It hardly is a secret: we have a growing problem with obesity. Worldwide it is predicted to cause millions of premature deaths – unless, of course, we come up with a safe and effective treatment that patients find acceptable.
Many herbal remedies are being promoted as the solution to this serious problem. My team looked at the evidence for such treatments in much detail. Sadly the results were less than impressive.
But now, there seems to be new hope! Two recent studies of a specific herbal mixture report amazingly good results – or are they perhaps too good to be true?
Stern JS, Peerson J, Mishra AT, Sadasiva Rao MV and Rajeswari KP from the Department of Nutrition and the Department of Internal Medicine, University of California Davis, have just published an RCT in 60 subjects with body mass index (BMI) between 30 and 40 kg/square meter. Participants received either 400 mg herbal capsules with extracts from Sphaeranthus indicus and Garcinia mangostana or 400 mg placebo capsules twice daily. During the study period, participants consumed a standard diet (2,000 kcal per day) and walked 30 min 5 days per week.
After 8 weeks of this treatment, significant reductions in body weight (3.7 kg), BMI (1.6 kg/m2), and waist circumference (5.4 cm) were observed in the herbal group compared with placebo. Additionally, a significant increase in serum adiponectin concentration was found in the herbal group versus placebo. Adverse events were mild and were equally distributed between the two groups.
The authors’ conclusion leave no doubt: Supplementation with the herbal blend resulted in a greater degree of weight loss than placebo over 8 weeks.
As our own review had suggested that extracts of Garcinia cause small short-term weight reductions, the results did not come as a complete surprise to me. What did strike me as odd, however, was the fact that almost simultaneously another article was published. It was authored by Stern JS, Peerson J, Mishra AT, Mathukumalli VS and Konda PR from the Department of Nutrition, University of California-Davis, and it reported the pooled data from the above plus another, similarly designed trial.
The two studies together enrolled 100 patients who were treated either with the same herbal formula or with placebo. All subjects received 2000 kcal/day throughout the study and walked 5 days a week for 30 min. The primary outcome was the reduction in body weight. Secondary outcomes were reductions in BMI and in waist and hip circumference. Serum glycaemic, lipid, and adiponectin levels were also measured. Ninety-five subjects completed the trials, and the data from these two studies were pooled and analysed.
At study conclusion (8 weeks), statistically significant reductions in body weight (5.2 kg), BMI (2.2 kg/m2), as well as waist (11.9 cm) and hip circumferences (6.3 cm) were observed in the pooled herbal groups compared with placebo. A significant increase in serum adiponectin concentration was also found in the herbal groups versus placebo at study conclusion along with reductions in fasting blood glucose (12.2%), cholesterol (13.8%), and triglyceride (41.6%) concentrations. No changes were seen across organ function panels, multiple vital signs, and no major adverse events were reported. The minor adverse events were equally distributed between the two groups.
And what should be odd about that? Authors are entitled to pool the data of two of their own trials! Yes, of course, but what confuses me is the fact that the data from the second study of 40 patients cannot be found anywhere. I would have liked to see how it is possible that the results from just 40 more patients (actually just 35 seemed to have been included in the analysis) raise the average weight loss from 3.7 kg in the first RCT to a remarkable 5.2 kg in the two RCTs together. As a rough estimate, this means that, in the second trial, patients who took the herbal mixture must have lost about one kilo per week more than those who were on placebo. If true, this outcome is pretty sensational! It could signal the end of the obesity epidemic. It would also mean that the manufacturer of this herbal wonder mixture stands to earn billions.
Considering the potential importance of these findings, I would also like to know what precisely the Californian researchers’ involvement has been in these two studies. In the second article they state that: The two clinical trials were performed at Alluri Sitarama Raju Academy of Medical Sciences (ASRAM), Eluru, Andhra Pradesh, India from November 2009 to April 2010 (clinical trial registration number: ISRCTN45078827) and from March 2010 to July 2010 (clinical trial registration number: ISRCTN52261953). I find this puzzling.
Moreover, it would be interesting to learn what happened to the following co-authors of the first study: Sadasiva, Rao MV and Rajeswari KP. As authors of the largest of the two trials, I would have thought their names would have to be included in the article reporting the pooled data of the two studies.
