critical thinking
Do chiropractors even know the difference between promotion and research?
Probably a rhetorical question.
Personally, I have seen them doing so much pseudo-research that I doubt they recognise the real thing, even if they fell over it.
Here is a recent example that stands for many, many more such ‘research’ projects (some of which have been discussed on this blog).
But first a few sentences on the background of this new ‘study’.
The UD chiropractic profession is currently on the ‘opioid over-use bandwagon’ hoping that this move might promote their trade. Most chiropractors have always been against using (any type of) pharmaceutical treatment and advise their patients accordingly. D D Palmer, the founder of chiropractic, was adamant that drugs are to be avoided; he stated for instance that Drugs are delusive; they do not adjust anything. And “as the Founder intended, chiropractic has existed as a drug-free healthcare profession for better than 120 years.” To this day, chiropractors are educated and trained to argue against non-drug treatments and regularly claim that chiropractic is a drug-free alternative to traditional medicine.
Considering this background, this new piece of (pseudo) research is baffling, in my view.
The objective of this investigation was to evaluate the association between utilization of chiropractic services and the use of prescription opioid medications. The authors used a retrospective cohort design to analyse health insurance claims data. The data source was the all payer claims database administered by the State of New Hampshire. The authors chose New Hampshire because health claims data were readily available for research, and in 2015, New Hampshire had the second-highest age-adjusted rate of drug overdose deaths in the United States.
The study population comprised New Hampshire residents aged 18-99 years, enrolled in a health plan, and with at least two clinical office visits within 90 days for a primary diagnosis of low-back pain. The authors excluded subjects with a diagnosis of cancer. They measured likelihood of opioid prescription fill among recipients of services delivered by chiropractors compared with a control group of patients not consulting a chiropractor. They also compared the cohorts with regard to rates of prescription fills for opioids and associated charges.
The adjusted likelihood of filling a prescription for an opioid analgesic was 55% lower among chiropractic compared to non-chiropractic patients. Average charges per person for opioid prescriptions were also significantly lower among the former group.
The authors concluded that among New Hampshire adults with office visits for noncancer low-back pain, the likelihood of filling a prescription for an opioid analgesic was significantly lower for recipients of services delivered by doctors of chiropractic compared with nonrecipients. The underlying cause of this correlation remains unknown, indicating the need for further investigation.
The underlying cause remains unknown???
Really?
Let me speculate, or even better, let me extrapolate by drawing an analogy:
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.
The authors concluded that among New Hampshire adults visiting Hamburger restaurants, the likelihood of vegetarianism was significantly lower for consumers frequenting Hamburger restaurants compared with those who failed to frequent such places. The underlying cause of this correlation remains unknown, indicating the need for further investigation.
Daaaahhhhhhh!
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)
Lock 10 bright people into a room and tell them they will not be let out until they come up with the silliest idea in healthcare. It is not unlikely, I think, that they might come up with the concept of visceral osteopathy.
In case you wonder what visceral osteopathy (or visceral manipulation) is, one ‘expert’ explains it neatly: Visceral Osteopathy is an expansion of the general principles of osteopathy which includes a special understanding of the organs, blood vessels and nerves of the body (the viscera). Visceral Osteopathy relieves imbalances and restrictions in the interconnections between the motions of all the organs and structures of the body. Jean-Piere Barral RPT, DO built on the principles of Andrew Taylor Still DO and William Garner Sutherland DO, to create this method of detailed assessment and highly specific manipulation. Those who wish to practice Visceral Osteopathy train intensively through a series of post-graduate studies. The ability to address the specific visceral causes of somatic dysfunction allows the practitioner to address such conditions as gastroesophageal reflux disease (GERD), irritable bowel (IBS), and even infertility caused by mechanical restriction.
But, as I have pointed out many times before, the fact that a treatment is based on erroneous assumptions does not necessarily mean that it does not work. What we need to decide is evidence. And here we are lucky; a recent paper provides just that.
