’ and apparently rigorous studies of homeopathic remedies. Let’s look at the recent meta-analysis of Mathie et al. The authors found several studies that were both positive and fairly rigorous. These trials differ in many respects (e. g. remedies used, conditions treated) but they have, as far as I can see, one important feature in common: THEY HAVE NOT BEEN INDEPENDENTLY REPLICATED.
If that is not astounding, I don’t know what is!
Think of it: faced with a finding that flies in the face of science and would, if true, revolutionise much of medicine, scientists should jump with excitement. Yet, in reality, nobody seems to take the trouble to check whether it is the truth or an error.
To explain this absurdity more fully, let’s take just one of these trials as an example, one related to a common and serious condition: COPD
The study is by Prof Frass and was published in 2005 – surely long enough ago for plenty of independent replications to emerge. Its results showed that potentized (C30) potassium dichromate decreases the amount of tracheal secretions was reduced, extubation could be performed significantly earlier, and the length of stay was significantly shorter. This is a scientific as well as clinical sensation, if there ever was one!
The RCT was published in one of the leading journals on this subject (Chest) which is read by most specialists in the field, and it was at the time widely reported. Even today, there is hardly an interview with Prof Frass in which he does not boast about this trial with truly sensational results (only last week, I saw one). If Frass is correct, his findings would revolutionise the lives of thousands of seriously suffering patients at the very brink of death. In other words, it is inconceivable that Frass’ result has not been replicated!
But it hasn’t; at least there is nothing in Medline.
Why not? A risk-free, cheap, universally available and easy to administer treatment for such a severe, life-threatening condition would normally be picked up instantly. There should not be one, but dozens of independent replications by now. There should be several RCTs testing Frass’ therapy and at least one systematic review of these studies telling us clearly what is what.
But instead there is a deafening silence.
For heaven sakes, why?
The only logical explanation is that many centres around the world did try Frass’ therapy. Most likely they found it does not work and soon dismissed it. Others might even have gone to the trouble of conducting a formal study of Frass’ ‘sensational’ therapy and found it to be ineffective. Subsequently they felt too silly to submit it for publication – who would not laugh at them, if they said they trailed a remedy that was diluted 1: 1000000000000000000000000000000000000000000000000000000000000 and found it to be worthless? Others might have written up their study and submitted it for publication, but got rejected by all reputable journals in the field because the editors felt that comparing one placebo to another placebo is not real science.
And this is roughly, how it went with the other ‘positive’ and seemingly rigorous studies of homeopathy as well, I suspect.
Regardless of whether I am correct or not, the fact is that there are no independent replications (if readers know any, please let me know).
Once a sufficiently long period of time has lapsed and no replications of a ‘sensational’ finding did not emerge, the finding becomes unbelievable or bogus – no rational thinker can possibly believe such a results (I for one have not yet met an intensive care specialist who believes Frass’ findings, for instance). Subsequently, it is quietly dropped into the waste-basket of science where it no longer obstructs progress.
The absence of independent replications is therefore a most useful mechanism by which science rids itself of falsehoods.
It seems that homeopathy is such a falsehood.
The plethora of dodgy meta-analyses in alternative medicine has been the subject of a recent post – so this one is a mere update of a regular lament.
This new meta-analysis was to evaluate evidence for the effectiveness of acupuncture in the treatment of lumbar disc herniation (LDH). (Call me pedantic, but I prefer meta-analyses that evaluate the evidence FOR AND AGAINST a therapy.) Electronic databases were searched to identify RCTs of acupuncture for LDH, and 30 RCTs involving 3503 participants were included; 29 were published in Chinese and one in English, and all trialists were Chinese.
The results showed that acupuncture had a higher total effective rate than lumbar traction, ibuprofen, diclofenac sodium and meloxicam. Acupuncture was also superior to lumbar traction and diclofenac sodium in terms of pain measured with visual analogue scales (VAS). The total effective rate in 5 trials was greater for acupuncture than for mannitol plus dexamethasone and mecobalamin, ibuprofen plus fugui gutong capsule, loxoprofen, mannitol plus dexamethasone and huoxue zhitong decoction, respectively. Two trials showed a superior effect of acupuncture in VAS scores compared with ibuprofen or mannitol plus dexamethasone, respectively.
