MD, PhD, FMedSci, FRSB, FRCP, FRCPEd.

methodology

I would warn every parent who thinks that taking their child to a chiropractor is a good idea. For this, I have three main reasons:

  1. Chiropractic has not been shown to be effective for any paediatric condition.
  2. Chiropractors often advise parents against vaccinating their children.
  3. Chiropractic spinal manipulations can cause harm to kids.

The latter point seems to be confirmed by a recent PhD thesis of which so far only one short report is available. Here are the relevant bits of information from it:

Katie Pohlman has successfully defended her PhD thesis, which focused on the assessment of safety in pediatric manual therapy. As a clinical research scientist at Parker University, Dallas, Texas, she identified a lack of prospective patient safety research within the chiropractic population in general and investigated this deficit in the paediatric population in particular.

Pohlman used a cross-sectional survey to assess the barriers and facilitators for participation in a patient safety reporting system. At the same time, she also conducted a randomized controlled trial comparing the quantity and quality of adverse event reports in children under 14 years receiving chiropractic care.

The RCT recruited 69 chiropractors and found adverse events reported in 8.8% and 0.1% of active and passive surveillance groups respectively. Of the adverse events reported, 56% were considered mild, 26% were moderate and 18% were severe. The frequency of adverse events was more common than previously thought.

This last sentence from the report is somewhat puzzling. Our systematic review of the risks of spinal manipulation showed that data from prospective studies suggest that minor, transient adverse events occur in approximately half of all patients receiving spinal manipulation. The most common serious adverse events are vertebrobasilar accidents, disk herniation, and cauda equina syndrome. Estimates of the incidence of serious complications range from 1 per 2 million manipulations to 1 per 400,000. Given the popularity of spinal manipulation, its safety requires rigorous investigation.

The 8.8% reported by Pohlman are therefore not even one fifth of the average incidence figure reported previously in all age groups.

What could be the explanation for this discrepancy?

There are, of course, several possibilities, including the fact that infants cannot tell the clinician when their pain has increased. However, the most likely one, in my view, lies in the fact that RCTs are wholly inadequate for investigating risks because they typically include far too few patients to generate reliable incidence figures about adverse events. More importantly, clinicians included in such studies are self-selected (and thus particularly responsible/cautious) and are bound to behave most carefully while being part of a clinical trial. Therefore it seems possible – I would speculate even likely – that the 8.8% reported by Pohlman is unrealistically low.

Having said that, I do feel that the research by Kathie Pohlman is a step in the right direction and I do applaud her initiative.

Lumbar spinal stenosis (LSS) is a common reason for spine surgery. Several non-surgical LSS treatment options are also available, but their effectiveness remains unproven. The objective of this study was to explore the comparative clinical effectiveness of three non-surgical interventions for patients with LSS:

  • medical care,
  • group exercise,
  • individualised exercise plus manual therapy.

All interventions were delivered during 6 weeks with follow-up at 2 months and 6 months at an outpatient research clinic. Patients older than 60 years with LSS were recruited from the general public. Eligibility required anatomical evidence of central canal and/or lateral recess stenosis (magnetic resonance imaging/computed tomography) and clinical symptoms associated with LSS (neurogenic claudication; less symptoms with flexion). Analysis was intention to treat.

Medical care consisted of medications and/or epidural injections provided by a physiatrist. Group exercise classes were supervised by fitness instructors. Manual therapy/individualized exercise consisted of spinal mobilization, stretches, and strength training provided by chiropractors and physical therapists. The primary outcomes were between-group differences at 2 months in self-reported symptoms and physical function measured by the Swiss Spinal Stenosis questionnaire (score range, 12-55) and a measure of walking capacity using the self-paced walking test (meters walked for 0 to 30 minutes).

A total of 259 participants were allocated to medical care (n = 88), group exercise (n = 84), or manual therapy/individualized exercise (n = 87). Adjusted between-group analyses at 2 months showed manual therapy/individualized exercise had greater improvement of symptoms and physical function compared with medical care or group exercise. Manual therapy/individualized exercise had a greater proportion of responders (≥30% improvement) in symptoms and physical function (20%) and walking capacity (65.3%) at 2 months compared with medical care (7.6% and 48.7%, respectively) or group exercise (3.0% and 46.2%, respectively). At 6 months, there were no between-group differences in mean outcome scores or responder rates.