The purpose of this systematic review was to identify and critically appraise the scientific literature concerning the reliability of diagnosis and the clinical efficacy of techniques used in visceral osteopathy.
Only inter-rater reliability studies including at least two raters or the intra-rater reliability studies including at least two assessments by the same rater were included. For efficacy studies, only randomized-controlled-trials (RCT) or crossover studies on unhealthy subjects (any condition, duration and outcome) were included. Risk of bias was determined using a modified version of the quality appraisal tool for studies of diagnostic reliability (QAREL) in reliability studies. For the efficacy studies, the Cochrane risk of bias tool was used to assess their methodological design. Two authors performed data extraction and analysis.
Extensive searches located 8 reliability studies and 6 efficacy trials that could be included in this review. The analysis of reliability studies showed that the diagnostic techniques used in visceral osteopathy are unreliable. Regarding efficacy studies, the least biased study showed no significant difference for the main outcome. The main risks of bias found in the included studies were due to the absence of blinding of the examiners, an unsuitable statistical method or an absence of primary study outcome.
The authors (who by the way declared no conflicts of interest) concluded that the results of the systematic review lead us to conclude that well-conducted and sound evidence on the reliability and the efficacy of techniques in visceral osteopathy is absent.
It is hard not to appreciate the scientific rigor of this review or to agree with the conclusions drawn by the French authors.
But what consequences should we draw from all this?
The authors of this paper state that more and better research is needed. Somehow, I doubt this. Visceral osteopathy is not plausible and the best evidence available to date does not show it works. In my view, this means that we should declare it an obsolete aberration of medical history.
To this, the proponents of visceral osteopathy will probably say that they have tons of experience and have witnessed wonderful cures etc. This I do not doubt; however, the things they saw were not due to the effects of visceral osteopathy, they were due to chance, placebo, regression towards the mean, the natural history of the diseases treated etc., etc. And sometimes, experience is nothing more that the ability to repeat a mistake over and over again.
- If it looks like a placebo,
- if it behaves like a placebo,
- if it tests like a placebo,
IT MOST LIKELY IS A PLACEBO!!!
And what is wrong with a placebo, if it helps patients?
GIVE ME A BREAK!
WE HAVE ALREADY DISCUSSED THIS AD NAUSEAM. JUST READ SOME OF THE PREVIOUS POSTS ON THIS SUBJECT.
The ‘European Scientific Cooperative on Anthroposophic Medicinal Products‘ claim that there is a need for a regulatory framework for anthroposophic medicinal products (AMPs) in Europe. The existing regulatory requirements for conventional medicinal products are not appropriate for AMPs. Special registration procedures exist in some countries for homeopathic products and in the European Union for herbal products. However, these procedures only apply to a proportion of AMPs and the particular properties of AMPs are only in part accounted for. Suitable registration procedures especially for AMPs exist only in Germany and Switzerland.
The European Commission has acknowledged the existence of therapy systems, whose products have no adequate regulation, and it has proposed that the suitability of a separate legal framework for products of certain traditions such as Anthroposophic Medicine should be assessed. This statement should be seen in the context of developments in international trade, whereby representatives of therapy systems such as Traditional Chinese Medicine and Ayurveda wish to market their products in Europe.
It seems obvious that the safety of AMPs must be demonstrated, if regulators are to comply with the wishes of the AMP-industry. In other words, they require evidence. As luck has it, a recent paper provides just what they need.
The main objective of this analysis was to determine the frequency of adverse drug reactions (ADRs) to AMPs, relative to the number of AMP prescriptions.
