MD, PhD, FMedSci, FSB, FRCP, FRCPEd

clinical trial

Chronic neck pain is common and makes the life of many sufferers a misery. Pain-killers are helpful, of course, but who wants to take such medications on the long-term? Is there anything else these patients can do?

Massage therapy has been shown to work but how often for how long? This trial was designed to evaluate the optimal dose of massage for individuals with chronic neck pain. 228 individuals with chronic non-specific neck pain were recruited and randomized them to 5 groups receiving various doses of massage:

  1. 30-minute treatments 2 or 3 times weekly
  2. 60-minute treatments once weekly
  3. 60-minutte treatments twice weekly
  4. 60-minute treatments thrice weekly
  5. a 4-week period on a wait list

Neck-related dysfunction was assessed with the Neck Disability Index (range, 0-50 points) and pain intensity with a numerical rating scale (range, 0-10 points) at baseline and at 5 weeks.

The results suggested that 30-minute treatments were not significantly better than the waiting list control condition in terms of achieving a clinically meaningful improvement in neck dysfunction or pain, regardless of the frequency of treatments. In contrast, 60-minute treatments 2 and 3 times weekly significantly increased the likelihood of such improvement compared with the control condition in terms of both neck dysfunction and pain intensity.

The authors conclude that after 4 weeks of treatment, we found multiple 60-minute massages per week more effective than fewer or shorter sessions for individuals with chronic neck pain. Clinicians recommending massage and researchers studying this therapy should ensure that patients receive a likely effective dose of treatment.

So two or three hours of massage therapy seems to be optimal as a treatment for chronic neck pain. This would cost ~£ 200-300 per week! Who can or wants to afford this? And are there other options that might be less expensive and equally or more effective? For instance, is physiotherapeutic exercise an option?

I am not sure I know the answers to these questions but, before we recommend massage therapy to the many who chronically suffer from neck pain, we should find out.

The safety of the manual treatments such as spinal manipulation is a frequent subject on this blog. Few experts would disagree with the argument that more good data are needed – and what could be better data than that coming from a randomised clinical trial (RCT)?

The aim of this RCT was to investigate differences in occurrence of adverse events between three different combinations of manual treatment techniques used by manual therapists (i.e. chiropractors, naprapaths, osteopaths, physicians and physiotherapists) for patients seeking care for back and/or neck pain.

Participants were recruited among patients seeking care at the educational clinic of the Scandinavian College of Naprapathic Manual Medicine in Stockholm. 767 patients were randomized to one of three treatment arms:

  1.  manual therapy (i.e. spinal manipulation, spinal mobilization, stretching and massage) (n = 249),
  2.  manual therapy excluding spinal manipulation (n = 258)
  3.  manual therapy excluding stretching (n = 260).

Treatments were provided by students in the seventh semester (of total 8). Adverse events were monitored via a questionnaire after each return visit and categorized in to five levels:

  1. short minor,
  2. long minor,
  3. short moderate,
  4. long moderate,
  5. serious

This was based on the duration and/or severity of the event.

The most common adverse events were soreness in muscles, increased pain and stiffness. No differences were found between the treatment arms concerning the occurrence of these adverse event. Fifty-one percent of patients, who received at least three treatments, experienced at least one adverse event after one or more visits. Women more often had short moderate adverse events, and long moderate adverse events than men.

The authors conclude that adverse events after manual therapy are common and transient. Excluding spinal manipulation or stretching do not affect the occurrence of adverse events. The most common adverse event is soreness in the muscles. Women reports more adverse events than men.

What on earth is naprapathy? I hear you ask. Here is a full explanation from a naprapathy website:

Naprapathy is a form of bodywork that is focused on the manual manipulation of the spine and connective tissue. Based on the fundamental principles of osteopathy and chiropractic techniques, naprapathy is a holistic and integrative approach to restoring whole health. In fact, naprapathy often incorporates multiple, complimentary therapies, such as massage, nutritional counseling, electrical muscle stimulation and low-level laser therapy.

Naprapathy also targets vertebral subluxations, or physical abnormalities present that suggest a misalignment or injury of the spinal vertebrae. This analysis is made by a physical inspection of the musculoskeletal system, as well as visual observation. The practitioner will also conduct a lengthy interview with the client to help determine stress level and nutritional status as well. An imbalance along one or more of these lines may signal trouble within the musculoskeletal structure.