Call me sceptical, perhaps even cynical, but I do wonder about trials which seem to beg so many intriguing questions. In case you want to know who funded these studies and who thus stands to make the above-named billions, the answer is provided in the second paper: This work was supported by an unrestricted grant from InterHealth Nutraceuticals Inc., Benicia, CA, to J.S.S.
So, do I think that we have finally identified a safe and effective treatment to combat the worldwide epidemic of obesity? Well….
Did I previously imply that osteopaths are not very research-active? Shame on me!
Here are two brand-new studies by osteopaths and they both seem to show that their treatments work.
Well, perhaps we better have a closer look at them before we start praising osteopathic research efforts.
THE FIRST STUDY
Researchers from the ‘European Institute for Evidence Based Osteopathic Medicine’ in Chieti, Italy, investigated the effect of osteopathic manipulative therapy (OMT) on the length of hospital-stay (LOHS) in premature infants. They conducted an RCT on 110 preterm newborns admitted to a single specialised unit. Thus the subjects with a gestational age between 28 and 38 weeks were randomized to receive either just routine care, or routine care with OMT for the period of hospitalization. Endpoints were differences in LOHS and daily weight gain. The results showed a mean difference in LOHS between the OMT and the control group: -5.906 days (95% C.I. -7.944, -3.869; p<0.001). However, OMT was not associated with any change in daily weight gain.
The authors’ conclusion was bold: OMT may have an important role in the management of preterm infants hospitalization.
THE SECOND STUDY
The second investigation suggested similarly positive effects of OMT on LOHS in a different setting. Using a retrospective cohort study, US osteopaths wanted to determine whether there is a relationship between post-operative use of OMT and post-operative outcomes in gastrointestinal surgical patients, including time to flatus, clear liquid diet, and bowel movement [all indicators for the length of the post-operative ileus] as well as LOHS. They thus assessed the records of 55 patients who underwent a major gastrointestinal operation in a hospital that had been routinely offering OMT to its patients. The analyses showed that 17 patients had received post-operative OMT and 38 had not.The two groups were similar in terms of all variables the researchers managed to assess. The time to bowel movement and to clear liquid diet did not differ significantly between the groups. The mean time to flatus was 4.7 days in the non-OMT group and 3.1 days in the OMT group (P=.035). The mean post-operative hospital LOHS was also reduced significantly with OMT, from 11.5 days in the non-OMT group to 6.1 days in the OMT group (P=.006).
The authors concluded that OMT applied after a major gastrointestinal operation is associated with decreased time to flatus and decreased postoperative hospital LOHS.
WHAT SHOULD WE MAKE OF THESE RESULTS?
Some people may have assumed that OMT is for bad backs; these two studies imply, however, that it can do much more. If the findings are correct, they have considerable implications: shortening the time patients have to spend in hospital would not only decrease individual suffering, it would also save us all tons of money! But do these results hold water?
The devil’s advocate in me cannot help but being more than a little sceptical. I fail to see how OMT might shorten LOHS; it just does not seem plausible! Moreover, some of the results seem too good to be true. Could there be any alternative explanations for the observed findings?
The first study, I think, might merely demonstrate that more time spent handling premature babies provides a powerful developmental stimulus. Therefore the infants are quicker ready to leave hospital compared to those children who did not receive this additional boost. But the effect might not at all be related to OMT per se; if, for instance, the parents had handled their children for the same amount of time, the outcome would probably have been quite similar, possibly even better.
The second study is not an RCT and therefore it tells us little about cause and effect. We might speculate, for instance, that those patients who elected to have OMT were more active, had lived healthier lives, adhered more rigorously to a pre-operative diet, or differed in other variables from those patients who chose not to bother with OMT. Again, the observed difference in the duration of the post-operative ileus and consequently the LOHS would be entirely unrelated to OMT.
I suggest therefore to treat these two studies with more than just a pinch of salt. Before hospitals all over the world start employing osteopaths right, left and centre in order to shorten their average LOHS, we might be well advised to plan and conduct a trial that avoids the pitfalls of the research so far. I would bet a fiver that, once we do a proper independent replication, we will find that both investigations did, in fact, generate false positive results.
My conclusion from all this is simple: RESEARCH CAN SOMETIMES BE MISLEADING, AND POOR QUALITY RESEARCH IS ALMOST INVARIABLY MISLEADING.