The researchers conducted a prospective pharmacovigilance study with the patients of physicians in outpatient care in Germany. Diagnoses and prescriptions were extracted from the electronic medical records. A total of 38 German physicians trained in AM were asked to link all AMP prescriptions to the respective indications (diagnoses), and to document all serious ADRs as well as all ADRs of intensity III–IV. In addition, a subgroup of 7 ‘prescriber physicians’ agreed to also document all non-serious ADRs of any intensity. The study was conducted under routine care conditions with ADRs identified at ordinary follow-up consultations, without any additional scheduled follow-up visits. Physicians were remunerated with 15 Euro for each ADR report but not for their regular participation; patients received no remuneration. Patients were eligible for this analysis, if they had one or more AMP prescription in the years 2001–2010, followed by one or more physician visit.
A total of 44,662 patients with 311,731 AMP prescriptions, comprising 1722 different AMPs, were included. One hundred ADRs to AMPs occurred, caused by 83 different AMPs. ADR intensity was mild, moderate, and severe in 50% (n = 50/100), 43%, and 7% of cases, respectively; one ADR was serious. ADRs of any intensity occurred in 0.071% (n = 67/94,734) of AMP prescriptions and in 0.502% (n = 65/12,956) of patients prescribed AMPs. The highest ADR frequency was 0.290% of prescriptions for one specific AMP. Among all patients, serious ADRs occurred in 0.0003% (n = 1/311,731) of prescriptions and 0.0022% (n = 1/44,662) of patients.
The authors concluded that in this analysis from a large sample, ADRs to AMP therapy in outpatient care were rare; ADRs of high intensity as well as serious ADRs were very rare.
Most AMPs are highly diluted, and therefore, one would not expect frequent or serious ADRs. Yet, I still find these incidence figures mysterious. The reason is simple: even the ARDs of pure placebos (such as most AMPs) are known to be much more frequent. In other words, the nocebo-effects of drugs are much more common than these results seem to reflect.
This, I think, leads to one of two possible conclusions:
- AMPs are somehow miraculously exempt from the known facts of ADRs.
- There is something fundamentally wrong with this study.
I let you decide which is the case.
Oh, I almost forgot. At the end of this paper there is a not unimportant note:
The EvaMed study was funded by the Software AG-Stiftung. This analysis and publication was commissioned by the European Scientific Cooperative on Anthroposophic Medicinal Products (http://www.escamp.org) with financial support from foundations (Christophorus-Stiftung, Damus-Donata-Stiftung, Ekhagastiftelsen, Mahle-Stiftung, Software AG-Stiftung) and manufacturers (Wala, Weleda). The sponsors had no influence on the planning or conduct of the EvaMed study; the collection, preparation, analysis or interpretation of data for this paper; nor on the preparation, review or approval of the manuscript.
“MDs do not make false claims HAHAHA.”
This is from a comment I recently received on this blog.
It made me think.
Yes, of course, MDs do not always reveal the full truth to their patients; sometimes they might even tell lies (in this post, I shall use the term ‘lies’ for any kind of untruth).
So, what about these lies?
The first thing to say about them is obvious: THEY CAN NEVER JUSTIFY THE LIES OF OTHERS.
- the lies of the Tories cannot justify the lies of Labour party members,
- the lies of a plaintiff in court cannot justify any lies of the defendant,
- the lies of MDs cannot justify the lies of alternative practitioners.
The second thing to say about the lies of MDs is that, in my experience, most are told in the desire to protect patients. In some cases, this may be ill-advised or ethically questionable, but the motivation is nevertheless laudable.
- I might not tell the truth when I say (this really should be ‘said’, because I have not treated patients for many years) THIS WILL NOT HURT AT ALL. In the end, it hurt quite a bit but we all understand why I lied.
- I might claim that this treatment is sure to work (knowing full well that such a prediction is impossible), but we all know that I said so in order to maximise my patient’s compliance and expectation in order to generate the best possible outcome.
- I might dismiss a patient’s fear that his condition is incurable (while strongly suspecting that it is), but I would do this to improve his anxiety and well-being.
