One of the best-selling supplements in the UK as well as several other countries is evening primrose oil (EPO). It is available via all sorts of outlets (even respectable pharmacies – or is that supposedly respectable?), and is being promoted for a wide range of conditions, including eczema. The NIH website is optimistic about its efficacy: “Evening primrose oil may have modest benefits for eczema.” Our brand-new Cochrane review was aimed at critically assessing the effects of oral EPO or borage oil (BO) on the symptoms of atopic eczema, and it casts considerable doubt on this somewhat uncritical view.
Here is what we did: We searched six databases as well as online trials registers and checked the bibliographies of included studies for further references to relevant trials. We corresponded with trial investigators and pharmaceutical companies to identify unpublished and ongoing trials. We also performed a separate search for adverse effects. All RCTs investigating oral intake of EPO or BO for eczema were included.
Two experts independently applied eligibility criteria, assessed risk of bias, and extracted data. We pooled dichotomous outcomes using risk ratios (RR), and continuous outcomes using the mean difference (MD). Where possible, we pooled study results using random-effects meta-analysis and tested statistical heterogeneity.
And here is what we found: 27 studies with a total of 1596 participants met our inclusion criteria: 19 studies tested EPO, and 8 studies assessed BO. A meta-analysis of results from 7 studies showed that EPO failed to improve global eczema symptoms as reported by participants and doctors. Treatment with BO also failed to improve global eczema symptoms. 67% of the studies had a low risk of bias for random sequence generation; 44%, for allocation concealment; 59%, for blinding; and 37%, for other biases.
Our conclusions were clear: Oral borage oil and evening primrose oil lack effect on eczema; improvement was similar to respective placebos used in trials. Oral BO and EPO are not effective treatments for eczema.
The very wide-spread notion that EPO is effective for eczema and a range of other conditions was originally promoted by the researcher turned entrepreneur, D F Horrobin, who claimed that several human diseases, including eczema, were due to a lack of fatty acid precursors and could thus be effectively treated with EPO. In the 1980s, Horrobin began to sell EPO supplements without having conclusively demonstrated their safety and efficacy; this led to confiscations and felony indictments in the US. As chief executive of Scotia Pharmaceuticals, Horrobin obtained licences for several EPO-preparations which later were withdrawn for lack of efficacy. Charges of mismanagement and fraud led to Horrobin being ousted as CEO by the board of the company. Later, Horrobin published a positive meta-analysis of EPO for eczema where he excluded the negative results of the largest published trial, but included results of 7 of his own unpublished studies. When scientists asked to examine the data, Horrobin’s legal team convinced the journal to refuse the request.
The evidence for EPO is negative not just for eczema. To the best of my knowledge, there is not a single disease or symptom for which it demonstrably works. Our own review of the data concluded ” EPO has not been established as an effective treatment for any condition”
Our new Cochrane review might help to put this long saga to rest. In my view, it is a fascinating tale of a scientist being blinded by creed and ambition. The results of such errors can be dramatic. Horrobin misled all of us: patients, health care professionals, scientists, regulators, decision makers, businessmen. This caused unnecessary expense and set back research efforts in a multitude of areas. I find the tale also fascinating from other perspectives; for instance, it begs the question why so many ‘respectable’ manufacturers and retailers are still allowed to make money on EPO. Is it not time to debunk the EPO-myth and say it as clearly as possible: EPO helps only those who financially profit from misleading the public?
In the UK, we have about 150000 practitioners of Spiritual Healing (SH). They treat all sorts of conditions claiming to channel ‘healing energy’ into the patient’s body which enables him/her to heal itself. The plausibility of SH is very close to zero and, despite numerous trials, its clinical effectiveness remains unproven. A new and, in my view, remarkable study of SH was aimed at investigating whether “SH could support patients with breast cancer”.
Spiritual Healing was provided by 4 healers registered with the National Federation of Spiritual Healers. Twelve patients with breast cancer undergoing long-term hormone treatment and experiencing its adverse-effects as onerous, self-referred themselves and were given ten weekly sessions of approximately 40 minutes each. Data collected included participant’s daily records, direct observations noted by the healers, the researcher’s field diary and a one-to-one semi-structured interview.
