clinical trial

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The use of homeopathy to treat depression in peri- and postmenopausal women seems widespread, but there is a lack of clinical trials testing its efficacy. The aim of this new study was therefore to assess efficacy and safety of individualized homeopathic treatment versus placebo and fluoxetine versus placebo in peri- and postmenopausal women with moderate to severe depression.

A randomized, placebo-controlled, double-blind, double-dummy, superiority, three-arm trial with a 6 week follow-up study was conducted. The study was performed in a Mexican outpatient service of homeopathy. One hundred thirty-three peri- and postmenopausal women diagnosed with major depression according to DSM-IV (moderate to severe intensity) were included. The outcomes were:

  1. the change in the mean total score among groups on the 17-item Hamilton Rating Scale for Depression,
  2. the Beck Depression Inventory;
  3. the Greene Scale, after 6 weeks of treatment,
  4. response rates,
  5. remission rates,
  6. safety.

Efficacy data were analyzed in the intention-to-treat population (ANOVA with Bonferroni post-hoc test).

After a 6-week treatment, the results of homeopathic group showed more effectiveness than placebo in the Hamilton Scale. Response rate was 54.5% and remission rate was 15.9%. There was a significant difference between groups in response rate, but not in remission rate. The fluoxetine-placebo difference was 3.2 points. No differences were observed between groups in the Beck Depression Inventory. The results of the homeopathic group were superior to placebo regarding Greene Climacteric Scale (8.6 points). Fluoxetine was not different from placebo in the Greene Climacteric Scale.

The authors concluded that homeopathy and fluoxetine are effective and safe antidepressants for climacteric women. Homeopathy and fluoxetine were significantly different from placebo in response definition only. Homeopathy, but not fluoxetine, improves menopausal symptoms scored by Greene Climacteric Scale.

The article is interesting but highly confusing and poorly reported. The trial is small and short-term only. The way I see it, the finding that individualised homeopathy is better than a standard anti-depressant might be due to a range of phenomena:

  • residual bias; (for instance, it is conceivable that some patients were ‘de-blinded’ due to the well-known side-effects of the conventional anti-depressant);
  • inappropriate statistical analysis if the data;
  • chance;
  • fraud;
  • or the effectiveness of individualised homeopathy.

Even if the findings of this study turned out to be real, it would most certainly be premature to advise patients to opt for homeopathy. At the very minimum, we would need an independent replication of this study – and somehow I doubt that it would confirm the results of this Mexican trial.

Twenty years ago, I published a short article in the British Journal of Rheumatology. Its title was ALTERNATIVE MEDICINE, THE BABY AND THE BATH WATER. Reading it again today – especially in the light of the recent debate (with over 700 comments) on acupuncture – indicates to me that very little has since changed in the discussions about alternative medicine (AM). Does that mean we are going around in circles? Here is the (slightly abbreviated) article from 1995 for you to judge for yourself:

“Proponents of alternative medicine (AM) criticize the attempt of conducting RCTs because they view this is in analogy to ‘throwing out the baby with the bath water’. The argument usually goes as follows: the growing popularity of AM shows that individuals like it and, in some way, they benefit through using it. Therefore it is best to let them have it regardless of its objective effectiveness. Attempts to prove or disprove effectiveness may even be counterproductive. Should RCTs prove that a given intervention is not superior to a placebo, one might stop using it. This, in turn, would be to the disadvantage of the patient who, previous to rigorous research, has unquestionably been helped by the very remedy. Similar criticism merely states that AM is ‘so different, so subjective, so sensitive that it cannot be investigated in the same way as mainstream medicine’. Others see reasons to change the scientific (‘reductionist’) research paradigm into a broad ‘philosophical’ approach. Yet others reject the RCTs because they think that ‘this method assumes that every person has the same problems and there are similar causative factors’.

The example of acupuncture as a (popular) treatment for osteoarthritis, demonstrates the validity of such arguments and counter-arguments. A search of the world literature identified only two RCTs on the subject. When acupuncture was tested against no treatment, the experimental group of osteoarthritis sufferers reported a 23% decrease of pain, while the controls suffered a 12% increase. On the basis of this result, it might seem highly unethical to withhold acupuncture from pain-stricken patients—’if a patient feels better for whatever reason and there are no toxic side effects, then the patient should have the right to get help’.