The authors concluded that a combination of manual therapy/individualized exercise provides greater short-term improvement in symptoms and physical function and walking capacity than medical care or group exercises, although all 3 interventions were associated with improvements in long-term walking capacity.

In many ways, this is a fairly rigorous study; in one important way, however, it is odd. One can easily see why one group received the usual standard care (except perhaps for the fact that standard medical care should also include exercise). I also understand why one group attended group exercise. Yet, I fail to see the logic in the third intervention, individualised exercise plus manual therapy.

Individualised exercise is likely to be superior to group exercise. If the researchers wanted to test this hypothesis, they should not have added the manual therapy. If they wanted to find out whether manual therapy is better that the other two treatments, they should not have added individualised exercise. As it stands, they cannot claim that either manual therapy or individualised exercise are effective (yet, I am sure that the chiropractic fraternity will claim that this study shows their treatment to be indicated for LSS [three of the authors are chiropractors and the 1st author seems to have a commercial interest in the matter!]).

Manual therapy procedures used in this trial included:

  • lumbar distraction mobilization,
  • hip joint mobilization,
  • side posture lumbar/sacroiliac joint mobilization,
  • and neural mobilization.

Is there any good reason to assume that these interventions work for LSS? I doubt it!

And this is what makes the new study odd, in my view. Assuming I am correct in speculating that individualised exercise is better than group exercise, the trial would have yielded a similarly positive result, if the researchers had offered, instead of the manual therapy, a packet of cigarettes, a cup of tea, a chocolate bar, or swinging a dead cat. In other words, if someone had wanted to make a useless therapy appear to be effective, they could not have chosen a better trial design.

And why do I find such studies objectionable?

Mainly because they deliberately mislead many of us. In the present case, many non-critical observers might conclude that manual therapy is effective for LSS. Yet, the truth could well be that it is useless or even harmful (assuming that the effect size of individualised exercise is large, adding a harmful therapy would still render the combination effective). To put it bluntly, such trials

  • could harm patients,
  • might waste money,
  • and hinder progress.

 

Benign prostate hypertrophy (BPH) affects many men aged 50 and older. It is caused by an enlargement of the prostate resulting in difficulties to urinate and to fully empty the bladder. There are several conventional treatment options, including life-style changes that are effective. In addition, a myriad of alternative therapies are being promoted, most of which are of doubtful effectiveness. Recently, a homeopathy-promoter, Dr Jens Behnke, triumphantly tweeted a trial of homeopathy for BPH allegedly proving that homeopathy does work after all. There is no conceivable reason why homeopathic remedies should have any effect on this (or any other) condition. Therefore, I decided to have a closer look at this paper.

The objective of this 5-centre, three-armed, open, randomised study was to evaluate the effectiveness of Homoeopathic Constitutional remedy (HC) and Homoeopathic Constitutional + Organ remedy (HCOM) in comparison to Placebo (PL) in patients suffering from BPH using International Prostate Symptom Score (IPSS), ultrasonographic changes in prostate volume, post-void residual urine, uroflowmetry and in WHO Quality of Life (QOL)-BREF. Patients were randomised into three groups in 2:2:1 ratio and were followed up for 6 months. The statistical analysis was done with modified intention-to-treat principle (mITT).

Of 461 patients screened, 254 patients were enrolled in the study and 241 patients were analysed as per mITT. The mean changes in IPSS and QOL due to urinary symptoms from baseline to end of study showed a positive trend in all the three groups. However, in the HC group, the changes were more prominent as compared to the other two groups. There was no difference between HC and HCOM groups and they were equally effective in terms of managing lower urinary tract symptoms due to BPH. With regard to secondary outcome, there was no difference between the groups. The psychological, social and environmental domains of WHOQOL-BREF have shown positive trend, but there was no statistically significant difference in intervention groups.

The authors concluded that statistical significance was found in the IPSS in all the three groups but only in HC and not in any of the objective parameters.

The paper is so badly written that I struggle to make sense of it. However, the above graph seems clear enough. The changes are perhaps statistically significant (which I find odd and cannot quite understand) but they are certainly not clinically relevant. Most likely, they are due to the fact that this study was not blind, meaning that patients and investigators were aware of the group allocations. This suggests to me that this study

  • is dubious in more than one way,
  • tests a hypothesis that lacks plausibility,
  • yields a result that is clinically irrelevant.