The alleged positive effects of SH included alleviation of the physical adverse-effects of their treatment, increased energy levels, enhanced well-being, emotional relaxation, and re-engagement with pre-cancer activities. Although one participant admitted considering a drug holiday prior to joining the study, none of the participants felt tempted to stop their hormonal treatments while receiving SH. The authors concluded that “these qualitative findings indicate that SH has the potential to support patients with breast cancer in the maintenance of their long-term orthodox treatments. Further research is needed to test SH as a cost-effective complementary therapy, for those undergoing long-term cancer treatments.”
As I already mentioned, I think this study is remarkable. Having done quite a bit of research into SH myself, I know how bizarre this intervention truly is. A typical treatment session might be with the patient lying on a couch in a relaxing atmosphere, often accompanied by soothing background music; the healer would talk gently but very little to enable the patient to be comfortable and relax; the SH itself might be performed by the healer moving his/her hands at a distance over the body of the patient; the healer would explain that this may cause the sensation of warmth as the ‘healing energy’ enters the body. Altogether, the experience is exotic to say the least.
It is therefore not surprising that SH generates a host of non-specific effects, including the most enormous placebo-response I have ever witnessed in any clinical trial which I have been involved in. I am mentioning this, of course, to point out that the above-noted effects are entirely compatible with those of placebo. As the study has no control group, there is no way of knowing what the effects of SH per se might have been. The fact that patients self-referred themselves to SH would only amplify this placebo-response. In the discussion of the paper, we find a further interesting pointer regarding patients’ prior experience with conventional health care professionals: “participants felt they were left to cope alone as their side-effects were trivialized.” This seems to suggest that the group of patients were indeed highly selected and all had suffered badly from previous experiences of poorly administered heath care. Thus their expectations of SH were probably high which, in turn, would exaggerate the placebo-response even further.
All of these phenomena might well be fascinating and could provide ample material for relevant research. They deserve to be analysed carefully and discussed openly and critically. Unfortunately none of this happened in the present study. The authors do not even consider the possibility that the observed effects could be related to anything else than their SH. Their stated aim to investigate whether SH supports cancer patients is not even approached; the authors simply assume a cause-effect relationship without demonstrating one. I find this is more than just a missed opportunity; in my view, it is pseudo-science. And this is the reason why I find this study remarkable.
If we believe homeopaths, we might get the impression that homeopathy is firmly established in mainstream health care. “They would say that, wouldn’t they?” To convince skeptics, we might want to have a bit more than wishful thinking.
We have just published a systematic review in order to instill some evidence into this debate. Our aim was to evaluate all the data from recent surveys of GPs and assess their involvement with and attitudes towards homeopathy. We searched 7 electronic databases to identify all relevant articles. Data extraction was conducted by three independent reviewers. Thirteen surveys met the inclusion criteria. Their findings suggest that less than 10% of GPs treated patients with homeopathy; referral rates varied hugely and ranged from 4.6% to 73%.
Two surveys also assessed GPs’ endorsement of homeopathy; they suggested that less than 15% of GPs were endorsing homeopathy. One survey asked about GPs’ personal usage of homeopathy and reported less than 10% had used this form of therapy on themselves.
Three surveys investigated adverse events (AEs) from homeopathic treatments. One was solely focussed on AEs which were classified as “serious” (either life threatening or likely to cause disability or sever morbidity) or non-serious. In total, 21 “indirect” serious AEs were reported (e.g., stopping medication, refusing immunisation, refusing cancer treatment, delaying diagnosis). Another survey found that 14% of GPs reported AEs following homeopathic treatment within a year. Other authors reported that the discontinuation of conventional asthma treatment in favour of a homeopathic remedy had led to cardiovascular arrest.
These data shed a much more sober light on the use of homeopathy in the UK. They fail to show that homeopathy is well-accepted by British GPs. More importantly perhaps they disclose serious problems with the use of homeopathy.
Whenever we consider alternative medicine, we think of therapeutic interventions and tend to forget that alternative practitioners frequently employ diagnostic methods which are alien to mainstream health care. Acupuncturists, iridologists, spiritual healers, massage therapists, reflexologists, applied kinesiologists, homeopaths, chiropractors, osteopaths and many other types of alternative practitioners all have their very own ways of diagnosing what might be wrong with their patients.