But what about the placebo effect? It is notoriously difficult to find a placebo indistinguishable to acupuncture which would allow patient-blinded studies. Needling non-acupuncture points may be as close as one can get to an acceptable placebo. When patients with osteoarthritis were randomized into receiving either ‘real acupuncture or this type of sham acupuncture both sub-groups showed the same pain relief.

These findings (similar results have been published for other AMs) are compatible only with two explanations. Firstly acupuncture might be a powerful placebo. If this were true, we need to establish how safe acupuncture is (clearly it is not without potential harm); if the risk/benefit ratio is favourable and no specific, effective form of therapy exists one might still consider employing this form as a ‘placebo therapy’ for easing the pain of osteoarthritis sufferers. One would also feel motivated to research this powerful placebo and identify its characteristics or modalities with the aim of using the knowledge thus generated to help future patients.

Secondly, it could be the needling, regardless of acupuncture points and philosophy, that decreases pain. If this were true, we could henceforward use needling for pain relief—no special training in or equipment for acupuncture would be required, and costs would therefore be markedly reduced. In addition, this knowledge would lead us to further our understanding of basic mechanisms of pain reduction which, one day, might evolve into more effective analgesia. In any case the published research data, confusing as they often are, do not call for a change of paradigm; they only require more RCTs to solve the unanswered problems.

Conducting rigorous research is therefore by no means likely to ‘throw out the baby with the bath water’. The concept that such research could harm the patient is wrong and anti-scientific. To follow its implications would mean neglecting the ‘baby in the bath water’ until it suffers serious damage. To conduct proper research means attending the ‘baby’ and making sure that it is safe and well.

In the realm of homeopathy there is no shortage of irresponsible claims. I am therefore used to a lot – but this new proclamation takes the biscuit, particularly as it currently is being disseminated in various forms worldwide. It is so outrageously unethical that I decided to reproduce it here [in a slightly shortened version]:

“Homeopathy has given rise to a new hope to patients suffering from dreaded HIV, tuberculosis and the deadly blood disease Hemophilia. In a pioneering two-year long study, city-based homeopath Dr Rajesh Shah has developed a new medicine for AIDS patients, sourced from human immunodeficiency virus (HIV) itself.

The drug has been tested on humans for safety and efficacy and the results are encouraging, said Dr Shah. Larger studies with and without concomitant conventional ART (Antiretroviral therapy) can throw more light in future on the scope of this new medicine, he said. Dr Shah’s scientific paper for debate has just been published in Indian Journal of Research in Homeopathy…

The drug resulted in improvement of blood count (CD4 cells) of HIV patients, which is a very positive and hopeful sign, he said and expressed the hope that this will encourage an advanced research into the subject. Sourcing of medicines from various virus and bacteria has been a practise in the homeopathy stream long before the prevailing vaccines came into existence, said Dr Shah, who is also organising secretary of Global Homeopathy Foundation (GHF)…

Dr Shah, who has been campaigning for the integration of homeopathy and allopathic treatments, said this combination has proven to be useful for several challenging diseases. He teamed up with noted virologist Dr Abhay Chowdhury and his team at the premier Haffkine Institute and developed a drug sourced from TB germs of MDR-TB patients.”

So, where is the study? It is not on Medline, but I found it on the journal’s website. This is what the abstract tells us:

“Thirty-seven HIV-infected persons were registered for the trial, and ten participants were dropped out from the study, so the effect of HIV nosode 30C and 50C, was concluded on 27 participants under the trial.

Results: Out of 27 participants, 7 (25.93%) showed a sustained reduction in the viral load from 12 to 24 weeks. Similarly 9 participants (33.33%) showed an increase in the CD4+ count by 20% altogether in 12 th and 24 th week. Significant weight gain was observed at week 12 (P = 0.0206). 63% and 55% showed an overall increase in either appetite or weight. The viral load increased from baseline to 24 week through 12 week in which the increase was not statistically significant (P > 0.05). 52% (14 of 27) participants have shown either stability or improvement in CD4% at the end of 24 weeks, of which 37% participants have shown improvement (1.54-48.35%) in CD4+ count and 15% had stable CD4+ percentage count until week 24 week. 16 out of 27 participants had a decrease (1.8-46.43%) in CD8 count. None of the adverse events led to discontinuation of study.