Yet, these are not the type of lies my commentator referred to. In fact, he provided a few examples of the lies MDs tell, in his opinion. He claimed that:
- They tell them that diabetes is not curable. False claim
- They compare egg intake with smoking on their affect to your health. False claim
- They say arthroscopic surgery of the knee is beneficial. False claim
- They state that surgery, chemo, and radiation is the only treatment for cancer. False claim
- They say that family association is the cause of most inflammatory conditions. False claim
I don’t want to go into the ‘rights or wrongs’ of these claims (mostly wrongs, as far as I can see). Instead, I would argue that any MD who makes a claim that is wrong behaves unethical and should retrain. If he erroneously assumes the claim to be correct, he is not fully informed (which, of course is unethical in itself) and needs to catch up with the current best evidence. If he makes a false claim knowing that it is wrong, he behaves grossly unethical and must justify himself in front of his professional disciplinary committee.
As this blog focusses on alternative medicine, let’s briefly consider the situation in that area. The commentator made his comments in connection to a post about chiropractic, so let’s look at the situation in chiropractic.
- Do many chiropractors claim to be able to treat a wide array of conditions without good evidence?
- Do they misadvise patients about conventional treatments, such as vaccinations?
- Do they claim that their spinal manipulations are safe?
- Do they tell patients they need regular ‘maintenance treatment’ to stay healthy?
- Do they claim to be able to diagnose subluxations?
- Do they pretend that subluxations cause illness and disease?
- Do they claim to adjust subluxations?
If you answered several of these questions with YES, I probably have made my point.
On reflection, it turns out that clinicians of all types do tell lies. Some are benign/white lies and others are fundamental, malignant lies. Most of us probably agree that the former category is largely negligible. The latter category can, however, be serious. In my experience, it is hugely more prevalent in the realm of alternative medicine. When it occurs in conventional medicine, appropriate measures are in place to prevent reoccurrence. When it occurs in alternative medicine, nobody seems to bat an eyelash.
My conclusion from these random thoughts: the truth is immeasurably valuable, and lies can be serious and often are damaging to patients. Therefore, we should always pursue those who tell serious lies, no matter whether they are MDs or alternative practitioners.
Yesterday, a press-release about our new book has been distributed by our publisher. As I hope than many regular readers of my blog might want to read this book – if you don’t want to buy it, please get it via your library – I decided to re-publish the press-release here:
Governments must legislate to regulate and restrict the sale of complementary and alternative therapies, conclude authors of new book More Harm Than Good.
Heidelberg, 20 February 2018
Commercial organisations selling lethal weapons or addictive substances clearly exploit customers, damage third parties and undermine genuine autonomy. Purveyors of complementary and alternative medicine (CAM) do too, argue authors Edzard Ernst and Kevin Smith.
The only downside to regulating such a controversial industry is that regulation could confer upon it an undeserved stamp of respectability and approval. At best, it can ensure the competent delivery of therapies that are inherently incompetent.
This is just one of the ethical dilemmas at the heart of the book. In all areas of healthcare, consumers are entitled to expect essential elements of medical ethics to be upheld. These include access to competent, appropriately-trained practitioners who base treatment decisions on evidence from robust scientific research. Such requirements are frequently neglected, ignored or wilfully violated in CAM.
“We would argue that a competent healthcare professional should be defined as one who practices or recommends plausible therapies that are supported by robust evidence,” says bioethicist Kevin Smith.
“Regrettably, the reality is that many CAM proponents allow themselves to be deluded as to the efficacy or safety of their chosen therapy, thus putting at risk the health of those who heed their advice or receive their treatment,” he says.
Therapies covered include homeopathy, acupuncture, chiropractic, iridology, Reiki, crystal healing, naturopathy, intercessory prayer, wet cupping, Bach flower therapy, Ukrain and craniosacral therapy. Their inappropriate use can not only raises false hope and inflicts financial hardship on consumers, but can also be dangerous; either through direct harm or because patients fail to receive more effective treatment. For example, advice given by homeopaths to diabetic patients has the potential to kill them; and when anthroposophic doctors advise against vaccination, they can be held responsible for measles outbreaks.