A recently published study by Danish researchers aimed at comparing the effectiveness of a patient education (PEP) programme with or without the added effect of chiropractic manual therapy (MT) to a minimal control intervention (MCI). Its results seem to indicate that chiropractic MT is effective. Is this the result chiropractors have been waiting for?
To answer this question, we need to look at the trial and its methodology in more detail.
A total of 118 patients with clinical and radiographic unilateral hip osteoarthritis (OA) were randomized into one of three groups: PEP, PEP+ MT or MCI. The PEP was taught by a physiotherapist in 5 sessions. The MT was delivered by a chiropractor in 12 sessions, and the MCI included a home stretching programme. The primary outcome measure was the self-reported pain severity on an 11-box numeric rating scale immediately following the 6-week intervention period. Patients were subsequently followed for one year.
The primary analyses included 111 patients. In the PEP+MT group, a statistically and clinically significant reduction in pain severity of 1.9 points was noted compared to the MCI of 1.90. The number needed to treat for PEP+MT was 3. No difference was found between the PEP and the MCI groups. At 12 months, the difference favouring PEP+MT was maintained.
The authors conclude that for primary care patients with osteoarthritis of the hip, a combined intervention of manual therapy and patient education was more effective than a minimal control intervention. Patient education alone was not superior to the minimal control intervention.
This is an interesting, pragmatic trial with a result suggesting that chiropractic MT in combination with PEP is effective in reducing the pain of hip OA. One could easily argue about the small sample size, the need for independent replication etc. However, my main concern is the fact that the findings can be interpreted in not just one but in at least two very different ways.
The obvious explanation would be that chiropractic MT is effective. I am sure that chiropractors would be delighted with this conclusion. But how sure can we be that it would reflect the truth?
I think an alternative explanation is just as (possibly more) plausible: the added time, attention and encouragement provided by the chiropractor (who must have been aware what was at stake and hence highly motivated) was the effective element in the MT-intervention, while the MT per se made little or no difference. The PEP+MT group had no less than 12 sessions with the chiropractor. We can assume that this additional care, compassion, empathy, time, encouragement etc. was a crucial factor in making these patients feel better and in convincing them to adhere more closely to the instructions of the PEP. I speculate that these factors were more important than the actual MT itself in determining the outcome.
In my view, such critical considerations regarding the trial methodology are much more than an exercise in splitting hair. They are important in at least two ways.
Firstly, they remind us that clinical trials, whenever possible, should be designed such that they allow only one interpretation of their results. This can sometimes be a problem with pragmatic trials of this nature. It would be wise, I think, to conduct pragmatic trials only of interventions which have previously been proven to work. To the best of my knowledge, chiropractic MT as a treatment for hip OA does not belong to this category.
Secondly, it seems crucial to be aware of such methodological issues and to consider them carefully before research findings are translated into clinical practice. If not, we might end up with therapeutic decisions (or guidelines) which are quite simply not warranted.
I would not be in the least surprised, if chiropractic interest groups were to use the current findings for promoting chiropractic in hip-OA. But what, if the MT per se was ineffective, while the additional care, compassion and encouragement was? In this case, we would not need to recruit (and pay for) chiropractors and put up with the considerable risks chiropractic treatments can entail; we would merely need to modify the PE programme such that patients are better motivated to adhere to it.
As it stands, the new study does not tell us much that is of any practical use. In my view, it is a pragmatic trial which cannot readily be translated into evidence-based practice. It might get interpreted as good news for chiropractic but, in fact, it is not.
S.O. Hansson from the Royal Institute of Technology, Stockholm, Sweden recently published an interesting comment on the law regulating the labelling of homeopathic products. In it he points out that, in the European Union (EU), all pre-packaged food products must contain a list of ingredients and their quantities. The list should be “accurate, clear and easy to understand for the consumer.” Similar requirements apply to pharmaceutical drugs and products – with one notable exception: homeopathic preparations.
For such products, the ingredients need not be disclosed on the label, which should instead specify “the scientific name of the stock or stocks followed by the degree of dilution.” The degree of homeopathic dilutions is, in turn, given in an understandable jargon, such as “C60”, which actually describes a dilution of 1:10120.