In other words, it does not amount to anything remotely resembling a proof of homeopathy’s efficacy.

My last post was rather depressive, and I certainly do not want my readers to be under the weather when they go into 2019. For this last post of 2018, I have therefore selected 20 events which gave me hope that perhaps we – those who prefer rationality to nonsense – are making progress.

  1. It has been reported that New Brunswick judge ruled this week that Canadian naturopaths — pseudoscience purveyors who promote a variety of “alternative medicines” like homeopathy, herbs, detoxes, and acupuncture — cannot legally call themselves “medically trained.”
  2. The Spanish Ministries of Health and Sciences announced their ‘Health Protection Plan against Pseudotherapies’.
  3. The medical school of Vienna axed their courses in homeopathy.
  4. A most comprehensive review of homeopathy concluded that the effects of homeopathy do not differ from those of placebo.
  5. The UK Pharmaceutical Society has stated that it does not endorse homeopathy and that pharmacists must advise patients considering a homeopathic product about their lack of efficacy beyond that of a placebo.
  6. A top medical journal has retracted a dodgy meta-analysis of acupuncture.
  7. A prominent BMJ columnist wrote : Many people seek to make money from those who don’t understand science. Doctors should call out bollocksology when they see it.
  8. Pharmacare and Bioglan received a ‘Stonky’ for its over-the-counter Melatonin Homeopathic Sleep Formula.
  9. The Governing Body of Bristol, North Somerset and South Gloucestershire (BNSSG) Clinical Commissioning Group (CCG) approved changes that mean NHS funded homeopathy will only be available in exceptional circumstances in the area.
  10. Health ministers of all German counties have decided that they will start reforming the profession of the Heilpraktiker, the German non-medically trained alternative practitioners.
  11. The NHS chief, Simon Stevens was quoted saying: There is no robust evidence to support homeopathy which is at best a placebo and a misuse of scarce NHS funds.
  12. A systematic review concluded that there is no evidence in the literature of an effect of chiropractic treatment in the scope of primary prevention or early secondary prevention for disease in general. Chiropractors have to assume their role as evidence-based clinicians and the leaders of the profession must accept that it is harmful to the profession to imply a public health importance in relation to the prevention of such diseases through manipulative therapy/chiropractic treatment.
  13. A Cochrane review did not show any benefit of homeopathic medicinal products compared to placebo on recurrence of acute respiratory tract infections or cure rates in children. 
  14. The French minister of health stated that ‘the French are very attached [to homeopathy]; it’s probably a placebo effect. If it can prevent the use of toxic medicine, I think that we all win. I does not hurt.
  15. The Australian Acupuncture and Chinese Medicine Association retracted false accusation against me about their assumption that I had undeclared conflicts of interest.
  16. The ‘Daily Telegraph‘ published the following statement after misquoting me: Emeritus Professor Edzard Ernst, Britain’s first professor of complementary medicine at Exeter University said that doctors should make it clear to patients that they could not be taking herbal remedies alongside drugs. Prof Ernst said there was no good evidence that they work and that doctors were ‘contributing to disinformation’ by turning a blind eye to the practice.
  17. A comprehensive overview of the therapeutic options for chronic low back pain showed that chiropractic is not any better than over-the-counter painkillers or exercise, and that patients need to take precautions when seeking out a chiropractor.

Hold on, you promised 20, but these are just 17!!!, I hear my attentive readers mutter.

Correct! I tried to find 20 to match my last post; and I only found 17. This might be a reflection that, in the realm of SCAM, the bad still outweighs the good news (by much more that 20:17, I fear).

Yet, this should not depress us. On the contrary, let’s see it as a challenge to get on with out work of fighting for good evidence, ethical standards, rationality and critical thinking.In this spirit, I wish you all a very good, healthy and productive year 2019.