The authors from the College of Traditional Chinese Medicine, Jinan University, Guangzhou, Guangdong, China, concluded that acupuncture showed a more favourable effect in the treatment of LDH than lumbar traction, ibuprofen, diclofenac sodium, meloxicam, mannitol plus dexamethasone and mecobalamin, fugui gutong capsule plus ibuprofen, mannitol plus dexamethasone, loxoprofen and huoxue zhitong decoction. However, further rigorously designed, large-scale RCTs are needed to confirm these findings.
Why do I call this meta-analysis ‘dodgy’? I have several reasons, 10 to be exact:
- There is no plausible mechanism by which acupuncture might cure LDH.
- The types of acupuncture used in these trials was far from uniform and included manual acupuncture (MA) in 13 studies, electro-acupuncture (EA) in 10 studies, and warm needle acupuncture (WNA) in 7 studies. Arguably, these are different interventions that cannot be lumped together.
- The trials were mostly of very poor quality, as depicted in the table above. For instance, 18 studies failed to mention the methods used for randomisation. I have previously shown that some Chinese studies use the terms ‘randomisation’ and ‘RCT’ even in the absence of a control group.
- None of the trials made any attempt to control for placebo effects.
- None of the trials were conducted against sham acupuncture.
- Only 10 studies 10 trials reported dropouts or withdrawals.
- Only two trials reported adverse reactions.
- None of these shortcomings were critically discussed in the paper.
- Despite their affiliation, the authors state that they have no conflicts of interest.
- All trials were conducted in China, and, on this blog, we have discussed repeatedly that acupuncture trials from China never report negative results.
And why do I find the journal ‘dodgy’?
Because any journal that publishes such a paper is likely to be sub-standard. In the case of ‘Acupuncture in Medicine’, the official journal of the British Medical Acupuncture Society, I see such appalling articles published far too frequently to believe that the present paper is just a regrettable, one-off mistake. What makes this issue particularly embarrassing is, of course, the fact that the journal belongs to the BMJ group.
… but we never really thought that science publishing was about anything other than money, did we?
A few days ago, the German TV ‘FACT’ broadcast a film (it is in German, the bit on homeopathy starts at ~min 20) about a young woman who had her breast cancer first operated but then decided to forfeit subsequent conventional treatments. Instead she chose homeopathy which she received from Dr Jens Wurster at the ‘Clinica Sta Croce‘ in Lucano/Switzerland.
Elsewhere Dr Wurster stated this: Contrary to chemotherapy and radiation, we offer a therapy with homeopathy that supports the patient’s immune system. The basic approach of orthodox medicine is to consider the tumor as a local disease and to treat it aggressively, what leads to a weakening of the immune system. However, when analyzing all studies on cured cancer cases it becomes evident that the immune system is always the decisive factor. When the immune system is enabled to recognize tumor cells, it will also be able to combat them… When homeopathic treatment is successful in rebuilding the immune system and reestablishing the basic regulation of the organism then tumors can disappear again. I’ve treated more than 1000 cancer patients homeopathically and we could even cure or considerably ameliorate the quality of life for several years in some, advanced and metastasizing cases.
The recent TV programme showed a doctor at this establishment confirming that homeopathy alone can cure cancer. Dr Wurster (who currently seems to be a star amongst European homeopaths) is seen lecturing at the 2017 World Congress of Homeopathic Physicians in Leipzig and stating that a ‘particularly rigorous study’ conducted by conventional scientists (the senior author is Harald Walach!, hardly a conventional scientist in my book) proved homeopathy to be effective for cancer. Specifically, he stated that this study showed that ‘homeopathy offers a great advantage in terms of quality of life even for patients suffering from advanced cancers’.
This study did, of course, interest me. So, I located it and had a look. Here is the abstract:
Many cancer patients seek homeopathy as a complementary therapy. It has rarely been studied systematically, whether homeopathic care is of benefit for cancer patients.
We conducted a prospective observational study with cancer patients in two differently treated cohorts: one cohort with patients under complementary homeopathic treatment (HG; n = 259), and one cohort with conventionally treated cancer patients (CG; n = 380). For a direct comparison, matched pairs with patients of the same tumour entity and comparable prognosis were to be formed. Main outcome parameter: change of quality of life (FACT-G, FACIT-Sp) after 3 months. Secondary outcome parameters: change of quality of life (FACT-G, FACIT-Sp) after a year, as well as impairment by fatigue (MFI) and by anxiety and depression (HADS).