The naprapathy practitioner is particularly skilled in identifying restricted or stressed components of the fascial system, or connective tissue. It is believed that where constriction of muscles, ligaments, and tendons exists, there is impaired blood flow and nerve functioning. Naprapathy attempts to correct these blockages through hands-on manipulation and stretching of connective tissue. However, since this discipline embodies a holistic approach, the naprapathy practitioner is also concerned with their client’s emotional health. To that end, many practitioners are also trained in psychotherapy and even hypnotherapy.

So, now we know!

We also know that the manual therapies tested here cause adverse effects in about half of all patients. This figure ties in nicely with the ones we had regarding chiropractic: ~ 50% of all patients suffer mild to moderate adverse effects after chiropractic spinal manipulation which usually last 2-3 days and can be strong enough to affect their quality of life. In addition very serious complications have been noted which luckily seem to be much rarer events.

In my view, this raises the question: DO THESE TREATMENTS GENERATE MORE GOOD THAN HARM? I fail to see any good evidence to suggest that they do – but, of course, I would be more than happy to revise this verdict, provided someone shows me the evidence.

Do you think that chiropractic is effective for asthma? I don’t – in fact, I know it isn’t because, in 2009, I have published a systematic review of the available RCTs which showed quite clearly that the best evidence suggested chiropractic was ineffective for that condition.

But this is clearly not true, might some enthusiasts reply. What is more, they can even refer to a 2010 systematic review which indicates that chiropractic is effective; its conclusions speak a very clear language: …the eight retrieved studies indicated that chiropractic care showed improvements in subjective measures and, to a lesser degree objective measures… How on earth can this be?

I would not be surprised, if chiropractors claimed the discrepancy is due to the fact that Prof Ernst is biased. Others might point out that the more recent review includes more studies and thus ought to be more reliable. The newer review does, in fact, have about twice the number of studies than mine.

How come? Were plenty of new RCTs published during the 12 months that lay between the two publications? The answer is NO. But why then the discrepant conclusions?

The answer is much less puzzling than you might think. The ‘alchemists of alternative medicine’ regularly succeed in smuggling non-evidence into such reviews in order to beautify the overall picture and confirm their wishful thinking. The case of chiropractic for asthma does by no means stand alone, but it is a classic example of how we are being misled by charlatans.

Anyone who reads the full text of the two reviews mentioned above will find that they do, in fact, include exactly the same amount of RCTs. The reason why they arrive at different conclusions is simple: the enthusiasts’ review added NON-EVIDENCE to the existing RCTs. To be precise, the authors included one case series, one case study, one survey, two randomized controlled trials (RCTs), one randomized patient and observer blinded cross-over trial, one single blind cross study design, and one self-reported impairment questionnaire.

Now, there is nothing wrong with case reports, case series, or surveys – except THEY TELL US NOTHING ABOUT EFFECTIVENESS. I would bet my last shirt that the authors know all of that; yet they make fairly firm and positive conclusions about effectiveness. As the RCT-results collectively happen to be negative, they even pretend that case reports etc. outweigh the findings of RCTs.

And why do they do that? Because they are interested in the truth, or because they don’t mind using alchemy in order to mislead us? Your guess is as good as mine.

The efficacy or effectiveness of medical interventions is, of course, best tested in clinical trials. The principle of a clinical trial is fairly simple: typically, a group of patients is divided (preferably at random) into two subgroups, one (the ‘verum’ group) is treated with the experimental treatment and the other (the ‘control’ group) with another option (often a placebo), and the eventual outcomes of the two groups is compared. If done well, such studies are able to exclude biases and confounding factors such that their findings allow causal inference. In other words, they can tell us whether an outcome was caused by the intervention per se or by some other factor such as the natural history of the disease, regression towards the mean etc.

A clinical trial is a research tool for testing hypotheses; strictly speaking, it tests the ‘null-hypothesis’: “the experimental treatment generates the same outcomes as the treatment of the control group”. If the trial shows no difference between the outcomes of the two groups, the null-hypothesis is confirmed. In this case, we commonly speak of a negative result. If the experimental treatment was better than the control treatment, the null-hypothesis is rejected, and we commonly speak of a positive result. In other words, clinical trials can only generate positive or negative results, because the null-hypothesis must either be confirmed or rejected – there are no grey tones between the black of a negative and the white of a positive study.