The point Hansson is trying to make is that very few health care professionals and even fewer consumers would understand such abbreviations and jargon. This means that, manufacturers of homeopathic products are legally permitted to hide the fact from their customers that their remedies typically contain no active ingredient at all. Considering that homeopathic products are typically bought ‘over the counter’ (OTC), i.e. without interference from a health care professional, just like food products, the exemption seems most surprising.
The most OTC homeopathic remedies are in the “C30” potency; this signifies a dilution of 1: 1 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000 000. The likelihood that any potency higher than “C12” might contain a single molecule of active ingredient is very close to zero. In order to comprehend the degree of dilution in homeopathy more fully, a visual approach might be best: for it to have a reasonable chance to contain just one single molecule of active ingredient, a homeopathic pill in a “C30” potency would need to have a diameter roughly equal to the distance between the earth and the sun. Homeopathy is truly impossible to swallow.
If homeopathic manufacturers were obliged to provide a description that is “accurate, clear and easy to understand for the consumer”, it would need to state that any dilution beyond “C12” contains no active molecule. It seems clear that such accurate, clear and understandable information would discourage most consumers to spend their hard-earned money for such nonsense. It seems thus to be obvious that the EU exemption of homeopathic remedies from honest labelling protects the interests of the homeopathic industry.
But surely, this is deeply wrong. Regulations in health care are not supposed to protect commercial interests, they should protect the consumer. In my view, it is time to change such profoundly misguided EU-regulation – in the interest of honesty, single standards, transparency and foremost in the interest of the patient and the consumer.
A cult can be defined not just in a religious context, but also as a” usually nonscientific method or regimen claimed by its originator to have exclusive or exceptional power in curing a particular disease.” After ~20 years of researching this area, I have come to suspect that much of alternative medicine resembles a cult – a bold statement, so I better explain.
One characteristic of a cult is the unquestioning commitment of its members to the bizarre ideas of their iconic leader. This, I think, chimes with several forms alternative medicine. Homeopaths, for instance, very rarely question the implausible doctrines of Hahnemann who, to them, is some sort of a semi-god. Similarly, few chiropractors doubt even the most ridiculous assumptions of their founding father, D D Palmer who, despite of having been a somewhat pathetic figure, is uncritically worshipped. By definition, a cult-leader is idealised and thus not accountable to anyone; he (yes, it is almost invariably a male person) cannot be proven wrong by logic arguments nor by scientific facts. He is quite simply immune to any form of scrutiny. Those who dare to disagree with his dogma are expelled, punished, defamed or all of the above.
Cults tend to brain-wash their members into unconditional submission and belief. Likewise, fanatics of alternative medicine tend to be brain-washed, i.e. systematically misinformed to the extend that reality becomes invisible. They unquestioningly believe in what they have been told, in what they have read in their cult-texts, and in what they have learnt from their cult-peers. The effects of this phenomenon can be dramatic: the powers of discrimination of the cult-member are reduced, critical questions are discouraged, and no amount of evidence can dissuade the cult-member from abandoning even the most indefensible concepts. Internal criticism is thus by definition non-existent.
Like religious cults, many forms of alternative medicine promote an elitist concept. Cult-members become convinced of their superiority, based not on rational considerations but on irrational beliefs. This phenomenon has a range of consequences. It leads to the isolation of the cult-member from the rest of the world. By definition, critics of the cult do not belong to the elite; they are viewed as not being able to comprehend the subtleties of the issues at hand and are thus ignored or not taken seriously. For cult-members, external criticism is thus non-existent or invalid.
Cult-members tend to be on a mission, and so are many enthusiasts of alternative medicine. They use any conceivable means to recruit new converts. For instance, they try to convince family, friends and acquaintances of their belief in their particular alternative therapy at every conceivable occasion. They also try to operate on a political level to popularize their cult. They cherry pick data, often argue emotionally rather than rationally, and ignore all arguments which contradict their belief system.
Cult-members, in their isolation from society, tend to be assume that there is little worthy of their consideration outside the cult. Similarly, enthusiasts of alternative medicine tend to think that their treatment is the only true method of healing. Therapies, concepts and facts which are not cult-approved are systematically defamed. An example is the notion of BIG PHARMA which is employed regularly in alternative medicine. No reasonable person assumes that the pharmaceutical industry smells of roses. However, the exaggerated and systematic denunciation of this industry and its achievements is a characteristic of virtually all branches of alternative medicine. Such behaviour usually tells us more about the accuser than the accused.