The purpose of a diagnostic test or technique is, of course, to establish the presence or absence of an abnormality, condition or disease. Conventional doctors use all sorts of validated diagnostic methods, from physical examination to laboratory tests, from blood pressure measurements to X-rays. Alternative practitioners use mostly alternative methods for arriving at a diagnosis, and we should ask: how reliable are these techniques?
Anyone trying to answer this question, will be surprised to find how very little reliable information on this topic exists. Scientific tests of the validity of alternative diagnostic tests are a bit like gold dust. And this is why a recently published article is, in my view, of particular importance and value.
The aim of this study was to evaluate the inter-rater reliability of pulse-diagnosis as performed by Traditional Korean Medicine (TKM) clinicians. A total 658 patients with stroke who were admitted into Korean oriental medical university hospitals were included. Each patient was seen by two TKM-experts for an examination of the pulse signs – pulse diagnosis is regularly used by practitioners of TKM and Traditional Chinese Medicine (TCM), and is entirely different from what conventional doctors do when they feel the pulse of a patient. Inter-observer reliability was assessed using three methods: simple percentage agreement, the kappa value, and the AC(1) statistic. The kappa value indicated that the inter-observer reliability in evaluating the pulse signs ranged from poor to moderate, whereas the AC(1) analysis suggested that agreement between the two experts was generally high (with the exception of ‘slippery pulse’). The kappa value indicated that the inter-observer reliability was generally moderate to good (with the exceptions of ‘rough pulse’ and ‘sunken pulse’) and that the AC(1) measure of agreement between the two experts was generally high.
Based on these findings, the authors drew the following conclusion: “Pulse diagnosis is regarded as one of the most important procedures in TKM… This study reveals that the inter-observer reliability in making a pulse diagnosis in stroke patients is not particularly high when objectively quantified. Additional research is needed to help reduce this lack of reliability for various portions of the pulse diagnosis.”
This indicates, I think, that the researchers (who are themselves practitioners of TCM!) are not impressed with the inter-rater reliability of the most commonly used diagnostic tool in TCM/TKM. Imagine this to be true for a commonly used test in conventional medicine; imagine, for instance, that one doctor measuring your blood pressure produces entirely different readings than the next one. Hardly acceptable, don’t you think?
And, of course, inter-rater reliability would be only one of several preconditions for their diagnostic methods to be valid. Other essential preconditions for diagnostic tests to be of value are their specificity and their sensitivity; do they discriminate between healthy and unhealthy, and are they capable of differentiating between severely abnormal findings and those that are just a little out of the normal range?
Until we have answers to all the open questions about each specific alternative diagnostic method, it would be unwise to pretend these tests are valid. Imagine a doctor prescribing a life-long anti-hypertensive therapy on the basis of a blood pressure reading that is little more than guess-work!
Since non-validated diagnostic tests can generate both false positive and false negative results, the danger of using them should not be under-estimated. In a way, invalid diagnostic tests are akin to bogus bomb-detectors (which made headlines recently): both are techniques to identify a problem. If the method generates a false positive result, an alert will be issued in vain, people will get anxious for nothing, time and money will be lost, etc. If the method generates a false negative result, we will assume to be safe while, in fact, we are not. In extreme cases, such an error will cost lives.
It is difficult to call those ‘experts’ who advocate using such tests anything else than irresponsible, I’d say. And it is even more difficult to have any confidence in the treatments that might be administered on the basis of such diagnostic methods, wouldn’t you agree?
I think I must have mentioned this once or twice before: I am constantly on the look-out for new evidence which shows or suggests that some form of alternative medicine works. Today, it seems, I have been lucky.
In this randomised, double-blind, placebo-controlled clinical trial, 200 patients suffering from chronic obstructive pulmonary disease (COPD) were randomly allocated to receive oral therapy with 3 × 30 drops/day of an extract of Pelargonium sidoides (EPs 7630) or placebo. Both treatments were administered in addition to standardised COPD- therapies, and the treatment period lasted 24 weeks. The primary endpoint of this study was the time to the next exacerbation of COPD. Secondary endpoints were the number of such exacerbations, consumption of antibiotics, quality of life, patient satisfaction, inability to work, and the tolerability of the treatment.