HG: FACT-G, or FACIT-Sp, respectively improved statistically significantly in the first three months, from 75.6 (SD 14.6) to 81.1 (SD 16.9), or from 32.1 (SD 8.2) to 34.9 (SD 8.32), respectively. After 12 months, a further increase to 84.1 (SD 15.5) or 35.2 (SD 8.6) was found. Fatigue (MFI) decreased; anxiety and depression (HADS) did not change. CG: FACT-G remained constant in the first three months: 75.3 (SD 17.3) at t0, and 76.6 (SD 16.6) at t1. After 12 months, there was a slight increase to 78.9 (SD 18.1). FACIT-Sp scores improved significantly from t0 (31.0 – SD 8.9) to t1 (32.1 – SD 8.9) and declined again after a year (31.6 – SD 9.4). For fatigue, anxiety, and depression, no relevant changes were found. 120 patients of HG and 206 patients of CG met our criteria for matched-pairs selection. Due to large differences between the two patient populations, however, only 11 matched pairs could be formed. This is not sufficient for a comparative study.
In our prospective study, we observed an improvement of quality of life as well as a tendency of fatigue symptoms to decrease in cancer patients under complementary homeopathic treatment. It would take considerably larger samples to find matched pairs suitable for comparison in order to establish a definite causal relation between these effects and homeopathic treatment.
Even the abstract makes several points very clear, and the full text confirms further embarrassing details:
- The patients in this study received homeopathy in addition to standard care (the patient shown in the film only had homeopathy until it was too late, and she subsequently died, aged 33).
- The study compared A+B with B alone (A=homeopathy, B= standard care). It is hardly surprising that the additional attention of A leads to an improvement in quality of life. It is arguably even unethical to conduct a clinical trial to demonstrate such an obvious outcome.
- The authors of this paper caution that it is not possible to conclude that a causal relationship between homeopathy and the outcome exists.
- This is true not just because of the small sample size, but also because of the fact that the two groups had not been allocated randomly and therefore are bound to differ in a whole host of variables that have not or cannot be measured.
- Harald Walach, the senior author of this paper, held a position which was funded by Heel, Baden-Baden, one of Germany’s largest manufacturer of homeopathics.
- The H.W.& J.Hector Foundation, Germany, and the Samueli Institute, provided the funding for this study.
In the film, one of the co-authors of this paper, the oncologist HH Bartsch from Freiburg, states that Dr Wurster’s interpretation of this study is ‘dishonest’.
I am inclined to agree.
The question whether spinal manipulative therapy (SMT) has any specific therapeutic effects is still open. This fact must irritate ardent chiropractors, and they therefore try everything to dispel our doubts. One way would be to demonstrate a dose-effect relationship between SMT and the clinical outcome. But, for several reasons, this is not an easy task.
This RCT was aimed at identifying the dose-response relationship between visits for SMT and chronic cervicogenic headache (CGH) outcomes; to evaluate the efficacy of SMT by comparison with a light massage control.
The study included 256 adults with chronic CGH. The primary outcome was days with CGH in the prior 4 weeks evaluated at the 12- and 24-week primary endpoints. Secondary outcomes included CGH days at remaining endpoints, pain intensity, disability, perceived improvement, medication use, and patient satisfaction. Participants were randomized to 4 different dose levels of chiropractic SMT: 0, 6, 12, or 18 sessions. They were treated 3 times per week for 6 weeks and received a focused light-massage control at sessions when SMT was not assigned. Linear dose effects and comparisons to the no-manipulation control group were evaluated at 6, 12, 24, 39, and 52 weeks.
A linear dose-response was observed for all follow-ups, a reduction of approximately 1 CGH day/4 weeks per additional 6 SMT visits (p<.05); a maximal effective dose could not be determined. CGH days/4 weeks were reduced from about 16 to 8 for the highest and most effective dose of 18 SMT visits. Mean differences in CGH days/4 weeks between 18 SMT visits and control were -3.3 (p=.004) and -2.9 (p=.017) at the primary endpoints, and similar in magnitude at the remaining endpoints (p<.05). Differences between other SMT doses and control were smaller in magnitude (p > .05). CGH intensity showed no important improvement nor differed by dose. Other secondary outcomes were generally supportive of the primary.
The authors concluded that there was a linear dose-response relationship between SMT visits and days with CGH. For the highest and most effective dose of 18 SMT visits, CGH days were reduced by half, and about 3 more days per month than for the light-massage control.
This trial would make sense, if the effectiveness of SMT for CGH had been a well-documented fact, and if the study had rigorously controlled for placebo-effects.