There are many other parallels between a cult and alternative medicine, I am sure. In my view, the most striking one must be the fact that any spark of cognitive dissonance in the cult-victim is being extinguished by highly effective and incessant flow of misinformation which often amounts to a form of brain-washing.
Acupuncture is not just one single form of therapy, there are dozens of variations of this theme. For instance, acupuncture-points can, according to proponents of this form of treatment, be stimulated in a number of ways: needles, heat (moxibustion), electrical current, laser-light, ultrasound or pressure. In the latter case, the therapy is called acupressure. This therapy is popular and often recommended as a form of self-treatment, for instance, to alleviate nausea and vomiting of all causes.
Chemotherapy-induced nausea/vomiting can normally be successfully treated with standard anti-emetic drugs. Some patients, however, may not respond satisfactorily and others prefer a drug-free option such as acupressure for which there has been encouraging evidence. A brand-new study sheds new light on this issue.
Its objective was to assess the effectiveness and cost-effectiveness of self-administered acupressure using wristbands compared with sham acupressure wristbands and standard care alone in the management of chemotherapy-induced nausea. Secondary objectives included assessment of the effectiveness and cost-effectiveness of the wristbands in relation to vomiting and quality of life and exploration of any age, gender and emetogenic risk effects. The trial was conducted in outpatient chemotherapy clinics in three regions in the UK involving 14 different cancer units/centres. Chemotherapy-naïve cancer patients were included receiving chemotherapy of low, moderate and high emetogenic risk. The intervention were acupressure wristbands pressing the P6 point (anterior surface of the forearm), sham-wrist bands providing no pressure on acupuncture-points or no wrist-bands at all; all three groups had standard care in addition. The main outcome measures were the Rhodes Index for Nausea/Vomiting, the Multinational Association of Supportive Care in Cancer (MASCC) Antiemesis Tool and the Functional Assessment of Cancer Therapy – General (FACT-G). At baseline participants also completed measures of anxiety/depression, nausea/vomiting expectation and expectations from using the wristbands.
In total, 500 patients were randomised (166 standard care, 166 sham acupressure + standard care, and 168 acupressure + standard care). Data were available for 361 participants for the primary outcome. The primary outcome analysis (nausea in cycle 1) revealed no differences between the three arms. Women responded more favourably to the use of sham acupressure wristbands than men. No significant differences were detected in relation to vomiting outcomes, anxiety and quality of life. Some transient adverse effects were reported, including tightness in the area of the wristbands, feeling uncomfortable when wearing them and minor swelling in the wristband area.There were no statistically significant cost differences associated with the use of real acupressure bands.
In total, 26 patients took part in qualitative interviews. The qualitative data suggested that participants perceived the wristbands (both real and sham) as effective and helpful in managing their nausea during chemotherapy.
The authors concluded that there were no statistically significant differences between the three arms in terms of nausea, vomiting and quality of life.
Intriguingly, this study was published in two different journals; and the second article reporting the identical data concluded that no clear recommendations can be made about the use of acupressure wristbands in the management of chemotherapy-related nausea and vomiting.
A further equally new study tested acupressure for post-operative nausea/vomiting. One hundred and thirty-four healthy, non-smoking women scheduled for breast surgery were randomised either to P6 stimulation or to sham control. Wristbands were applied and covered with a dressing before induction of anaesthesia. Follow-up was carried out three times within 24 h postoperative. Primary outcomes were postoperative nausea and/or vomiting.
One hundred and twelve patients completed the study. There were no statistically significant differences in the incidence of nausea or vomiting. Approximately, one third of the patients reported adverse-effects caused by the wristband, for example, redness, swelling and tenderness.
The authors of this trial concluded as follows: We did not find the Vital-Band effective in preventing either nausea or vomiting after operation in women undergoing breast surgery.
There has been quite a bit of previous research on acupressure. The most recent summary included 2 meta-analyses, 6 systematic reviews and 39 RCTs of acupressure for various conditions. Its authors stated that the strongest evidence was for pain (particularly dysmenorrhoea, lower back and labour), post-operative nausea and vomiting.