The results show that the median time to exacerbation was significantly prolonged with the herbal treatment compared to placebo (57 versus 43 days). The superiority of EPs 7630 over placebo was also confirmed in secondary endpoints, e.g., fewer exacerbations, less patients with antibiotic use, improved quality of life, higher patient satisfaction, and less days of inability to work. The incidence of minor gastrointestinal adverse events was higher in the EPs 7630 group.
The authors of the study conclude that “the results demonstrate a statistically significant and clinically relevant superiority of add-on therapy with EPs 7630 over placebo and a good long-term tolerability in the treatment of moderate to severe COPD. EPs 7630 prolonged time to exacerbations and reduced exacerbation frequency and antibiotic use.”
Chronic obstructive pulmonary disease, is a progressive and serious condition linked to smoking which makes breathing increasingly difficult. The symptoms of COPD typically include a productive cough, wheezing, shortness of breath and chest tightness. Long-term exposure to other lung irritants—such as air pollution, chemical fumes, or dust may contribute to COPD. The condition is a major cause of disability, and currently it is the third leading cause of death, which means that millions of people suffer from COPD.
There is no cure for COPD; the damage to the airways and lungs is not reversible. Various symptomatic treatments exist, for instance, antibiotics, bronchio-dilators, steroids and physiotherapy. Lifestyle changes can further improve the situation, help patients to stay more active, and slow the progress of the disease.
It is clear that COPD is a very serious condition, that the burden of suffering for individual patients can be immense, that therapeutic options are limited and often associated with adverse-effects. In this situation, any new effective and safe therapy would be more than welcome. Pelargonium has previously shown promise in the treatment of asthma, acute bronchitis as well as other respiratory infections. It seems generally safe but is not totally devoid of adverse-effects.
This new study gives hope to COPD-sufferers as it suggests that Pelargonium sidoides might alleviate their symptoms. The trial seems rigorous but the benefit is not huge and the treatment is not a cure of COPD. Moreover, I should point out that any new finding of this nature requires independent confirmations. I do think that the trial is an important step in the right direction, yet I feel that it is too early for issuing general recommendations.
This post has an odd title and addresses an odd subject. I am sure some people reading it will ask themselves “has he finally gone potty; is he a bit xenophobic, chauvinistic, or what?” I can assure you none of the above is the case.
Since many years, I have been asked to peer-review Chinese systematic reviews and meta-analyses of TCM-trials submitted to various journals and to the Cochrane Collaboration for publication, and I estimate that around 300 such articles are available today. Initially, I thought they were a valuable contribution to our knowledge, particularly for the many of us who cannot read Chinese languages. I hoped they might provide reliable information about this huge and potentially important section of the TCM-evidence. After doing this type of work for some time, I became more and more frustrated; now I have decided not to accept this task any longer – not because it is too much trouble, but because I have come to the conclusion that these articles are far less helpful than I had once assumed; in fact, I now fear that they are counter-productive.
In order to better understand what I mean, it might be best to use an example; this recent systematic review seems as good for that purpose as any.
Its Chinese authors “hypothesized that the eligible trials would provide evidence of the effect of Chinese herbs on bone mineral density (BMD) and the therapeutic benefits of Chinese medicine treatment in patients with bone loss“. Randomized controlled trials (RCTs) were thus retrieved for a systematic review from Medline and 8 Chinese databases. The authors identified 12 RCTs involving a total of 1816 patients. The studies compared Chinese herbs with placebo or standard anti-osteoporotic therapy. The pooled data from these RCTs showed that the change of BMD in the spine was more pronounced with Chinese herbs compared to the effects noted with placebo. Also, in the femoral neck, Chinese herbs generated significantly higher increments of BMD compared to placebo. Compared to conventional anti-osteoporotic drugs, Chinese herbs generated greater BMD changes.