You probably know what yoga is. But what is FODMAP? It stands for fermentable oligosaccharides, disaccharides, monosaccharides and polyols, more commonly known as carbohydrates. In essence, FODMAPs are carbohydrates found in a wide range of foods including onions, garlic, mushrooms, apples, lentils, rye and milk. These sugars are poorly absorbed, pass through the small intestine and enter the colon . There they are fermented by bacteria a process that produces gas which stretches the sensitive bowel causing bloating, wind and sometimes even pain. This can also cause water to move into and out of the colon, causing diarrhoea, constipation or a combination of both. Irritable bowel syndrome (IBS) makes people more susceptible to such problems.

During a low FODMAP diet these carbohydrates are eliminated usually for six to eight weeks.  Subsequently, small amounts of FODMAP foods are gradually re-introduced to find a level of symptom-free tolerance. The question is, does the low FODMAP diet work?

This study examined the effect of a yoga-based intervention vs a low FODMAP diet on patients with irritable bowel syndrome. Fifty-nine patients with IBS undertook a randomised controlled trial involving yoga or a low FODMAP diet for 12 weeks. Patients in the yoga group received two sessions weekly, while patients in the low FODMAP group received a total of three sessions of nutritional counselling. The primary outcome was a change in gastrointestinal symptoms (IBS-SSS). Secondary outcomes explored changes in quality of life (IBS-QOL), health (SF-36), perceived stress (CPSS, PSQ), body awareness (BAQ), body responsiveness (BRS) and safety of the interventions. Outcomes were examined in weeks 12 and 24 by assessors “blinded” to patients’ group allocation.

No statistically significant difference was found between the intervention groups, with regard to IBS-SSS score, at either 12 or 24 weeks. Within-group comparisons showed statistically significant effects for yoga and low FODMAP diet at both 12 and 24 weeks. Comparable within-group effects occurred for the other outcomes. One patient in each intervention group experienced serious adverse events and another, also in each group, experienced nonserious adverse events.

The authors concluded that patients with irritable bowel syndrome might benefit from yoga and a low-FODMAP diet, as both groups showed a reduction in gastrointestinal symptoms. More research on the underlying mechanisms of both interventions is warranted, as well as exploration of potential benefits from their combined use.

Technically, this study is an equivalence study comparing two interventions. Such trials only make sense, if one of the two treatments have been proven to be effective. This is, however, not the case. Moreover, equivalence studies require much larger sample sizes than the 59 patients included here.

What follows is that this trial is pure pseudoscience and the positive conclusion of this study is not warranted. The authors have, in my view, demonstrated a remarkable level of ignorance regarding clinical research. None of this is all that unusual in the realm of alternative medicine; sadly, it seems more the rule than the exception.

What might make this lack of research know-how more noteworthy is something else: starting in January 2019, one of the lead authors of this piece of pseudo-research (Prof. Dr. med. Jost Langhorst) will be the director of the new Stiftungslehrstuhl “Integrative Medizin” am Klinikum Bamberg (clinic and chair of integrative medicine in Bamberg, Germany).

This does not bode well, does it?

According to the investigators, the primary objective this study (thanks again Dr Jens Behnke) was to evaluate the effectiveness of homoeopathic remedies in improving quality of life (QoL) of chronic urticaria (CU) patients.

The study population included patients attending the Outpatient Department of State Homoeopathic Dispensary, Ahmadpur, India. Quality of Life (QoL) questionnaire (CU-Q2oL) and average Urticaria Activity Score for 7 days (UAS7) questionnaires were filled at baseline and 3rd, 6th, 9th and 12th months. The study included both male and female patients diagnosed with CU. Eighteen homoeopathic remedies were used. The individualised prescriptions were based on the totality of each patient’s symptoms.

A total of 134 patients were screened and 70 were diagnosed with CU and enrolled in the study. The results were analysed under modified intention-to-treat approach. Significant difference was found in baseline and 12th month CU-Q2oL score. Apis mellifica (n = 10), Natrum muriaticum (n = 9), Rhus toxicodendron (n = 8) and Sulphur (n = 8) were the most frequently used remedies.

The authors concluded that homoeopathic medicines have potential to improve QoL of CU patients by reducing pruritus, intensity of wheals, swelling, nervousness, and improve sleep, mood and concentration. Further studies with more sample size are desirable.