For enthusiasts of alternative medicine, this can create a dilemma, particularly if there are lots of published studies with negative results. In this case, the totality of the available trial evidence is negative which means the treatment in question cannot be characterised as effective. It goes without saying that such an overall conclusion rubs the proponents of that therapy the wrong way. Consequently, they might look for ways to avoid this scenario.

One fairly obvious way of achieving this aim is to simply re-categorise the results. What, if we invented a new category? What, if we called some of the negative studies by a different name? What about NON-CONCLUSIVE?

That would be brilliant, wouldn’t it. We might end up with a simple statistic where the majority of the evidence is, after all, positive. And this, of course, would give the impression that the ineffective treatment in question is effective!

How exactly do we do this? We continue to call positive studies POSITIVE; we then call studies where the experimental treatment generated worst results than the control treatment (usually a placebo) NEGATIVE; and finally we call those studies where the experimental treatment created outcomes which were not different from placebo NON-CONCLUSIVE.

In the realm of alternative medicine, this ‘non-conclusive result’ method has recently become incredibly popular . Take homeopathy, for instance. The Faculty of Homeopathy proudly claim the following about clinical trials of homeopathy: Up to the end of 2011, there have been 164 peer-reviewed papers reporting randomised controlled trials (RCTs) in homeopathy. This represents research in 89 different medical conditions. Of those 164 RCT papers, 71 (43%) were positive, 9 (6%) negative and 80 (49%) non-conclusive.

This misleading nonsense was, of course, warmly received by homeopaths. The British Homeopathic Association, like many other organisations and individuals with an axe to grind lapped up the message and promptly repeated it: The body of evidence that exists shows that much more investigation is required – 43% of all the randomised controlled trials carried out have been positive, 6% negative and 49% inconclusive.

Let’s be clear what has happened here: the true percentage figures seem to show that 43% of studies (mostly of poor quality) suggest a positive result for homeopathy, while 57% of them (on average the ones of better quality) were negative. In other words, the majority of this evidence is negative. If we conducted a proper systematic review of this body of evidence, we would, of course, have to account for the quality of each study, and in this case we would have to conclude that homeopathy is not supported by sound evidence of effectiveness.

The little trick of applying the ‘NON-CONCLUSIVE’ method has thus turned this overall result upside down: black has become white! No wonder that it is so popular with proponents of all sorts of bogus treatments.

Whenever a new trial of an alternative intervention emerges which fails to confirm the wishful thinking of the proponents of that therapy, the world of alternative medicine is in turmoil. What can be done about yet another piece of unfavourable evidence? The easiest solution would be to ignore it, of course - and this is precisely what is often tried. But this tactic usually proves to be unsatisfactory; it does not neutralise the new evidence, and each time someone brings it up, one has to stick one’s head back into the sand. Rather than denying its existence, it would be preferable to have a tool which invalidates the study in question once and for all.

The ‘fatal flaw’ solution is simpler than anticipated! Alternative treatments are ‘very special’, and this notion must be emphasised, blown up beyond all proportions and used cleverly to discredit studies with unfavourable outcomes: the trick is simply to claim that studies with unfavourable results have a ‘fatal flaw’ in the way the alternative treatment was applied. As only the experts in the ‘very special’ treatment in question are able to judge the adequacy of their therapy, nobody is allowed to doubt their verdict.

Take acupuncture, for instance; it is an ancient ‘art’ which only the very best will ever master – at least that is what we are being told. So, all the proponents need to do in order to invalidate a trial, is read the methods section of the paper in full detail and state ‘ex cathedra’ that the way acupuncture was done in this particular study is completely ridiculous. The wrong points were stimulated, or the right points were stimulated but not long enough [or too long], or the needling was too deep [or too shallow], or the type of stimulus employed was not as recommended by TCM experts, or the contra-indications were not observed etc. etc.

As nobody can tell a correct acupuncture from an incorrect one, this ‘fatal flaw’ method is fairly fool-proof. It is also ever so simple: acupuncture-fans do not necessarily study hard to find the ‘fatal flaw’, they only have to look at the result of a study – if it was favourable, the treatment was obviously done perfectly by highly experienced experts; if it was unfavourable, the therapists clearly must have been morons who picked up their acupuncture skills in a single weekend course. The reasons for this judgement can always be found or, if all else fails, invented.