In their abstract, the part on the paper that most readers access, the authors reached the following conclusions: “Our results demonstrated that Chinese herb significantly increased lumbar spine BMD as compared to the placebo or other standard anti-osteoporotic drugs.” In the article itself, we find this more detailed conclusion: “We conclude that Chinese herbs substantially increased BMD of the lumbar spine compared to placebo or anti-osteoporotic drugs as indicated in the current clinical reports on osteoporosis treatment. Long term of Chinese herbs over 12 months of treatment duration may increase BMD in the hip more effectively. However, further studies are needed to corroborate the positive effect of increasing the duration of Chinese herbs on outcome as the results in this analysis are based on indirect comparisons. To date there are no studies available that compare Chinese herbs, Chinese herbs plus anti-osteoporotic drugs, and anti-osteoporotic drug versus placebo in a factorial design. Consequently, we are unable to draw any conclusions on the possible superiority of Chinese herbs plus anti-osteoporotic drug versus anti-osteoporotic drug or Chinese herb alone in the context of BMD.“
Most readers will feel that this evidence is quite impressive and amazingly solid; they might therefore advocate routinely using Chinese herbs for the common and difficult to treat problem of osteoporosis. The integration of TCM might avoid lots of human suffering, prolong the life of many elderly patients, and save us all a lot of money. Why then am I not at all convinced?
The first thing to notice is the fact that we do not really know which of the ~7000 different Chinese herbs should be used. The article tells us surprisingly little about this crucial point. And even, if we manage to study this question in more depth, we are bound to get thoroughly confused; there are simply too many herbal mixtures and patent medicines to easily identify the most promising candidates.
The second and more important hurdle to making sense of these data is the fact that most of the primary studies originate from inaccessible Chinese journals and were published in Chinese languages which, of course, few people in the West can understand. This is entirely our fault, some might argue, but it does mean that we have to believe the authors, take their words at face value, and cannot check the original data. You may think this is fine, after all, the paper has gone through a rigorous peer-review process where it has been thoroughly checked by several top experts in the field. This, however, is a fallacy; like you and me, the peer-reviewers might not read Chinese either! (I don’t, and I reviewed quite a few of these papers; in some instances, I even asked for translations of the originals to do the job properly but this request was understandably turned down) In all likelihood, the above paper and most similar articles have not been properly peer-reviewed at all.
The third and perhaps most crucial point can only be fully appreciated, if we were able to access and understand the primary studies; it relates to the quality of the original RCTs summarised in such systematic reviews. The abstract of the present paper tells us nothing at all about this issue. In the paper, however, we do find a formal assessment of the studies’ risk of bias which shows that the quality of the included RCTs was poor to very poor. We also find a short but revealing sentence: “The reports of all trials mentioned randomization, but only seven described the method of randomization.” This remark is much more significant than it may seem: we have shown that such studies use such terminology in a rather adventurous way; reviewing about 2000 of these allegedly randomised trials, we found that many Chinese authors call a trial “randomised” even in the absence of a control group (one cannot randomise patients and have no control group)! They seem to like the term because it is fashionable and makes publication of their work easier. We thus have good reason to fear that some/many/most of the studies were not RCTs at all.
The fourth issue that needs mentioning is the fact that very close to 100% of all Chinese TCM-trials report positive findings. This means that either TCM is effective for every indication it is tested for (most unlikely, not least because there are many negative non-Chinese trials of TCM), or there is something very fundamentally wrong with Chinese research into TCM. Over the years, I have had several Chinese co-workers in my team and was invariably impressed by their ability to work hard and efficiently; we often discussed the possible reasons for the extraordinary phenomenon of 0% negative Chinese trials. The most plausible answer they offered was this: it would be most impolite for a Chinese researcher to produce findings which contradict the opinion of his/her peers.
In view of these concerns, can we trust the conclusions of such systematic reviews? I don’t think so – and this is why I have problems with research of this nature. If there are good reasons to doubt their conclusions, these reviews might misinform us systematically, they might not further but hinder progress, and they might send us up the garden path. This could well be in the commercial interest of the Chinese multi-billion dollar TCM-industry, but it would certainly not be in the interest of patients and good health care.
I happen to be convinced that safety issues related to alternative medicine are important – very important, in fact. Therefore I will continue to report on recent publications addressing them – even at the risk of irritating a few of my readers. And here is such a recent publication:
This review, a sequel to one published 10 years ago, is an evaluation of the number and the severity of adverse events (AEs) reported after acupuncture, moxibustion, and cupping between 2000 and 2011. Relevant English-language reports in 6 databases were identified and assessed by two reviewers; no Asian databases were searched and no articles were included which were in languages other than English. 117 reports of 308 AEs from 25 countries and regions were associated with acupuncture (294 cases), moxibustion (4 cases), or cupping (10 cases). Three patients died after receiving acupuncture.