The primary objective of this study was, I would argue, to promote the erroneous idea that homeopathy is an effective therapy. It cannot have been to evaluate its effectiveness, because for such an aim one would clearly have needed a control group. Without it, the findings are consistent with the following facts:

  1. Homeopathy is useless.
  2. CU responds to placebo treatments.
  3. CU gets better over time.
  4. Regression towards the mean has contributed to the outcome.
  5. Homeopaths often have no idea about clinical research.
  6. Further trials are not needed.
  7. If someone disagrees with my point 6, the sample size is less important than the inclusion of a control group.

It is time, I think, to express my gratitude to Dr Jens Behnke, a German homeopath employed by the pro-homeopathy lobby group the ‘Carstens Stiftung’, who diligently tweets trials of homeopathy which he obviously believes prove the value of his convictions.

The primary objective of this new study was to evaluate the efficacy of homoeopathy for women suffering from polycystic ovary syndrome. This condition is characterised by:

  • irregular periods which means your ovaries don’t regularly release eggs,
  • abnormally high levels of male hormones in the body, which may cause physical signs such as excess facial or body hair,
  • polycystic ovaries – ovaries become enlarged and contain many fluid-filled sacs (follicles) which surround the eggs.

There’s no cure for PCOS, but the symptoms can usually be treated. As so often in such situations, homeopaths are happy to step into the fray.

This single-blind, randomised, placebo-controlled pilot study was conducted at two research centres in India. The cases fulfilling the eligibility criteria were enrolled (n = 60) and randomised to either the homoeopathic intervention (HI) (n = 30) or placebo (P) (n = 30) with uniform lifestyle modification (LSM) for 6 months.

The menstrual regularity with improvement in other signs/symptoms was observed in 60% of the cases (n = 18) in HI + LSM group and none (n = 0) in control group. Statistically significant difference was observed in the reduction of intermenstrual duration in HI + LSM in comparison to placebo + LSM group. Significant improvements were also observed in HI+LSM group in domains of weight, fertility, emotions and menstrual problems. No change was observed in respect of improvement in the ultrasound findings. Pulsatilla was the most frequently indicated homeopathic remedy.

The authors concluded that HI along with LSM has shown promising outcome; further comparative study with standard conventional treatment on adequate sample size is desirable.

This trial might convince believers (mostly because they do not even need convincing), but it cannot convince anybody capable of critical thinking. Here is why:

  • According to its authors, this trial was a pilot study; this means it should not report any results and merely focus on the feasibility of a definitive trial.
  • Researchers were not blinded, meaning that they might have influenced the outcome in more than one way.
  • The primary endpoint was subjective and could have been influenced by the non-blinded researchers.
  • 0% success rate in achieving the primary endpoint in the placebo group is not plausible.
  • Compliance to LSM was not checked; as the homeopathy group lost more weight, these patients seemed to have complied better (probably due to being better motivated by the non-blinded researchers).

So?

My conclusion is not very original but all the more true: POORLY DESIGNED STUDIES USUALLY GENERATE UNRELIABLE RESULTS. 

For some researchers, the question whether homeopathy works beyond a placebo effect is not as relevant as the question whether it works as well as an established treatment. To answer it, they must conduct RCTs comparing homeopathy with a therapy that has been shown beyond reasonable doubt to be effective, i.e better than placebo. Such a drug is, for instance, Ibuprofen.

The purpose of this study was to compare the efficacy of Ibuprofen and homeopathic Belladonna for orthodontic pain. 51 females and 21 males, were included in this study. Cases with non-extraction treatment plan having proper contacts’ mesial and distal to permanent first molar and currently not taking any analgesics or antibiotics were included in the study. They were randomly divided into two groups; one group was assigned to ibuprofen 400 mg and second group took Belladonna 6C (that’s a dilution of 1: 1000000000000). Patients were given two doses of medication of their respective remedies one hour before placement of elastomeric separators (Ormco Separators, Ormco Corporation, CA, USA) and one dose 6 h after the placement. Pain scores were recorded on a visual analogue scale (VAS) 2 h after placement, 6 h after placement, bedtime, day 1 morning, day 2 morning, day 3 morning and day 5 morning.

The comparisons showed that there were no differences between the two groups at any time point.

(Mean visual analogue scale pain score at different time intervals after separator placement in Ibuprofen and Belladonna group)

The authors concluded that Ibuprofen and Belladonna 6C are effective and provide adequate analgesia with no statistically significant difference. Lack of adverse effects with Belladonna 6C makes it an effective and viable alternative.