Conclusion: The study results revealed improvement in immunological parameters, treatment satisfaction, reported by an increase in weight, relief in symptoms, and an improvement in health status, which opens up possibilities for future studies.”

In other words, the study had not even a control group. This means that the observed ‘effects’ are most likely just the normal fluctuations one would expect without any clinical significance whatsoever.

The homeopathic Ebola cure was bad enough, I thought, but, considering the global importance of AIDS, the homeopathic HIV treatment is clearly worse.

Reflexology is the treatment of reflex zones, usually on the sole of the feet, with manual massage and pressure. Reflexologists assume that certain zones correspond to certain organs, and that their treatment can influence the function of these organs. Thus reflexology is advocated for all sorts of conditions. Proponents are keen to point out that their approach has many advantages: it is pleasant (the patient feels well with the treatment and the therapist feels even better with the money), safe and cheap, particularly if the patient does the treatment herself.

Self-administered foot reflexology could be practical because it is easy to learn and not difficult to apply. But is it also effective? A recent systematic review evaluated the effectiveness of self-foot reflexology for symptom management.

Participants were healthy persons not diagnosed with a specific disease. The intervention was foot reflexology administered by participants, not by practitioners or healthcare providers. Studies with either between groups or within group comparison were included. The electronic literature searches utilized core databases (MEDLINE, EMBASE, Cochrane, and CINAHL Chinese (CNKI), Japanese (J-STAGE), and Korean databases (KoreaMed, KMbase, KISS, NDSL, KISTI, and OASIS)).

Three non-randomized trials and three before-and-after studies met the inclusion criteria. No RCTs were located. The results of these studies showed that self-administered foot reflexology resulted in significant improvement in subjective outcomes such as perceived stress, fatigue, and depression. However, there was no significant improvement in objective outcomes such as cortisol levels, blood pressure, and pulse rate. We did not find any randomized controlled trial.

The authors concluded that this study presents the effectiveness of self-administered foot reflexology for healthy persons’ psychological and physiological symptoms. While objective outcomes showed limited results, significant improvements were found in subjective outcomes. However, owing to the small number of studies and methodological flaws, there was insufficient evidence supporting the use of self-performed foot reflexology. Well-designed randomized controlled trials are needed to assess the effect of self-administered foot reflexology in healthy people.

I find this review quite interesting, but I would draw very different conclusions from its findings.

The studies that are available turned out to be of very poor methodological quality: they lack randomisation or rely on before/after comparisons. This means they are wide open to bias and false-positive results, particularly in regards to subjective outcome measures. Predictably, the findings of this review confirm that no effects are seen on objective endpoints. This is in perfect agreement with the hypothesis that reflexology is a pure placebo. Considering the biological implausibility of the underlying assumptions of reflexology, this makes sense.

My conclusions of this review would therefore be as follows: THE RESULTS ARE IN KEEPING WITH REFLEXOLOGY BEING A PURE PLACEBO.

Reiki healers believe they are able to channel ‘healing energy’ into patients’ body and thus enable them to get healthy. If Reiki were not such a popular treatment, one could brush such claims aside and think “let the lunatic fringe believe what they want”. But as Reiki so effectively undermines consumers’ sense of reality and rationality, I feel a responsibility to inform the public what Reiki truly amounts to.

This pilot study compared the effects of Reiki therapy with those of companionship on improvements in quality of life, mood, and symptom distress in cancer patients receiving chemotherapy. Thirty-six breast cancer patients received one of three treatments:

  1. usual care,
  2. Reiki + usual care,
  3. companionship + usual care.

First, data were collected from patients receiving usual care. Second, patients were randomized to either receive Reiki or a companionship during chemotherapy.

Questionnaires assessing quality of life, mood, symptom distress, and Reiki acceptability were completed at baseline and chemotherapy sessions 1, 2, and 4.