A total of 239 of infections associated with acupuncture were reported in 17 countries and regions. Korea reported 162 cases, Canada 33, Hong Kong 7, Australia 8, Japan 5, Taiwan 5, UK 4, USA 6, Spain 1, Ireland 1, France 1, Malaysia 1, Croatia 1, Scotland 1, Venezuela 1, Brazil 1, and Thailand 1. Of 38 organ or tissue injuries, 13 were pneumothoraxes; 9 were central nerve system injuries; 4 were peripheral nerve injuries; 5 were heart injuries; 7 were other injuries. These cases originated from 10 countries: 10 from South Korea, 6 from the USA, 6 from Taiwan, 5 from Japan, 3 from the UK, 2 from Germany, 2 from Hong Kong, 1 from Austria, 1 from Iran, 1 from Singapore, and 1 from New Zealand.
The authors concluded “although serious AEs associated with acupuncture are rare, acupuncture practice is not risk-free. Adequate regulation can even further minimize any risk. We recommend that not only adequate training in biomedical knowledge, such as anatomy and microbiology, but also safe and clean practice guidelines are necessary requirements and should continue to be enforced in countries such as the United States where they exist, and that countries without such guidelines should consider developing them in order to minimize acupuncture AEs.”
When I last wrote about the risks of acupuncture, I discussed a Chinese paper reporting 1038 cases of serious adverse events, including 35 fatalities. I was keen to point out that, due to under-reporting, this might just be the tip of a much bigger iceberg. Subsequently, my inbox was full with hate-mail, and comments such as this one appeared on the blog: “This is tiresome old stuff, and we have to wonder what’s wrong with Ernst that he still peddles his dubious arguments.”
I suspect that I will see similar reactions to this post. It probably does not avert the anger to point out that the authors of the new article are, in fact, proponents of acupuncture. Neither will it cool the temper of acupuncture-fans to stress that the new paper completely ignored the Chinese literature as well as articles not published in English; this means that the 1038 Chinese cases (and an unknown amount published in other languages; after all, there might be a lot of published material in Japanese, Korean or other Asian languages) would need adding to the published 308 cases summarised in the new article; and this, in turn, means that the numbers provided here are not even nearly complete. And finally, my re-publishing the conclusions from my previous post is unlikely to apease many acupuncture-enthusiasts either:
True, these are almost certainly rare events – but we have no good idea how rare they are. There is no adverse event reporting scheme in acupuncture, and the published cases are surely only the tip of the ice-berg. True, most other medical treatments carry much greater risks! And true, we need to have the right perspective in all of this!
So let’s put this in a reasonable perspective: with most other treatments, we know how effective they are. We can thus estimate whether the risks outweigh the benefit, and if we find that they do, we should (and usually do) stop using them. I am not at all sure that we can perform similar assessments in the case of acupuncture.
Having previously criticised the abundance of mostly rather meaningless surveys in alternative medicine, I now should perhaps admit to having published my fair share of such investigations. The most recent one was only just published.
The aim of this survey was to conduct a follow-up of a previous, identical investigation and to thus ascertain changes in usage, referral rate, beliefs and attitudes towards alternative medicine during the last decade. A questionnaire was posted in 2009 to all GPs registered with the Liverpool Primary Care Trust asking them whether they treat, refer, endorse or discuss eight common alternative therapies and about their views on National Health Service (NHS) funding, effectiveness, training needs and theoretical validity of each therapy. Comparisons were made between these results and those collected 10 years ago.
The response rate was unfortunately low (32%) compared with the 1999 survey (52%). The main findings were similar as 10 years before: the most popular therapies were still acupuncture, hypnotherapy and chiropractic and the least popular were aromatherapy, reflexology and medical herbalism. GPs felt most comfortable with acupuncture and had greater belief in its theoretical validity, a stronger desire for training in acupuncture and more support for acupuncture to receive NHS funding than for the other alternative therapies. Opinions about homeopathy had become less supportive during the last 10 years. Overall, GPs were less likely to endorse alternative treatments than previously shown (38% versus 19%).