And the end-result of the ‘fatal flaw’ method is most satisfactory; what is more, it can be applied to all alternative therapies – homeopathy, herbal medicine, reflexology, Reiki healing, colonic irrigation…the method works for all of them! What is even more, the ‘fatal flaw’ method is adaptable to other aspects of scientific investigations such that it fits every conceivable circumstance.

An article documenting the ‘fatal flaw’ has to be published, of course - but this is no problem! There are dozens of dodgy alternative medicine journals which are only too keen to print even the most far-fetched nonsense as long as it promotes alternative medicine in some way. Once this paper is published, the proponents of the therapy in question have a comfortable default position to rely on each time someone cites the unfavourable study: “WHAT NOT THAT STUDY AGAIN! THE TREATMENT HAS BEEN SHOWN TO BE ALL WRONG. NOBODY CAN EXPECT GOOD RESULTS FROM A THERAPY THAT WAS NOT CORRECTLY ADMINISTERED. IF YOU DON’T HAVE BETTER STUDIES TO SUPPORT YOUR ARGUMENTS, YOU BETTER SHUT UP.”

There might, in fact, be better studies – but chances are that the ‘other side’ has already documented a ‘fatal flaw’ in them too.

There is not a discussion about homeopathy where an apologist would eventually state: HOMEOPATHY CANNOT BE A PLACEBO, BECAUSE IT WORKS IN ANIMALS!!! Those who are not well-versed in this subject tend to be impressed, and the argument has won many consumers over to the dark side, I am sure. But is it really correct?

The short answer to this question is NO.

Pavlov discovered the phenomenon of ‘conditioning’ in animals, and ‘conditioning’ is considered to be a major part of the placebo-response. So, depending on the circumstances, animals do respond to placebo (my dog, for instance, used to go into a distinct depressive mood when he saw me packing a suitcase).

Then there is the fact that the animal’s response might be less important than the owner’s reaction to homeopathic treatment. This is particularly important with pets, of course. Homeopathy-believing pet owners might over-interpret the pet’s response and report that the homeopathic remedy has worked wonders when, in fact, it has made no difference.

Finally, there may be some situations where neither of the above two phenomena can play a decisive role. Homeopaths like to cite studies where entire herds of cows were treated homeopathically to prevent mastitis, a common problem in milk-cows. It is unlikely that conditioning or wishful thinking of the owner are decisive in such a study. Let’s see whether homeopathy-promoters will also be fond of this new study of exactly this subject.

New Zealand vets compared clinical and bacteriological cure rates of clinical mastitis following treatment with either antimicrobials or homeopathic preparations. They used 7 spring-calving herds from the Waikato region of New Zealand to source cases of clinical mastitis (n=263 glands) during the first 90 days following calving. Duplicate milk samples were collected for bacteriology from each clinically infected gland at diagnosis and 25 (SD 5.3) days after the initial treatment. Affected glands were treated with either an antimicrobial formulation or a homeopathic remedy. Generalised linear models with binomial error distribution and logit link were used to analyse the proportion of cows that presented clinical treatment cures and the proportion of glands that were classified as bacteriological cures, based on initial and post-treatment milk samples.

The results show that the mean cumulative incidence of clinical mastitis was 7% (range 2-13% across herds) of cows. Streptococcus uberis was the most common pathogen isolated from culture-positive samples from affected glands (140/209; 67%). The clinical cure rate was higher for cows treated with antimicrobials (107/113; 95%) than for cows treated with homeopathic remedies (72/114; 63%) (p<0.001) based on the observance of clinical signs following initial treatment. Across all pathogen types bacteriological cure rate at gland level was higher for those cows treated with antimicrobials (75/102; 74%) than for those treated with a homeopathic preparation (39/107; 36%) (p<0.001).

The authors conclude that homeopathic remedies had significantly lower clinical and bacteriological cure rates compared with antimicrobials when used to treat post-calving clinical mastitis where S. uberis was the most common pathogen. The proportion of cows that needed retreatment was significantly higher for the homeopathic treated cows. This, combined with lower bacteriological cure rates, has implications for duration of infection, individual cow somatic cell count, costs associated with treatment and animal welfare.

Yes, I know, this is just one single study, and we need to consider the totality of the reliable evidence. Currently, there are 203 clinical trials of homeopathic treatments of animals; and they are being reviewed at the very moment (unfortunately by a team that is not known for its objective stance on homeopathy). So, we will have to wait and see. When, in 1999, A. Vickers reviewed all per-clinical studies, including those on animals, he concluded that there is a lack of independent replication of any pre-clinical research in homoeopathy. In the few instances where a research team has set out to replicate the work of another, either the results were negative or the methodology was questionable.