FINALLY, THE PROOF HOMEOPATHS HAVE BEEN WAITING FOR: HOMEOPATHY DOES WORK AFTER ALL!

Not so fast – before we draw any conclusions, let’s have a closer look at this study. Here are a few of its limitations (apart from the fact that it was published in a journal that does not exactly belong to the ‘crème de la crème’ of medical publications):

  • Patients obviously knew which group they were assigned to; thus their expectations would have influenced the outcome.
  • The same applies to the researchers (the study could have been ‘blind’ using a ‘double dummy’ method, but the researchers did not use it).
  • The study was an equivalence trial (it did not test whether homeopathy is superior to placebo, but whether its effects are equivalent to Ibuprofen); such studies need sample sizes that are about one dimension larger than was the case here.

Therefore, all this trial does demonstrate that the sample was too small for an existing group difference in favour of Ibuprofen to show.

So sorry, my homeopathic friends!

Personally, I like sauna bathing. It makes me feel fine. But is it healthy? More specifically, is it good for the cardiovascular system?

Finnish researchers had already shown in a large cohort study with 20 years of follow-up that increased frequency of sauna bathing is associated with a reduced risk of sudden cardiac death (SCD), fatal coronary heart disease (CHD), fatal cardiovascular disease (CVD), and all-cause mortality. Now the same group of researchers report more encouraging news for sauna-fans.

The aim of their new study was to investigate the relationship between sauna habits and CVD mortality in men and women, and whether adding information on sauna habits to conventional cardiovascular risk factors is associated with improvement in prediction of CVD mortality risk.

Sauna bathing habits were assessed at baseline in a sample of 1688 participants (mean age 63; range 53-74 years), of whom 51.4% were women. Multivariable-adjusted hazard ratios (HRs) were calculated to investigate the relationships of frequency and duration of sauna use with CVD mortality.

A total of 181 fatal CVD events occurred during a median follow-up of 15.0 years (interquartile range, 14.1-15.9). The risk of CVD mortality decreased linearly with increasing sauna sessions per week with no threshold effect. In age- and sex-adjusted analysis, compared with participants who had one sauna bathing session per week, HRs (95% CIs) for CVD mortality were 0.71 (0.52 to 0.98) and 0.30 (0.14 to 0.64) for participants with two to three and four to seven sauna sessions per week, respectively. After adjustment for established CVD risk factors, potential confounders including physical activity, socioeconomic status, and incident coronary heart disease, the corresponding HRs (95% CIs) were 0.75 (0.52 to 1.08) and 0.23 (0.08 to 0.65), respectively. The duration of sauna use (minutes per week) was inversely associated with CVD mortality in a continuous manner. Addition of information on sauna bathing frequency to a CVD mortality risk prediction model containing established risk factors was associated with a C-index change (0.0091; P = 0.010), difference in - 2 log likelihood (P = 0.019), and categorical net reclassification improvement (4.14%; P = 0.004).

(Hazard ratios for cardiovascular mortality by quartiles of the duration of sauna bathing. a Adjusted for age and gender. b Adjusted for age, gender, body mass index, smoking, systolic blood pressure, serum low-density lipoprotein cholesterol, alcohol consumption, previous myocardial infarction, and type 2 diabetes. CI, confidence interval.)

The authors concluded that higher frequency and duration of sauna bathing are each strongly, inversely, and independently associated with fatal CVD events in middle-aged to elderly males and females. The frequency of sauna bathing improves the prediction of the long-term risk for CVD mortality.