I think these findings speak for themselves. They suggest that British GPs have become more skeptical about alternative medicine in general and about homeopathy in particular. It would, of course, be interesting to know why this is so. Unfortunately we are merely able to speculate here: might it be the increasingly obvious lack of evidence and biological plausibility that matter? As a rationalist, I would hope this to be true but our data do not allow any firm conclusion.
Speaking about the data, I have to admit that they are rather soft. This was just a very small survey in one specific part of the UK. More importantly, the flaws in our investigation are fairly obvious. The most important limitation probably is the low response rate. It may be caused by a general ‘survey-fatigue’ that many GPs suffer from. Whatever the reason, it severely limits the usefulness of our paper.
So why publish the survey at all then? The answer is simple: we certainly do already have an abundance of surveys, but we have a dearth of longitudinal data. Because we employed the same methodology as 10 years ago, this investigation does provide a unique insight into what might have been happening over time – albeit with more than just a pinch of salt.
Some national and international guidelines advise physicians to use spinal manipulation for patients suffering from acute (and chronic) low back pain. Many experts have been concerned about the validity of this advice. Now an up-date of the Cochrane review on this subject seems to provide clarity on this rather important matter.
Its aim was to assess the effectiveness of spinal manipulative therapy (SMT) as a treatment of acute low back pain. Randomized controlled trials (RCTs) testing manipulation/mobilization in adults with low back pain of less than 6-weeks duration were included. The primary outcome measures were pain, functional status and perceived recovery. Secondary endpoints were return-to-work and quality of life. Two authors independently conducted the study selection, risk of bias assessment and data extraction. The effects were examined for SMT versus inert interventions, sham SMT, other interventions, and for SMT as an adjunct to other forms of treatment.
The researchers identified 20 RCTs with a total number of 2674 participants, 12 (60%) RCTs had not been included in the previous version of this review. Only 6 of the 20 studies had a low risk of bias. For pain and functional status, there was low- to very low-quality evidence suggesting no difference in effectiveness of SMT compared with inert interventions, sham SMT or as adjunct therapy. There was varying quality of evidence suggesting no difference in effectiveness of SMT compared with other interventions. Data were sparse for recovery, return-to-work, quality of life, and costs of care.
The authors draw the following conclusion: “SMT is no more effective for acute low back pain than inert interventions, sham SMT or as adjunct therapy. SMT also seems to be no better than other recommended therapies. Our evaluation is limited by the few numbers of studies; therefore, future research is likely to have an important impact on these estimates. Future RCTs should examine specific subgroups and include an economic evaluation.”
In other words, guidelines that recommend SMT for acute low back pain are not based on the current best evidence. But perhaps the situation is different for chronic low back pain? The current Cochrane review of 26 RCTs is equally negative: “High quality evidence suggests that there is no clinically relevant difference between SMT and other interventions for reducing pain and improving function in patients with chronic low-back pain. Determining cost-effectiveness of care has high priority. Further research is likely to have an important impact on our confidence in the estimate of effect in relation to inert interventions and sham SMT, and data related to recovery.”
This clearly begs the question why many of the current guidelines seem to mislead us. I am not sure I know the answer to this one; however I suspect that the panels writing the guidelines might have been dominated by chiropractors and osteopaths or their supporters who have not exactly made a name for themselves for being impartial. Whatever the reason, I think it is time for a re-think and for up-dating guidelines which are out of date and misleading.
Similarly, it might be time to question for what conditions chiropractors and osteopaths, the two professions who use spinal manipulation/mobilisation most, do actually offer anything of real value at all. Back pain and SMT are clearly their domains; if it turns out that SMT is not evidence-based for back pain, what is left? There is no good evidence for anything else, as far as I can see. To make matters worse, there are quite undeniable risks associated with SMT. The conclusion of such considerations is, I fear, obvious: the value of and need for these two professions should be re-assessed.