All this is to say that, until truly convincing evidence to the contrary is available, the homeopaths’ argument ‘HOMEOPATHY CANNOT BE A PLACEBO, BECAUSE IT WORKS IN ANIMALS!!!’ is, in my view, as weak as the dilution of their remedies.

I am constantly on the look-out for good studies of alternative medicine, particularly those that yield positive findings. The trouble is that there aren’t many of those; studies tend to be either good or positive. Could this one be an exception?

The aim of this brand-new trial was to determine, if  dietary supplements of glucosamine and/or chondroitin, result in reduced joint space narrowing (JSN) and pain in patients with knee osteoarthritis. It was designed as a  double-blind randomised placebo-controlled clinical trial with 2-year follow-up. 605 participants, aged 45–75 years, reporting chronic knee pain and with evidence of medial tibio-femoral compartment narrowing (but retaining >2 mm medial joint space width) were randomised to once daily: glucosamine sulfate 1500 mg (n=152), chondroitin sulfate 800 mg (n=151), both of these dietary  supplements (n=151) or placebo capsules (n=151). JSN (mm) over 2 years was measured from digitised knee radiographs. Maximum knee pain (0–10) was self-reported in a participant diary for 7 days every 2 months over 1 year.

The results indicate that, after adjusting for factors associated with structural disease progression (gender, body mass index (BMI), baseline structural disease severity and Heberden’s nodes), allocation to the dietary supplement combination (glucosamine–chondroitin) resulted in a statistically significant (p=0.046) reduction of 2-year JSN compared to placebo: mean difference 0.10 mm (95% CI 0.002 mm 0.20 mm); no significant structural effect for the single treatment allocations was detected. All 4 groups demonstrated reduced knee pain over the first year, but no significant between-group differences (p=0.93) were detected. 34 (6%) participants reported possibly-related adverse medical events over the 2-year follow-up period.

The authors drew the following conclusions: allocation to the glucosamine–chondroitin combination resulted in a statistically significant reduction in JSN at 2 years. While all allocation groups demonstrated reduced knee pain over the study period, none of the treatment allocation groups demonstrated significant symptomatic benefit above placebo.

This study has many strengths: it addresses a relevant research question, has a sufficiently large sample size, includes a long follow-up, and is well reported. So, it is a good study of an alternative therapy that is used by many patients. But did it really produce a positive result, i.e. findings which suggest that the tested treatments are effective? The answer seems ‘yes and no’. The combined, regular intake of both supplements caused less joint space narrowing which is a good objective sign of reduced disease activity. However, this was not paralleled by a reduction in pain that was better than that on placebo.

So, if you are a fan of glucosamine/chondroitin supplements, you will be pleased with this study, but if you are not in favour of such medications or do not have the spare cash to afford the considerable costs, you might say: I told you, they are pretty useless!

There are dozens of observational studies of homeopathy which seem to suggest – at least to homeopaths – that homeopathic treatments generate health benefits. As these investigations lack a control group, their results can be all to easily invalidated by pointing out that factors like ‘regression towards the mean‘ (RTM, a statistical artefact caused by the phenomenon that a variable that is extreme on its first measurement tends to be closer to the average on its second measurement) might be the cause of the observed change. Thus the debate whether such observational data are reliable or not has been raging for decades. Now, German (pro-homeopathy) investigators have published a paper which potentially could resolve this dispute.

With this re-analysis of an observational study, the investigators wanted to evaluate whether the observed changes in previous cohort studies are due to RTM and to estimate RTM adjusted effects. SF-36 quality-of-life (QoL) data from a cohort of 2827 chronically diseased adults treated with homeopathy were reanalysed using a method described in 1991 by Mee and Chua’s. RTM adjusted effects, standardized by the respective standard deviation at baseline, were 0.12 (95% CI: 0.06-0.19, P < 0.001) in the mental and 0.25 (0.22-0.28, P < 0.001) in the physical summary score of the SF-36. Small-to-moderate effects were confirmed for most individual diagnoses in physical, but not in mental component scores. Under the assumption that the true population mean equals the mean of all actually diseased patients, RTM adjusted effects were confirmed for both scores in most diagnoses.