These results are impressive. What could be the underlying mechanisms? The authors offer plenty of explanations: Dry and hot sauna baths have been shown to increase the demands of cardiovascular function. Sauna bathing causes an increase in heart rate which is a reaction to the body heat load. Heart rate may be elevated up to 120–150 beats per minute during sauna bathing, corresponding to low- to moderate-intensity physical exercise training for the circulatory system without active muscle work. Acute sauna exposure has been shown to produce blood pressure lowering effects, decrease peripheral vascular resistance and arterial stiffness, and improve arterial compliance. Short-term sauna exposure also activates the sympathetic nervous and the renin-angiotensin-aldosterone systems and the hypothalamus-pituitary-adrenal hormonal axis, and short-term increases in levels of their associated hormones have been reported. Repeated sauna exposure improves endothelial function, suggesting a beneficial role of thermal therapy on vascular function. Long-term sauna bathing habit may be beneficial in the reduction of high systemic blood pressure, which is in line with previous evidence showing that blood pressure may be lower among those who are living in warm conditions with higher ambient temperature. Regular sauna bathing is associated with a lowered risk of future hypertension. Typical hot and dry Finnish sauna increases body temperature which causes more efficient skin blood flow, leading to a higher cardiac output, whereas blood flow to internal organs decreases. Sweat is typically secreted at a rate which corresponds to an average total secretion of 0.5 kg during a sauna bathing session. Increased sweating is accompanied by a reduction in blood pressure and higher heart rate, while cardiac stroke volume is largely maintained, although a part of blood volume is diverted from the internal organs to body peripheral parts with decreasing venous return which is not facilitated by active skeletal muscle work. However, it has been proposed that muscle blood flow may increase to at least some extent in response to heat stress, although sauna therapy-induced myocardial metabolic adaptations are largely unexplored. There is also evidence that regular long-term sauna bathing (average of two sessions per week) increases left ventricular ejection fraction. Heat therapy may improve left ventricular function with decreased cardiac pre- and afterload, thereby maintaining appropriate stroke volume despite large reductions in ventricular filling pressures. Additionally, previous studies have demonstrated a positive alteration of the autonomic nervous system and reduced levels of natriuretic peptides, oxidative stress, inflammation, and norepinephrine due to regular sauna therapy.

It is possible that the results are influenced by confounding factors that the researchers were unable to account for. It is also possible that people who are already ill avoid sauna bathing and that this contributed to the findings. However, the authors did their best to explore such phenomena in sub-group analysis and found that a causal relationship between sauna and CVD risk is still very likely. As a sauna-fan, I am inclined to believe them and the sceptic in me tends to agree.

Shiatsu has been mentioned here before (see for instance here, here and here). It is one of those alternative therapies for which a plethora of therapeutic claims are being made in the almost total absence of reliable evidence. This is why I am delighted each time a new study emerges.

This proof of concept study explored the feasibility of ‘hand self-shiatsu’ as an intervention to promote sleep onset and continuity for young adults with SRC. It employed a prospective case-series design, where participants, athletes who have suffered from concussion, act as their own controls. Baseline and follow-up data included standardized self-reported assessment tools and sleep actigraphy. Seven athletes, aged between 18 and 25 years, participated. Although statistically significant improvement in actigraphy sleep scores between baseline and follow-up was not achieved, metrics for sleep quality and daytime fatigue showed significant improvement.

The authors concluded from these data that these findings support the hypothesis that ‘hand self-shiatsu has the potential to improve sleep and reduce daytime fatigue in young postconcussion athletes. This pilot study provides guidance to refine research protocols and lays a foundation for further, large-sample, controlled studies.

How very disappointing! If this was truly meant to be a pilot study, it should not mention findings of clinical improvement at all. I suspect that the authors labelled it ‘a pilot study’ only when they realised that it was wholly inadequate. I also suspect that the study did not yield the result they had hoped for (a significant improvement in actigraphy sleep scores), and thus they included the metrics for sleep quality and daytime fatigue in the abstract.

In any case, even a pilot study of just 7 patients is hardly worth writing home about. And the remark that participants acted as their own controls is a new level of obfuscation: there were no controls, and the results are based on before/after comparisons. Thus none of the outcomes can be attributed to shiatsu; more likely, they are due to the natural history of the condition, placebo effects, concomitant treatments, social desirability etc.

What sort of journal publishes such drivel that can only have the effect of giving a bad name to clinical research? The Journal of Integrative Medicine (JIM) is a peer-reviewed journal sponsored by Shanghai Association of Integrative Medicine and Shanghai Changhai Hospital, China. It is a continuation of the Journal of Chinese Integrative Medicine (JCIM), which was established in 2003 and published in Chinese language. Since 2013, JIM has been published in English language. They state that the editorial board is committed to publishing high-quality papers on integrative medicine... I consider this as a bad joke! More likely, this journal is little more than an organ for popularising TCM propaganda in the West.

And which publisher hosts such a journal?

Elsevier

What a disgrace!

 

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