Many people who have arrived at a certain age have knee osteoarthritis and most of them suffer pain, lack of mobility etc. because of it. There are many effective treatments for this condition, of course, but some have serious side-effects, others are tedious to follow and therefore not popular, and none of the existing options totally cure the problem. In many cases, surgery is the best solution; a knee-endoprosthesis can restore everything almost back to normal. But surgery carries risks and will cause considerable pain and rehabilitation-effort. This is perhaps why we are still looking for a treatment that is both effective and risk-free. Personally, I doubt that such a therapy will ever be found, but that does, of course, not stop alternative medicine enthusiasts from claiming that this or that treatment is what the world has been waiting for. The newest kid on this block is leech therapy. Did I just write “newest”? Leeches are not new at all; they are a treatment from the dark ages of medicine – but are they about to experience a come-back?
A recent systematic review and meta-analysis evaluated the effectiveness of medical leech therapy for osteoarthritis of the knee. Five electronic databases were screened to identify randomized (RCTs) and non randomized controlled clinical trials (CCTs) comparing leech therapy to any type of control condition. The main outcome measures were pain, functional impairment, and joint stiffness. Three RCTs and 1 CCT with a total of 237 patients with osteoarthritis were included. Three trials had, according to the review-authors, a low risk of bias. They claimed to have found strong evidence for immediate and short-term pain reduction, immediate improvement in patients’ physical function, and both immediate and long-term improvement in their joint stiffness. Moderate evidence was found for leech therapy’s short-term effects on physical function and long-term effects on pain. Leech therapy was not associated with any serious adverse events. The authors reached the following conclusion: ” Given the low number of reported adverse events, leech therapy may be a useful approach in treating this condition. Further high-quality RCTs are required for the conclusive judgment of its effectiveness and safety.”
When, about 35 years ago, I worked as a young doctor in the homeopathic hospital in Munich, I was taught how to apply leeches to my patients. We got the animals from a specialised supplier, put them on the patient’s skin and waited until they had bitten a little hole and started sucking the patient’s blood. Once they were full they spontaneously fell off and were then disposed off. Many patients were too disgusted with the prospect of leech therapy to agree to this intervention. Those who did were very impressed with the procedure; it occurred to me then that this therapy must be associated with an enormous placebo-effect simply because it is exotic, impressive and a treatment that no patient will ever forget.
The bite of the leech is not normally painful because the leech has a local anaesthetic which it applies in order to suck blood without being noticed. The leech furthermore injects a powerful anticoagulant into its victim’s body which is necessary for preventing the blood from clotting. Through the injection of these pharmacologically active substances, leeches can clearly be therapeutic and they are thus not entirely unknown in conventional medicine; in plastic surgery, for instance, they are sometimes being used to generate optimal results for micro surgical wounds. Their anticoagulant has long been identified and is sometimes being used therapeutically. The use of leeches for the management of osteoarthritis, however, is not a conventional concept. So, how convincing are the above data? Should we agree with the authors’ conclusion that “leech therapy may be a useful approach in treating this condition“? I think not, and here is why:
1) The collective evidence for efficacy is far from convincing. The few studies which were summarised in this systematic review are mostly those of the research group that also authored the review. Critical thinkers would insist on an independent assessment of those trials. Moreover, none of the trials was patient-blind (which would not be all that difficult to do), and thus the enormous placebo-effect of applying a leech might be the cause of all or most of the observed effect.
2) The authors claim that the treatment is safe. On the basis of just 250 patients treated under highly controlled conditions, this claim has almost no evidential basis.
3) As already mentioned above, there are many treatments which are more effective for improving pain and function than leeches.
4) Leech therapy is time-consuming, relatively expensive and quite unpractical as a regular, long-term therapy.
5) In my experience, patients will run a mile to avoid having something as ‘disgusting’ as leeches sucking blood from their body.
6) The animals need to be destroyed after the treatment to avoid infections.
7) As multiple leeches applied regularly will suck a significant volume of blood, the treatment might lead to anaemia and would be contra-indicated in patients with low haemoglobin levels.
8) Like most other treatments for osteoarthritis, leech therapy would not be curative but might just alleviate the symptoms temporarily.
On balance therefore, I very much doubt that the leech will have a come-back in the realm of osteoarthritis therapy. In fact, I think that, in this particular context, leeches are just a chapter from the dark ages of medicine. Their re-introduction into osteoarthritis care seems like a significant step into the wrong direction.