The authors reached the following conclusion: “In our paper we showed that the effects on quality of life observed in patients receiving homeopathic care in a usual care setting are small or moderate at maximum, but cannot be explained by RTM alone. Due to the uncontrolled study design they may, however, completely be due to nonspecific effects. All our analyses made a restrictive and conservative assumption, so the true treatment effects might be larger than shown.” 

Of course, the analysis heavily relies on the validity of Mee and Chua’s modified t-test. It requires the true mean in the target population to be known, a requirement that seldom can be fulfilled. The authors therefore took the SF-36 mean summary scores from the 1998 German health survey as proxies. I am not a statistician and therefore unable to tell how reliable this method might be (- if there is someone out there who can give us some guidance here, please post your comment).

In order to make sense of these data, we need to consider that, during the study period, about half of the patients admitted to have had additional visits to non-homeopathic doctors, and 27% also received conventional drugs. In addition, they would have benefitted from:

  • the benign history of the conditions they were suffering from,
  • a placebo-effect,
  • the care and attention they received
  • and all sorts of other non-specific effects.

So, considering these factors, what does this interesting re-analysis really tell us? My interpretation is as follows: the type of observational study that homeopaths are so fond of yields false-positive results. If we correct them – as the authors have done here for just one single factor, the RTM – the effect size gets significantly smaller. If we were able to correct them for some of the other factors mentioned above, the effect size would shrink more and more. And if we were able to correct them for all confounders, their results would almost certainly concur with those of rigorously controlled trials which demonstrate that homeopathic remedies are pure placebos.

I am quite sure that this interpretation is unpopular with homeopaths, but I am equally certain that it is correct.

Cancer patients are understandably desperate and leave no stone unturned to improve their prognosis. Thus they become easy prey of charlatans who claim that this or that alternative therapy will cure them or improve their outlook. One of the most popular alternative cancer therapies is mistletoe, a treatment dreamt up by Rudolf Steiner on the basis of the ‘like cures like’ principle: the mistletoe plant grows on a host tree like a cancer in the human body. One of many websites on this subject, for instance, states:

Mistletoe therapy

  • integrates with conventional cancer treatments
  • can be used for a wide range of cancers
  • may be started at any stage of the illness….

potential benefits…include:

  • Improved quality of life
  • generally feeling better
  • increased appetite and weight
  • less tired/more energy
  • reduced pain
  • better sleep pattern
  • felling more hopeful and motivated
  • reduced adverse effects from chemo and radiotherapy
  • reduced risk of cancer spread and recurrence
  • increased life expectancy.

Mistletoe extracts have been shown in studies to:

  • stimulate the immune system
  • cause cancer cell death
  • protect healthy cells against harmful effects of radiation and chemotherapy.

In fact, the debate about the efficacy of mistletoe either as a cancer cure, a supportive therapy, or a palliative measure is often less than rational and seems never-ending.

The latest contribution to this saga comes from US oncologists who published a phase I study of gemcitabine (GEM) and mistletoe in advanced solid cancers (ASC). The trial was aimed at evaluating: (1) safety, toxicity, and maximum tolerated dose (MTD), (2) absolute neutrophil count (ANC) recovery, (3) formation of mistletoe lectin antibodies (ML ab), (4) cytokine plasma concentrations, (5) clinical response, and (6) pharmacokinetics of GEM.

A total of 44 study participants were enrolled; 20 were treated in stage I (mistletoe dose escalation phase) and 24 in stage II (gemcitabine dose escalation phase). All patients had stage IV disease; the majority had received previous chemo-, hormonal, immunological, or radiation therapy, and 23% were chemotherapy-naïve.

Patients were treated with increasing doses of a mistletoe-extract (HELIXOR Apis (A), growing on fir trees) plus a fixed GEM dose in stage I, and with increasing doses of GEM plus a fixed dose of mistletoe in stage II. Response in stage IV ASC was assessed with descriptive statistics. Statistical analyses examined clinical response/survival and ANC recovery.

The results show that dose-limiting toxicities were neutropenia, thrombocytopenia, acute renal failure, and cellulitis, attributed to mistletoe. GEM 1380 mg/m2 and mistletoe 250 mg combined were the MTD. Of the 44 patients, 24 developed non-neutropenic fever and flu-like syndrome. GEM pharmacokinetics were unaffected by mistletoe. All patients developed ML3 IgG antibodies. ANC showed a trend to increase between baseline and cycle 2 in stage I dose escalation.