The results show that Reiki was rated relaxing with no side effects. Reiki and companionship groups both reported improvements in quality of life and mood that were greater than those seen in the usual care group.

The authors concluded that interventions during chemotherapy, such as Reiki or companionship, are feasible, acceptable, and may reduce side effects.

Yet another example of utterly bizarre conclusions from a fairly straight forward study and quite clear results. What they really demonstrate is the fact that Reiki is nothing more than a placebo; its perceived benefit relies entirely on non-specific effects. This view is also supported by our systematic review (its 1st author is a Reiki healer!): the evidence is insufficient to suggest that reiki is an effective treatment for any condition. Therefore the value of reiki remains unproven.

In other words, we do not need a trained Reiki master, nor the illusion of some mysterious ‘healing energy’. Simple companionship without woo or make-believe has exactly the same effect without undermining rationality. Or, to put it much more bluntly: REIKI IS NONSENSE ON STILTS.

Poor sleep quality during pregnancy is a frequent problem. Drug treatment can be problematic due to possible adverse effects for mother and embryo/foetus. Many pregnant women prefer natural treatments and assume that ‘natural’ equals harmless.

In the present study, the sedative effects of Bryophyllum pinnatum were investigated. This remedy is a phytotherapeutic medication predominantly used in anthroposophic medicine. In previous clinical studies on its tocolytic effect, B. pinnatum showed a promising risk/benefit ratio for mother and child. A recent analysis of the prescribing pattern for B. pinnatum in a network of anthroposophic physicians revealed sleep disorders as one of the most frequent diagnosis.

In this prospective, multi-centre, observational study, pregnant women suffering from sleep problems were treated with B. pinnatum (350mg tablets, 50% leaf press juice, Weleda AG, Arlesheim, dosage at physician’s consideration). Sleep quality, daily sleepiness and fatigue were assessed with the aid of standardised questionnaires, at the beginning of the treatment and after 2 weeks. Possible adverse effects perceived by the patients during the treatment were recorded.

The results show that the number of wake-ups, as well as the subjective quality of sleep was significantly improved at the end of the treatment with B. pinnatum. The Epworth Sleeping Scale decreased, indicating a reduction in tiredness during the day. There was, however, no evidence for a prolongation of the sleep duration, reduction in the time to fall asleep, as well as change in the Fatigue Severity Scale after B. pinnatum. No serious adverse drug reactions were detected.

From these data, the authors concluded that B. pinnatum is a suitable treatment of sleep problems in pregnancy. The data of this study encourage further clinical investigations on the use of B. pinnatum in sleep disorders.

Clinical trials of anthroposophic remedies, i.e. remedies which are based on the school of medicine founded by Rudolf Steiner, are very rare. Therefore this trial could be important.

B. pinnatum is a plant used in traditional Tai medicine against hypertension, and to some extend this makes sense: it contains cardiac glycosides which might help lowering elevated blood pressure. The reason for its use as a hypnotic, however, is not clear.

So, is B pinnatum really a ‘suitable treatment of sleep problems in pregnancy’? I doubt it for the following reasons:

  • the effects documented in this study are far from convincing,
  • we would need much more solid data to issue such a general recommendation,
  • cardiac glycosides can cause very serious adverse effects,
  • the sample size of the study is at least one dimension too small for assuming that it is safe,
  • we know nothing about its potential to cause harm to the foetus.

Personally, I find it irresponsible to draw conclusions such as the ones above on the basis of data which are flimsy to the extreme. I ask myself, to what extend wishful thinking might be a regrettable characteristic for the entire field of anthroposophic medicine.

Highly diluted homeopathic remedies are pure placebos; at least this is what sceptics have been saying for about 200 years. This assumption is based on the fact that homeopathy’s plausibility is close to zero and that the totality of the reliable evidence fails to demonstrate that it works beyond placebo for any condition.

But, if this is true,  why do so many patients swear by homeopathy and experience benefit from it? This question has been answered many times: THE BENEFIT IS NOT DUE TO THE REMEDY BUT TO NON-SPECIFIC EFFECTS OF THE CONSULTATION.

More confirmation for this conclusion comes from an unexpected source.