But guess what?
Neither of these conditions were met.
A recent review concluded that there are few published randomized controlled trials analyzing the effectiveness of spinal manipulation and/or mobilization for TTH, CeH, and M in the last decade. In addition, the methodological quality of these papers is typically low. Clearly, there is a need for high-quality randomized controlled trials assessing the effectiveness of these interventions in these headache disorders. And this is by no means the only article making such statements; similar reviews arrive at similar conclusions. In turn, this means that the effects observed after SMT are not necessarily specific effects due to SMT but could easily be due to placebo or other non-specific effects. In order to avoid confusion, one would need a credible placebo – one that closely mimics SMT – and make sure that patients were ‘blinded’. But ‘light massage’ clearly does not mimic SMT, and patients obviously were aware of which interventions they received.
So, an alternative – and I think at least as plausible – conclusion of the data provided by this new RCT is this:
Chiropractic SMT is associated with a powerful placebo response which, of course, obeys a dose-effect relationship. Thus these findings are in keeping with the notion that SMT is a placebo.
And why would the researchers – who stress that they have no conflicts of interest – mislead us by making this alternative interpretation of their findings not abundantly clear?
I fear, the reason might be simple: they also seem to mislead us about their conflicts of interest: they are mostly chiropractors with a long track record of publishing promotional papers masquerading as research. What, I ask myself, could be a stronger conflict of interest?
(Pity that a high-impact journal like SPINE did not spot these [not so little] flaws)
Sipjeondaebo-tang is an East Asian herbal supplement containing Angelica root (Angelicae Gigantis Radix), the rhizome of Cnidium officinale Makino (Cnidii Rhizoma), Radix Paeoniae, Rehmannia glutinosa root (Rehmanniae Radix Preparata), Ginseng root (Ginseng Radix Alba), Atractylodes lancea root (Atractylodis Rhizoma Alba), the dried sclerotia of Poria cocos (Poria cocos Sclerotium), Licorice root (Glycyrrhizae Radix), Astragalus root (Astragali Radix), and the dried bark of Cinnamomum verum (Cinnamomi Cortex).
But does this herbal mixture actually work? Korean researchers wanted to find out.
The purpose of their study was to examine the feasibility of Sipjeondaebo-tang (Juzen-taiho-to, Shi-Quan-Da-Bu-Tang) for cancer-related anorexia. A total of 32 participants with cancer anorexia were randomized to either Sipjeondaebo-tang group or placebo group. Participants were given 3 g of Sipjeondaebo-tang or placebo 3 times a day for 4 weeks. The primary outcome was a change in the Anorexia/Cachexia Subscale of Functional Assessment of Anorexia/Cachexia Therapy (FAACT). The secondary outcomes included Visual Analogue Scale (VAS) of anorexia, FAACT scale, and laboratory tests.
The results showed that anorexia and quality of life measured by FAACT and VAS were improved after 4 weeks of Sipjeondaebo-tang treatment. However, there was no significant difference between changes of Sipjeondaebo-tang group and placebo group.
From this, the authors of the study concluded that sipjeondaebo-tang appears to have potential benefit for anorexia management in patients with cancer. Further large-scale studies are needed to ensure the efficacy.
Well, isn’t this just great? Faced with a squarely negative result, one simply ignores it and draws a positive conclusion!
As we all know – and as trialists certainly must know – controlled trials are designed to compare the outcomes of two groups. Changes within one of the groups can be caused by several factors unrelated to the therapy and are therefore largely irrelevant. This means that “no significant difference between changes of Sipjeondaebo-tang group and placebo group” indicates that the herbal mixture had no effect. In turn this means that a conclusion stating that “sipjeondaebo-tang appears to have potential benefit for anorexia” is just fraudulent.
This level of scientific misconduct is remarkable, even for the notoriously poor Evid Based Complement Alternat Med.
I strongly suggest that:
- The journal is de-listed from Medline because similarly misleading nonsense has been coming out of this rag for some time.
- The paper is withdrawn because it can only mislead vulnerable patients.
Cranio-sacral therapy is firstly implausible, and secondly it lacks evidence of effectiveness (see for instance here, here, here and here). Yet, some researchers are nevertheless not deterred to test it in clinical trials. While this fact alone might be seen as embarrassing, the study below is a particular and personal embarrassment to me, in fact, I am shocked by it and write these lines with considerable regret.