There are even ethical concerns to subjecting such therapies to clinical research. In mainstream medical research, a convincing database from pre-clinical research is accumulated before patients are experimented upon. However, this is mostly not possible with CAM. Pre-scientific forms of medicine have been used since time immemorial, but their persistence alone does not make them credible or effective. Some are based on notions so deeply implausible that accepting them is tantamount to believing in magic.
“Dogma and ideology, not rationality and evidence, are the drivers of CAM practice,” says Professor Edzard Ernst.
Edzard Ernst, Kevin Smith
More Harm than Good?
1st ed. 2018, XXV, 223 p.
Softcover $22.99, €19,99, £15.99 ISBN 978-3-319-69940-0
Also available as an eBook ISBN 978-3-319-69941-7
END OF PRESS RELEASE
As I already stated above, I hope you will read our new book. It offers something that has, I think, not been attempted before: it critically evaluates many aspects of alternative medicine by holding them to the ethical standards of medicine. Previously, we have often been asking WHERE IS THE EVIDENCE FOR THIS OR THAT CLAIM? In our book, we ask different questions: IS THIS OR THAT ASPECT OF ALTERNATIVE MEDICINE ETHICAL? Of course, the evidence question does come into this too, but our approach in this book is much broader.
The conclusions we draw are often surprising, sometimes even provocative.
Well, you will see for yourself (I hope).
The chiropractor Oakley Smith had graduated under D D Palmer in 1899. Smith was a former Iowa medical student who also had investigated Andrew Still’s osteopathy in Kirksville, before going to Palmer in Davenport. Eventually, Smith came to reject the Palmer concept of vertebral subluxation and developed his own concept of “the connective tissue doctrine” or naprapathy. Today, naprapathy is a popular form of manual therapy, particularly in Scandinavia and the US.
But what exactly is naprapathy? This website explains it quite well: Naprapathy is defined as a system of specific examination, diagnostics, manual treatment and rehabilitation of pain and dysfunction in the neuromusculoskeletal system. The therapy is aimed at restoring function through treatment of the connective tissue, muscle- and neural tissues within or surrounding the spine and other joints. Naprapathic treatment consists of combinations of manual techniques for instance spinal manipulation and mobilization, neural mobilization and Naprapathic soft tissue techniques, in additional to the manual techniques Naprapaths uses different types of electrotherapy, such as ultrasound, radial shockwave therapy and TENS. The manual techniques are often combined with advice regarding physical activity and ergonomics as well as medical rehabilitation training in order to decrease pain and disability and increase work ability and quality of life. A Dr. of Naprapathy is specialized in the diagnosis of structural and functional neuromusculoskeletal disorders, treatment and rehabilitation of patients with problems of such origin as well as to differentiate pain of other origin.
DOCTOR OF NAPRAPATHY? I hear you shout.
Yes, in the US, the title exists: The National College of Naprapathic Medicine is chartered by the State of Illinois and recognized by the State Board of Higher Education to grant the degree, Doctor of Naprapathy (D.N.). Graduates of the College are eligible to take the Naprapathic Medicine examination for licensure in the State of Illinois. The D.N. Degree requires:
- 66 hours – Basic Sciences
- 64 hours – Naprapathic Sciences
- 60 hours – Clinical Internship
Things become even stranger when we ask, what does the evidence show?
I found all of three clinical trials on Medline.
A 2016 clinical trial was designed to compare the treatment effect on pain intensity, pain related disability and perceived recovery from a) naprapathic manual therapy (spinal manipulation, spinal mobilization, stretching and massage) to b) naprapathic manual therapy without spinal manipulation and to c) naprapathic manual therapy without stretching for male and female patients seeking care for back and/or neck pain.