So, is acupressure effective in reducing nausea and vomiting or not? The evidence is contradictory to a degree that is baffling. If we look closer at the existing trials, we are likely to find that the more rigorous studies and those published by researchers who do not have an axe to grind tend to produce negative findings. I am therefore not convinced that acupressure has any effects beyond placebo.
Sorry, but I am fighting a spell of depression today.
Why? I came across this website which lists the 10 top blogs on alternative medicine. To be precise, here is what they say about their hit-list: this list includes the top 10 alternative medicine bloggers on Twitter, ranked by Klout score. Using Cision’s media database, we compiled the list based on Cision’s proprietary research, with results limited to bloggers who dedicate significant coverage to alternative medicine and therapies…
And here are the glorious top ten:
All of these sites are promotional and lack even the slightest hint of critical evaluation. All of them sell or advertise products and are thus out to make money. All of them are full of quackery, in my view. Some of the most popular bloggers are world-famous quacks!
What about impartial information for the public? What about critical review of the evidence? What about a degree of balance? What about guiding consumers to make responsible, evidence-based decisions? What about preventing harm? What about using scarce resources wisely?
I don’t see any of this on any of the sites.
You see, now I have depressed you too!
Quick, buy some herbal, natural, holistic and integrative anti-depressant! As it happens, I have some for sale….
Some people will probably think that I am obsessed with writing about the risk of chiropractic. True, I have published quite a bit on this subject, both in the peer-reviewed literature as well as on this blog – but not because I am obsessed; on this blog, I will re-visit the topic every time a relevant new piece of evidence becomes available because it is indisputably such an important subject. Writing about it might prevent harm.
So far, we know for sure that mild to moderate as well as serious complications, including deaths, do occur after chiropractic spinal manipulations, particularly those of the upper spine. What we cannot say with absolute certainty is whether they are caused by the treatment or whether they happened coincidentally. Our knowledge in this area relies mostly on case-reports and surveys which, by their very nature, do not allow causal inferences. Therefore chiropractors have, in the past, been able to argue that a causal link remains unproven.
A brand-new blinded parallel group RCT might fill this gap in our knowledge and might reject or establish the notion of causality once and for all. The authors’ objective was to establish the frequency and severity of adverse effects from short term usual chiropractic treatment of the spine when compared to a sham treatment group. They thus conducted the first ever RCT with the specific aim to examine the occurrence of adverse events resulting from chiropractic treatment. It was conducted across 12 chiropractic clinics in Perth, Western Australia. The participants comprised 183 adults, aged 20-85, with spinal pain. Ninety two participants received individualized care consistent with the chiropractors’ usual treatment approach; 91 participants received a sham intervention. Each participant received two treatment sessions.
Completed adverse questionnaires were returned by 94.5% of the participants after the first appointment and 91.3% after the second appointment. Thirty three per cent of the sham group and 42% of the usual care group reported at least one adverse event. Common adverse events were increased pain (sham 29%; usual care 36%), muscle stiffness (sham 29%; usual care 37%), headache (sham 17%; usual care 9%). The relative risk was not significant for either adverse event occurrence (RR = 1.24 95% CI 0.85 to 1.81); occurrence of severe adverse events (RR = 1.9; 95% CI 0.98 to 3.99); adverse event onset (RR = 0.16; 95% CI 0.02 to 1.34); or adverse event duration (RR = 1.13; 95% CI 0.59 to 2.18). No serious adverse events were reported.
The authors concluded that a substantial proportion of adverse events following chiropractic treatment may result from natural history variation and non-specific effects.
If we want to assess causality of effects, we have no better option than to conduct an RCT. It is the study design that can give us certainty, or at least near certainty – that is, if the RCT is rigorous and well-made. So, does this study reject or confirm causality? The disappointing truth is that it does neither.
Adverse events were clearly more frequent with real as compared to sham-treatment. Yet the difference failed to be statistically significant. Why? There are at least two possibilities: either there was no true difference and the numerically different percentages are a mere fluke; or there was a true difference but the sample size was too small to prove it.
My money is on the second option. The number of patients was, in my view, way too small for demonstrating differences in frequencies of adverse effects. This applies to the adverse effects noted, but also, and more importantly, to the ones not noted.