Why? Bear with me, I will explain later.
The purpose of this trial was to evaluate the effectiveness of osteopathic manipulative treatment and osteopathy in the cranial field in temporomandibular disorders. Forty female subjects with temporomandibular disorders lasting at least three months were included. At enrollment, subjects were randomly assigned into two groups: (1) osteopathic manipulative treatment group (n=20) and (2) osteopathy in the cranial field [craniosacral therapy for you and me] group (n=20). Examinations were performed at baseline (E0) and at the end of the last treatment (E1), and consisted of subjective pain intensity with the Visual Analog Scale, Helkimo Index and SF-36 Health Survey. Subjects had five treatments, once a week. 36 subjects completed the study.
Patients in both groups showed significant reduction in Visual Analog Scale score (osteopathic manipulative treatment group: p = 0.001; osteopathy in the cranial field group: p< 0.001), Helkimo Index (osteopathic manipulative treatment group: p = 0.02; osteopathy in the cranial field group: p = 0.003) and a significant improvement in the SF-36 Health Survey – subscale “Bodily Pain” (osteopathic manipulative treatment group: p = 0.04; osteopathy in the cranial field group: p = 0.007) after five treatments (E1). All subjects (n = 36) also showed significant improvements in the above named parameters after five treatments (E1): Visual Analog Scale score (p< 0.001), Helkimo Index (p< 0.001), SF-36 Health Survey – subscale “Bodily Pain” (p = 0.001). The differences between the two groups were not statistically significant for any of the three endpoints.
The authors concluded that both therapeutic modalities had similar clinical results. The findings of this pilot trial support the use of osteopathic manipulative treatment and osteopathy in the cranial field as an effective treatment modality in patients with temporomandibular disorders. The positive results in both treatment groups should encourage further research on osteopathic manipulative treatment and osteopathy in the cranial field and support the importance of an interdisciplinary collaboration in patients with temporomandibular disorders. Implications for rehabilitation Temporomandibular disorders are the second most prevalent musculoskeletal condition with a negative impact on physical and psychological factors. There are a variety of options to treat temporomandibular disorders. This pilot study demonstrates the reduction of pain, the improvement of temporomandibular joint dysfunction and the positive impact on quality of life after osteopathic manipulative treatment and osteopathy in the cranial field. Our findings support the use of osteopathic manipulative treatment and osteopathy in the cranial field and should encourage further research on osteopathic manipulative treatment and osteopathy in the cranial field in patients with temporomandibular disorders. Rehabilitation experts should consider osteopathic manipulative treatment and osteopathy in the cranial field as a beneficial treatment option for temporomandibular disorders.
This study has so many flaws that I don’t know where to begin. Here are some of the more obvious ones:
- There is, as already mentioned, no rationale for this study. I can see no reason why craniosacral therapy should work for the condition. Without such a rationale, the study should never even have been conceived.
- Technically, this RCTs an equivalence study comparing one therapy against another. As such it needs to be much larger to generate a meaningful result and it also would require a different statistical approach.
- The authors mislabelled their trial a ‘pilot study’. However, a pilot study “is a preliminary small-scale study that researchers conduct in order to help them decide how best to conduct a large-scale research project. Using a pilot study, a researcher can identify or refine a research question, figure out what methods are best for pursuing it, and estimate how much time and resources will be necessary to complete the larger version, among other things.” It is not normally a study suited for evaluating the effectiveness of a therapy.
- Any trial that compares one therapy of unknown effectiveness to another of unknown effectiveness is a complete and utter nonsense. Equivalent studies can only ever make sense, if one of the two treatments is of proven effectiveness – think of it as a mathematical equation: one equation with two unknowns is unsolvable.
- Controlled studies such as RCTs are for comparing the outcomes of two or more groups, and only between-group differences are meaningful results of such trials.
- The ‘positive results’ which the authors mention in their conclusions are meaningless because they are based on such within-group changes and nobody can know what caused them: the natural history of the condition, regression towards the mean, placebo-effects, or other non-specific effects – take your pick.
- The conclusions are a bonanza of nonsensical platitudes and misleading claims which do not follow from the data.
As regular readers of this blog will doubtlessly have noticed, I have seen plenty of similarly flawed pseudo-research before – so, why does this paper upset me so much? The reason is personal, I am afraid: even though I do not know any of the authors in person, I know their institution more than well. The study comes from the Department of Physical Medicine and Rehabilitation, Medical University of Vienna, Austria. I was head of this department before I left in 1993 to take up the Exeter post. And I had hoped that, even after 25 years, a bit of the spirit, attitude, knowhow, critical thinking and scientific rigor – all of which I tried so hard to implant in my Viennese department at the time – would have survived.