Participants were recruited among patients, ages 18-65, seeking care at the educational clinic of Naprapathögskolan – the Scandinavian College of Naprapathic Manual Medicine in Stockholm. The patients (n = 1057) were randomized to one of three treatment arms a) manual therapy (i.e. spinal manipulation, spinal mobilization, stretching and massage), b) manual therapy excluding spinal manipulation and c) manual therapy excluding stretching. The primary outcomes were minimal clinically important improvement in pain intensity and pain related disability. Treatments were provided by naprapath students in the seventh semester of eight total semesters. Generalized estimating equations and logistic regression were used to examine the association between the treatments and the outcomes.
At 12 weeks follow-up, 64% had a minimal clinically important improvement in pain intensity and 42% in pain related disability. The corresponding chances to be improved at the 52 weeks follow-up were 58% and 40% respectively. No systematic differences in effect when excluding spinal manipulation and stretching respectively from the treatment were found over 1 year follow-up, concerning minimal clinically important improvement in pain intensity (p = 0.41) and pain related disability (p = 0.85) and perceived recovery (p = 0.98). Neither were there disparities in effect when male and female patients were analyzed separately.
The authors concluded that the effect of manual therapy for male and female patients seeking care for neck and/or back pain at an educational clinic is similar regardless if spinal manipulation or if stretching is excluded from the treatment option.
Even though this study is touted as showing that naprapathy works by advocates, in all honesty, it tells us as good as nothing about the effect of naprapathy. The data are completely consistent with the interpretation that all of the outcomes were to the natural history of the conditions, regression towards the mean, placebo, etc. and entirely unrelated to any specific effects of naprapathy.
A 2010 study by the same group was to compare the long-term effects (up to one year) of naprapathic manual therapy and evidence-based advice on staying active regarding non-specific back and/or neck pain.
Subjects with non-specific pain/disability in the back and/or neck lasting for at least two weeks (n = 409), recruited at public companies in Sweden, were included in this pragmatic randomized controlled trial. The two interventions compared were naprapathic manual therapy such as spinal manipulation/mobilization, massage and stretching, (Index Group), and advice to stay active and on how to cope with pain, provided by a physician (Control Group). Pain intensity, disability and health status were measured by questionnaires.
89% completed the 26-week follow-up and 85% the 52-week follow-up. A higher proportion in the Index Group had a clinically important decrease in pain (risk difference (RD) = 21%, 95% CI: 10-30) and disability (RD = 11%, 95% CI: 4-22) at 26-week, as well as at 52-week follow-ups (pain: RD = 17%, 95% CI: 7-27 and disability: RD = 17%, 95% CI: 5-28). The differences between the groups in pain and disability considered over one year were statistically significant favoring naprapathy (p < or = 0.005). There were also significant differences in improvement in bodily pain and social function (subscales of SF-36 health status) favoring the Index Group.
The authors concluded that combined manual therapy, like naprapathy, is effective in the short and in the long term, and might be considered for patients with non-specific back and/or neck pain.
This study is hardly impressive either. The results are consistent with the interpretation that the extra attention and care given to the index group was the cause of the observed outcomes, unrelated to ant specific effects of naprapathy.
The last study was published in 2017 again by the same group. It was designed to compare naprapathic manual therapy with evidence-based care for back or neck pain regarding pain, disability, and perceived recovery.
Four hundred and nine patients with pain and disability in the back or neck lasting for at least 2 weeks, recruited at 2 large public companies in Sweden in 2005, were included in this randomized controlled trial. The 2 interventions were naprapathy, including spinal manipulation/mobilization, massage, and stretching (Index Group) and support and advice to stay active and how to cope with pain, according to the best scientific evidence available, provided by a physician (Control Group). Pain, disability, and perceived recovery were measured by questionnaires at baseline and after 3, 7, and 12 weeks.
At 7-week and 12-week follow-ups, statistically significant differences between the groups were found in all outcomes favoring the Index Group. At 12-week follow-up, a higher proportion in the naprapathy group had improved regarding pain [risk difference (RD)=27%, 95% confidence interval (CI): 17-37], disability (RD=18%, 95% CI: 7-28), and perceived recovery (RD=44%, 95% CI: 35-53). Separate analysis of neck pain and back pain patients showed similar results.