Indian homeopaths recently published a trial of individualized homeopathy in osteoarthritis. To be more precise, it was a prospective, parallel-arm, double-blind, randomized, placebo-controlled pilot study which was conducted from January to October 2014 involving 60 patients (homeopathy, n = 30; placebo, n = 30). All patients were suffering from acute painful episodes of knee osteoarthritis and visiting the outpatient clinic of Mahesh Bhattacharyya Homeopathic Medical College and Hospital, West Bengal, India.

The results show statistically significant reduction in 3 visual analogue scales (measuring pain, stiffness, and loss of function) and Osteoarthritis Research Society International scores in both groups over 2 weeks (P < .05). However, group differences were not significant (P > .05).

The authors conclude that, overall, homeopathy did not appear to be superior to placebo; still, further rigorous evaluation in this design involving a larger sample size seems feasible in future.

Considering what I wrote above, I would alter these conclusion to something much more reasonable: further studies of homeopathy are certainly feasible. However, they are neither necessary nor desirable.


Homeopathy has many critics who claim that there is no good evidence for this type of therapy. Homeopaths invariably find this most unfair and point to a plethora of studies that show an effect. They are, of course, correct! There are plenty of trials that suggest that homeopathic remedies do work. The question, however, is HOW RELIABLE ARE THESE STUDIES?

Here is a brand new one which might stand for dozens of others.

In this study, homeopaths treated 50 multimorbid patients with homeopathic remedies identifies by a method called ‘polarity analysis’ (PA) and prospectively followed them over one year (PA enables homeopaths to calculate a relative healing probability, based on Boenninghausen’s grading of polar symptoms).

The 43 patients (86%) who completed the observation period experienced an average improvement of 91% in their initial symptoms. Six patients dropped out, and one did not achieve an improvement of 80%, and was therefore also counted as a treatment failure. The cost of homeopathic treatment was 41% of projected equivalent conventional treatment.

Good news then for enthusiasts of homeopathy? 91% improvement!

Yet, I am afraid that critics might not be bowled over. They might smell a whiff of selection bias, lament the lack of a control group or regret the absence of objective outcome measures. But I was prepared to go as far as stating that such results might be quite interesting… until I read the authors’ conclusions that is:

Polarity Analysis is an effective method for treating multimorbidity. The multitude of symptoms does not prevent the method from achieving good results. Homeopathy may be capable of taking over a considerable proportion of the treatment of multimorbid patients, at lower costs than conventional medicine.

Virtually nothing in these conclusions is based on the data provided. They are pure extrapolation and wild assumptions. Two questions seem to emerge from this:

  1. How on earth can we take this and so many other articles on homeopathy seriously?
  2. When does this sort of article cross the line between wishful thinking and scientific misconduct?

As promised, I will try with this post to explain my reservations regarding the new meta-analysis suggesting that individualised homeopathic remedies are superior to placebos. Before I start, however, I want to thank all those who have commented on various issues; it is well worth reading the numerous and diverse comments.

To remind us of the actual meta-analysis, it might be useful to re-publish its abstract (the full article is also available online):


A rigorous and focused systematic review and meta-analysis of randomised controlled trials (RCTs) of individualised homeopathic treatment has not previously been undertaken. We tested the hypothesis that the outcome of an individualised homeopathic treatment approach using homeopathic medicines is distinguishable from that of placebos.


The review’s methods, including literature search strategy, data extraction, assessment of risk of bias and statistical analysis, were strictly protocol-based. Judgment in seven assessment domains enabled a trial’s risk of bias to be designated as low, unclear or high. A trial was judged to comprise ‘reliable evidence’ if its risk of bias was low or was unclear in one specified domain. ‘Effect size’ was reported as odds ratio (OR), with arithmetic transformation for continuous data carried out as required; OR > 1 signified an effect favouring homeopathy.


Thirty-two eligible RCTs studied 24 different medical conditions in total. Twelve trials were classed ‘uncertain risk of bias’, three of which displayed relatively minor uncertainty and were designated reliable evidence; 20 trials were classed ‘high risk of bias’. Twenty-two trials had extractable data and were subjected to meta-analysis; OR = 1.53 (95% confidence interval (CI) 1.22 to 1.91). For the three trials with reliable evidence, sensitivity analysis revealed OR = 1.98 (95% CI 1.16 to 3.38).