The authors state that no serious adverse effects were observed. With less that 200 patients participating, it would have been most amazing to see a case of arterial dissection or stroke. From all we currently know, such events are quite rare and occur perhaps in one of 10 000 patients or even less often. This means that one would require a trial of several hundred thousand patients to note just a few of such events, and an RCT with several million patients to see a difference between real and sham treatment. It seems likely that such an undertaking will never be affordable.
So, what does this new study tell us? In my view, it is strong evidence to suggest a causal kink between chiropractic treatment and mild to moderate adverse effects. I dose not prove it, but merely suggests it – yet I am fairly sure that chiropractors, once again, will not agree with me.
Postoperative ileus (POI), the phenomenon that after an operation the intestines tend to be inactive for a few days, can cause intense pain and thus contributes significantly to human suffering. It also prolongs hospital stay and increases the risks of post-operative complications. There is no known effective treatment for POI.
In China, POI is often treated with acupuncture, and due to this fact acupuncture became known in the West: James Reston, a journalist who accompanied Nixon on his first trip to China, had to have an appendectomy in a Beijing hospital, he subsequently suffered from POI, was treated with acupuncture and moxibustion, experienced symptom-relief, and subsequently wrote about it in the New York Times. This was the beginning of the present acupuncture-boom.
Since then, thousands of acupuncture trials have been published but, intriguingly, very few have tested the effectiveness of acupuncture for POI. Now researchers from the Sloan Kettering Cancer Center in New York have conducted a randomized, sham-controlled trial to test whether acupuncture reduces POI more effectively than sham acupuncture.
Ninety colon cancer patients undergoing elective colectomy were randomized to receive 30 min of true or sham acupuncture twice daily during their first three postoperative days. GI-3 (the later of the following two events: time that the patient first tolerated solid food, AND time that the patient first passed flatus OR a bowel movement) and GI-2 (the later of the following two events: time patient first tolerated solid food AND time patient first passed a bowel movement) were determined. Pain, nausea, vomiting, and use of pain medications were evaluated daily for the first three postoperative days. Eighty-one patients received the allocated intervention: 39 the true acupuncture and 42 the sham acupuncture. The mean time to GI-3 was 149 hours and 146 hours for the acupuncture group and the sham acupuncture group. No significant differences were found between groups for secondary endpoints.
The authors’ conclusion was clear: True acupuncture as provided in this study did not reduce POI more significantly than sham acupuncture.
So, did a mere misunderstanding start the present acupuncture boom? POI inevitably normalises with time. Did the journalist just imagine that acupuncture helped, while nature cured the condition? It would seem so, according to this study. But perhaps things are not just black or white. Almost at the same time as the New York trial, another study was emerged.
Researchers from Hong Kong conducted an RCT with 165 patients undergoing elective laparoscopic surgery for colonic and upper rectal cancer. Patients were assigned randomly to receive electroacupuncture (n = 55) or sham acupuncture (n = 55), once daily from postoperative days 1-4, or no acupuncture (n = 55). The primary outcome was time to defecation. Secondary outcomes included postoperative analgesic requirement, time to ambulation, and length of hospital stay. The results showed that patients who received electroacupuncture had a shorter time to defecation than patients who received no acupuncture (85.9 ± 36.1 vs 122.1 ± 53.5 h) and length of hospital stay (6.5 ± 2.2 vs 8.5 ± 4.8 days). Patients who received electroacupuncture also had a shorter time to defecation than patients who received sham acupuncture (85.9 ± 36.1 vs 107.5 ± 46.2 h). Electroacupuncture was more effective than no or sham acupuncture in reducing postoperative analgesic requirement and time to ambulation.
The Chinese researchers’ conclusion is equally clear: electroacupuncture reduced the duration of postoperative ileus, time to ambulation, and postoperative analgesic requirement, compared with no or sham acupuncture, after laparoscopic surgery for colorectal cancer.
The only other trial I know in this area failed to show that acupuncture shortens POI. What should we make of these data? A systematic review would be nice, of course, but, to the best of my knowledge, none is currently available.
Is this a question of everyone being able to pick and chose the evidence they like? Is it a question of who we trust, the researchers in New York or those in China? Is it a question of where the treatment was done authentically? Is it a question of critically analysing which study had the higher risks of bias? Or is it a question of simply saying that two negative studies are more than one positive trial?