The authors thought that this trial suggests that combined manual therapy, like naprapathy, might be an alternative to consider for back and neck pain patients.
As the study suffers from the same limitations as the one above (in fact, it might be a different analysis of the same trial), they might be mistaken. I see no good reason to assume that any of the three studies provide good evidence for the effectiveness of naprapathy.
So, what should we conclude from all this?
If you ask me, naprapathy is something between chiropractic (without some of the woo) and physiotherapy (without its expertise). There is no good evidence that it works. Crucially, there is no evidence that it is superior to other therapeutic options.
I was going to finish on a positive note stating that ‘at least the ‘naprapathologists’ (I refuse to even consider the title of ‘doctor of naprapathy’) do not claim to treat conditions other than musculoskeletal problems’. But then I found this advertisement of a ‘naprapathologist’ on Twitter:
And now, I am going to finish by stating that A LOT OF NAPRAPATHY LOOKS VERY MUCH LIKE QUACKERY TO ME.
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.
Difficulties breastfeeding?
Some say that Chinese herbal medicine offers a solution.
This Chinese multi-centre RCT included 588 mothers considering breastfeeding. The intervention group received the Chinese herbal mixture Zengru Gao, while the control group received no therapy. The primary outcomes were the percentages of fully and partially breastfeeding mothers, and a secondary outcome was baby’s daily formula intake.
At day 3 and 7 after delivery, significant differences were found in favour of Zengru Gao group on the percentage of full/ partial breastfeeding. At day 7, the percentage of full/ partial breastfeeding of the active group increased to 71.48%/20.70% versus 58.67%/30.26% in the control group, the differences remained significant. No statistically significant differences were detected on primary measures at day. While intake of formula differed between groups at day 1 and 3, this difference did not achieve statistical significance, but this difference was apparent by day 7.
The authors concluded that the Chinese Herbal medicine Zengru Gao enhanced breastfeeding success during one week postpartum. The approach is acceptable to participants and merits further evaluation.
To the naïve observer, this study might look rigorous, but it is a seriously flawed RCT. Here are just some of its most obvious limitations:
- All we get in the methods section is this explanation: Participants were randomly allocated to the blank control group or the intervention group: Zengru Gao, orally, 30 g a time and 3 times a day. This seems to indicate that the control group got no treatment at all which means there was no blinding nor placebo control. The authors even comment on this point in the discussion section of their paper stating that because we included new mothers who received no treatment as a control group, we were able to prove that the improvement in breastfeeding was not due to the placebo effect. However, this is a totally nonsensical argument.
- The experimental treatment is not reproducible. The authors state: Zengru Gao, a Chinese herbal formula, which is composed of 8 herbs: Semen Vaccariae, Medulla Tetrapanacis, Radix Rehmanniae Praeparata, Radix Angelicae Sinensis, Radix Paeoniae Alba,Rhizoma Chuanxiong, Herba Leonuri, Radix Trichosanthis. This is not enough information to replicate the study outside China where the mixture is not commercially available.
- The primary outcome was the percentage of fully, and partially breastfeeding mothers. Breastfeeding was defined as mother’s milk given by direct breast feeding. Full breastfeeding meant that no other types of milk or solids were given. Partially breastfeeding meant that sustained latch with deep rhythmic sucking through the length of the feed, with some pause, on either/ or both breasts. We are not being told how the endpoint was quantified. Presumably women kept diaries. We cannot guess how accurate this process was.
- As far as I can see, there was no correction for multiple testing for statistical significance. This means that some or all of the significant results might be false-positive.
- There is insufficient data to show that the herbal mixture is safe for the mothers and the babies. At the very minimum, the researchers should have measured essential safety parameters. This omission is a gross violation of research ethics.