Perhaps I was wrong.
Many hard-nosed sceptics might claim that there is no herbal treatment for upper respiratory infections that makes the slightest difference difference. But is this assumption really correct?
According to my own research of 2004, it is not. Here is the abstract of our systematic review:
Acute respiratory infections represent a significant cause of over-prescription of antibiotics and are one of the major reasons for absence from work. The leaves of Andrographis paniculata (Burm. f.) Wall ex Nees (Acanthaceae) are used as a medicinal herb in the treatment of infectious diseases. Systematic literature searches were conducted in six computerised databases and the reference lists of all papers located were checked for further relevant publications. Information was also requested from manufacturers, the spontaneous reporting schemes of the World Health Organisation and national drug safety bodies. No language restrictions were imposed. Seven double-blind, controlled trials (n = 896) met the inclusion criteria for evaluation of efficacy. All trials scored at least three, out of a maximum of five, for methodological quality on the Jadad scale. Collectively, the data suggest that A. paniculata is superior to placebo in alleviating the subjective symptoms of uncomplicated upper respiratory tract infection. There is also preliminary evidence of a preventative effect. Adverse events reported following administration of A. paniculata were generally mild and infrequent. There were few spontaneous reports of adverse events. A. paniculata may be a safe and efficacious treatment for the relief of symptoms of uncomplicated upper respiratory tract infection; more research is warranted.
A. Paniculata (Burm.f.) Wall ex Nees (Acanthaceae family), also known as nemone chinensi, Chuān Xīn Lián, has traditionally been used in Indian and Chinese herbal medicine mostly as an antipyretic for relieving and reducing the severity and duration of symptoms of common colds and alleviating fever, cough and sore throats, or as a tonic to aid convalescence after uncomplicated respiratory tract infections. The active constituents of A. paniculata include the diterpene, lactones commonly known as the andrographolides which have shown anti-inflammatory, antiviral, anti-allergic, and immune-stimulatory activities. A. Paniculata has also been shown, in vitro, to be effective against avian influenza A (H9N2 and H5N1) and human influenza A H1N1 viruses, possibly through blocking the binding of viral hemagglutinin to cells, or by inhibiting H1N1 virus-induced cell death.
But our systematic review was published 14 years ago!
We need more up-to-date information!
And I am pleased to report that a recent paper provided exactly that.
This systematic review included published and unpublished RCTs. Quasi-RCTs, crossover trials, controlled before and after studies, interrupted time series (ITS) studies, and non-experimental studies were not included due to their potential high risk of bias.
Thirty-three trials involving 7175 patients with ARTIs were included. Their methodological quality was restricted as randomisation was not well documented; 73% of the trials included were not blinded; where ITT analysis were performed, loss to follow-up data were counted as no effect; and most trials were published without a protocol available.
Findings suggested limited but consistent evidence that A. Paniculata improved cough and sore throat when compared with placebo. A. Paniculata (alone or plus usual care) had a statistically significant effect in improving overall symptoms of ARTIs when compared to placebo, usual care, and other herbal therapies. A. Paniculata in pillule tended to be more effective in improving overall symptoms over A. Paniculata in tablet. Evidence also suggested that A. Paniculata (alone or plus usual care) shortens the duration of cough, sore throat and sick leave/time to resolution when compared versus usual care. Reduction in antibiotic usage was seldom evaluated in the included trials.
The authors concluded that A. Paniculata appears beneficial and safe for relieving ARTI symptoms and shortening time to symptom resolution. However, these findings should be interpreted cautiously owing to poor study quality and heterogeneity. Well-designed trials evaluating the effectiveness and potential to reduce antibiotic use of A. Paniculata are warranted.
In case you wonder about conflicts of interest: there were none with my 2004 paper, and the authors of the new review state that this paper presents independent research funded by the National Institute for Health Research School for Primary Care Research (NIHR SPCR). The views expressed are those of the author(s) and not necessarily those of the NIHR, the NHS or the Department of Health.
Yes, the RCTs are not all of top quality.
And yes, the effect size is not huge.
But maybe – just maybe – we do have here an alternative therapy that does help against a condition for which conventional drugs are fairly useless!?!