6% of patients showed a partial response, and 42% had stable disease. Of the 44 study participants, three died during the study, 10 participants requested to terminate the study, 23 participants progressed while on study, one terminated the study due to a dose limiting toxicity, 6 left due to complicating disease issues which may be tied to progression, and one voluntarily withdrew.

An attempt was made to follow study subjects once they terminated study treatment until death. At the last attempt to contact former participants, three were still alive and five others were lost to follow-up. The median time to death of any cause was approximately 200 days. Compliance with mistletoe injections was high.

The authors explain that a partial response rate of 6% is comparable to what would be expected from single agent gemcitabine in this population of patients with advanced, mostly heavily pretreated carcinomas. The median survival from study enrollment of about 200 days is within the range of what would be expected from single agent gemcitabine.

The authors concluded that GEM plus mistletoe is well tolerated. No botanical/drug interactions were observed. Clinical response  is similar to GEM alone.

These results are hardly encouraging but they originate from just one (not particularly rigorous) study and might thus not be reliable. So, what does the totality of the reliable evidence tell us? Our 2003 systematic review of 10 RCTs found that none of the methodologically stronger trials exhibited efficacy in terms of quality of life, survival or other outcome measures. Rigorous trials of mistletoe extracts fail to demonstrate efficacy of this therapy.

Will this stop the highly lucrative trade in mistletoe extracts? will it prevent desperate cancer patients being misled about the value of mistletoe treatment? I fear not.

Times of celebration are often also times of over-indulgence and subsequent suffering. Who would not know, for instance, how a hangover can spoil one’s pleasure at the start of a new year? But where is the research that addresses this problem? Scientists seem to be cynically devoid of sympathy for the hangover-victim – well, not all scientists.

During the course of my research-career, I must have conducted well over 60 clinical trials, but none was remotely as entertaining as the one my Exeter-team did several years ago to test whether an artichoke extract is effective in preventing the signs and symptoms of alcohol-induced hangover.

We recruited healthy adult volunteers from our own ranks to participate in a randomized double-blind crossover trial. Participants received either 3 capsules of commercially available standardized artichoke extract or indistinguishable, inert placebo capsules immediately before and after alcohol exposure. After a 1-week washout period the volunteers received the opposite treatment. Each participant predefined the type and amount of alcoholic beverage that would give him/her a hangover and ate the same meal before commencing alcohol consumption on the two study days. The primary outcome measure was the difference in hangover severity scores between the artichoke extract and placebo interventions. Secondary outcome measures were differences between the interventions in scores using a mood profile questionnaire and cognitive performance tests administered 1 hour before and 10 hours after alcohol exposure.

The mean number of alcohol units consumed per person during treatment with artichoke extract and placebo were  10.7 and 10.5 respectively, equivalent to 1.2 g of alcohol per kilogram body weight. The volume of non-alcoholic drink consumed and the duration of sleep after the binge were similar during the artichoke extract and placebo interventions. The hangovers we experienced the mornings after our alcohol exposure were monumental but unaffected by the treatments. None of the outcome measures differed significantly between interventions. Adverse events of the treatment were rare and were mild and transient. Our results therefore suggested that artichoke extract is not effective in preventing the signs and symptoms of alcohol-induced hangover.

While it was great fun to obtain ethic’s approval and run this trial, the results of our two binges in the name of science were, of course, a disappointment. As diligent researchers we felt we had to do a little more for the poor victims of over-indulgence.

We thus decided to conduct a systematic review aimed at assessing the clinical evidence on the effectiveness of any medical intervention for preventing or treating alcohol hangover. We conducted systematic searches to identify all RCTs of any medical intervention for preventing or treating alcohol hangover. Fifteen potentially relevant trials were found. Seven publications failed to meet all inclusion criteria. Eight RCTs assessing 8 different interventions were reviewed. The agents tested were propranolol, tropisetron, tolfenamic acid, fructose or glucose as well as the dietary supplements Borago officinalis (borage), Cynara scolymus (artichoke), Opuntia ficus-indica (prickly pear), and a yeast based preparation. All studies were double blind. Significant intergroup differences for overall symptom scores and individual symptoms were reported only for tolfenamic acid, gamma linolenic acid from borage, and a yeast based preparation.

We concluded that the most effective way to avoid the symptoms of alcohol induced hangover is to practise abstinence or moderation.

WISE WORDS PERHAPS, BUT EASIER SAID THAN DONE, I’M SURE.

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