- Towards the end of the paper, we find the following statement: The authors would like to thank the Research and Development Department of Zhangzhou Pien Tze Huang Pharmaceutical co., Ltd. … The authors declare that they have no competing interests. And the 1st and 3rd authors are “affiliated with” Guangzhou Hipower Pharmaceutical Technology Co., Ltd, Guangzhou, China, i. e. work for the manufacturer of the mixture. This does clearly not make any sense whatsoever.
I have seen too many flawed studies of alternative medicine to be shocked or even surprised by this level of incompetence and nonsense. Yet, I still find it lamentable. But, in my view, the worst is that supposedly peer-reviewed journals such as ‘BMC Complement Altern Med’ publish such overt rubbish.
It would be easy to shrug one’s shoulder and bin the paper. But the effect of such fatally flawed research is too serious for that. In our recent book MORE HARM THAN GOOD? THE MORAL MAZE OF COMPLEMENTARY AND ALTERNATIVE MEDICINE, we discuss that such flawed science amounts to a violation of medical ethics: CAM journals allocate peer review tasks to a narrow range of CAM enthusiasts who often have been chosen by the authors of the article in question. The raison d’être of CAM journals and CAM researchers is inextricably tied to a belief in CAM, resulting in a self-referential situation which is permissive to the acceptance of weak or flawed reports of clinical effectiveness… Defective research—whether at the design, execution, analysis, or reporting stage—corrupts the repository of reliable medical knowledge. Ultimately, this leads to suboptimal and erroneous treatment decisions…
The authors of this systematic review aimed to summarize the evidence of clinical trials on cupping for athletes. Randomized controlled trials on cupping therapy with no restriction regarding the technique, or co-interventions, were included, if they measured the effects of cupping compared with any other intervention on health and performance outcomes in professionals, semi-professionals, and leisure athletes. Data extraction and risk of bias assessment using the Cochrane Risk of Bias Tool were conducted independently by two pairs of reviewers.
Eleven trials with n = 498 participants from China, the United States, Greece, Iran, and the United Arab Emirates were included, reporting effects on different populations, including soccer, football, and handball players, swimmers, gymnasts, and track and field athletes of both amateur and professional nature. Cupping was applied between 1 and 20 times, in daily or weekly intervals, alone or in combination with, for example, acupuncture. Outcomes varied greatly from symptom intensity, recovery measures, functional measures, serum markers, and experimental outcomes. Cupping was reported as beneficial for perceptions of pain and disability, increased range of motion, and reductions in creatine kinase when compared to mostly untreated control groups. The majority of trials had an unclear or high risk of bias. None of the studies reported safety.
Risk of bias of included trials. “+” indicates low risk of bias, “−” indicates high risk of bias, and “?” indicates unclear risk of bias.
The authors concluded that no explicit recommendation for or against the use of cupping for athletes can be made. More studies are necessary for conclusive judgment on the efficacy and safety of cupping in athletes.
Considering the authors’ stated aim, this conclusion seems odd. Surely, they should have concluded that THERE IS NO CONVINCING EVIDENCE FOR THE USE OF CUPPING IN ATHLETES. But this sounds rather negative, and the JCAM does not seem to tolerate negative conclusions, as discussed repeatedly on this blog.
The discussion section of this paper is bar of any noticeable critical input (for those who don’t know: the aim of any systematic review must be to CRITICALLY EVALUATE THE PRIMARY DATA). The authors even go as far as stating that the trials reported in this systematic review found beneficial effects of cupping in athletes when compared to no intervention. I find this surprising and bordering on scientific misconduct. The RCTs were mostly not on cupping but on cupping in combination with some other treatments. More importantly, they were of such deplorable quality that they allow no conclusions about effectiveness. Lastly, they mostly failed to report on adverse effects which, as I have often stated, is a violation of research ethics.
In essence, all this paper proves is that, if you have rubbish trials, you can produce a rubbish review and publish it in a rubbish journal.