Confused? Me too, a little!
Whatever answers we chose, several things seems fairly certain to me. It would be wrong to say that there is good evidence for acupuncture as a treatment of POI. And the acupuncture-boom that ensued after Reston’s article was to a very large degree built on a simple misunderstanding: POI is a condition that resolves literally into thin air whether we treat it or not.
On this blog, we have repeatedly discussed the serious adverse effects of Spinal Manipulative Therapies (SMT) as frequently administered by chiropractors, osteopaths and physiotherapists. These events mostly relate to vascular accidents involving vertebral or carotid arterial dissections after SMT of the upper spine. Lower down, the spine is anatomically far less vulnerable which, however, does not mean that injuries in this region after SMT are impossible. They have been reported repeatedly but, to the best of my knowledge, there is no up-to-date review of such events – that is until recently.
Australian researchers have just filled this gap by publishing a systematic review aimed at systematically reviewing all reports of serious adverse events following lumbo-pelvic SMT. They conducted electronic searches in MEDLINE, EMBASE, CINAHL, and The Cochrane Library up to January 12, 2012. Article-selection was performed by two independent reviewers using predefined criteria. Cases were included involving individuals 18 years or older who experienced a serious adverse event following SMT applied to the lumbar spine or pelvis by any type of provider (chiropractic, medical, physical therapy, osteopathic, layperson). A serious adverse event was defined as an untoward occurrence that resulted in death or was life threatening, required hospital admission, or resulted in significant or permanent disability. Reports published in English, German, Dutch, and Swedish were included.
The searches identified a total of 2046 papers, and 41 articles reporting a total of 77 cases were included in the review. Important case details were frequently missing in these reports, such as descriptions of SMT technique, the pre-SMT presentation of the patient, the specific details of the adverse event, time from SMT to the adverse event, factors contributing to the adverse event, and clinical outcome.
The 77 adverse events consisted of cauda equina syndrome (29 cases); lumbar disk herniation (23 cases); fracture (7 cases); haematoma or haemorrhagic cyst (6 cases); and12 cases of neurologic or vascular compromise, soft tissue trauma, muscle abscess formation, disrupted fracture healing, and oesophageal rupture.
The authors’ conclusion was that this systematic review describes case details from published articles that describe serious adverse events that have been reported to occur following SMT of the lumbo-pelvic region. The anecdotal nature of these cases does not allow for causal inferences between SMT and the events identified in this review.
This review is timely and sound. Yet several factors need consideration:
1) The search strategy was thorough but it is unlikely that all relevant articles were retrieved because these papers are often well-hidden in obscure and not electronically listed journals.
2) It is laudable that the authors included languages other than English but it would have been preferable to impose no language restrictions at all.
3) Under-reporting of adverse events is a huge problem, and it is anyone’s guess how large it really is [we have shown that, in our research it was precisely 100%]
4) This means that the 77 cases, which seem like a minute number, could in reality be 770 or 7700 or 77000; nobody can tell.
Cauda equina (horse tail) syndrome was the most frequent and most serious adverse event reported. This condition is caused by nerve injury at the lower end of the spinal canal. Symptoms can include leg pain along the sciatic nerve, severe back pain, altered or loss of sensation over the area around the genitals, anus and inner thighs as well as urine retention or incontinence and faecal incontinence. The condition must be treated as an emergency and usually requires surgical decompression of the injured nerves.
Disk herniation, the second most frequent adverse event, is an interesting complication of SMT. Most therapists using SMT would probably claim (no, I have no reference for that speculation!) that they can effectively treat herniated disks with SMT. The evidence for this claim is, as far as I know, non-existent. In view of the fact that SMT can actually cause a disk to herniate, I wonder whether SMT should not be contra-indicated for this condition. I am sure there will be some discussion about this question following this post.
The authors make a strong point about the fact that case reports never allow causal inference. One can only agree with this notion. However, the precautionary principle in medicine also means that, if case reports provide reasonable suspicion that an intervention might led to adverse-effects, we need to be careful and should warn patients of this possibility. It also means that it is up to the users of SMT to demonstrate beyond reasonable doubt that SMT is safe.