Medicines prescribed in individualised homeopathy may have small, specific treatment effects. Findings are consistent with sub-group data available in a previous ‘global’ systematic review. The low or unclear overall quality of the evidence prompts caution in interpreting the findings. New high-quality RCT research is necessary to enable more decisive interpretation.

Since my team had published an RCTs of individualised homeopathy, it seems only natural that my interest focussed on why the study (even though identified by Mathie et al) had not been included in the meta-analysis. Our study had provided no evidence that adjunctive homeopathic remedies, as prescribed by experienced homeopathic practitioners, are superior to placebo in improving the quality of life of children with mild to moderate asthma in addition to conventional treatment in primary care.

I was convinced that this trial had been rigorous and thus puzzled why, despite receiving ‘full marks’ from the reviewers, they had not included it in their meta-analysis. I thus wrote to Mathie, the lead author of the meta-analysis, and he explained: For your trial (White et al. 2003), under domain V of assessment, we were unable to extract data for meta-analysis, and so it was attributed high risk of bias, as specified by the Cochrane judgmental criteria. Our designated main outcome was the CAQ, for which we needed to know (or could at least estimate) a mean and SD for both the baseline and the end-point of the study. Since your paper reported only the change from baseline in Table 3 or in the main text, it is not possible to derive the necessary end-point for analysis.

It took a while and several further emails until I understood: our study did report both the primary (Table 2 quality of life) and secondary outcome measure (Table 3 severity of symptoms). The primary outcome measure was reported in full detail such that a meta-analysis would have been possible. The secondary outcome measure was also reported but not in full detail, and the data provided by us would not lend themselves to meta-analyses. By electing not our primary but our secondary outcome measure for their meta-analysis, Mathie et al were able to claim that they were unable to use our study and reject it for their meta-analysis.

Why did they do that?

The answer is simple: in their methods section, they specify that they used outcome measures “based on a pre-specified hierarchical list in order of greatest to least importance, recommended by the WHO“. This, I would argue is deeply flawed: the most important outcome measure of a study is usually the one for which the study was designed, not the one that some guys at the WHO feel might be important (incidentally, the WHO list was never meant to be applied to meta-analyses in that way).

By following rigidly their published protocol, the authors of the meta-analysis managed to exclude our negative trial. Thus they did everything right – or did they?

Well, I think they committed several serious mistakes.

  • Firstly, they wrote the protocol, which forced them to exclude our study. Following a protocol is not a virtue in itself; if the protocol is nonsensical it even is the opposite. Had they proceeded as is normal in such cases and used our primary outcome measure in their meta-analyses, it is most likely that their overall results would not have been in favour of homeopathy.
  • Secondly, they awarded our study a malus point for the criterium ‘selective outcome reporting’. This is clearly a wrong decision: we did report the severity-outcome, albeit not in sufficient detail for their meta-analysis. Had they not committed this misjudgment, our RCT would have been the only one with an ‘A’ rating. This would have very clearly highlighted the nonsense of excluding the best-rated trial from meta-analysis.

There are several other oddities as well. For instance, Mathie et al judge our study to be NOT free of vested interest. I asked Mathie why they had done this and was told it is because we accepted free trial medication from a homeopathic pharmacy. I would argue that my team was far less plagued by vested interest than the authors of their three best (and of course positive) trials who, as I happen to know, are consultants for homeopathic manufacturers.

And all of this is just in relation to our own study. Norbert Aust has uncovered similar irregularities with other trials and I take the liberty of quoting his comments posted previously again here:

I have reason to believe that this review and metaanalysis in biased in favor of homeopathy. To check this, I compared two studies (1) Jacobs 1994 about the treatment of childhood diarrhea in Nicaragua, (2) Walach 1997 about homeopathic threatment of headaches. The Jacobs study is one of the three that provided ‘reliable evidence’, Walach’s study earned a poor C2.2 rating and was not included in the meta-analyses. Jacobs’ results were in favour of homeopathy, Walach’s not.

For the domains where the rating of Walach’s study was less than that of the Jacobs study, please find citations from the original studies or my short summaries for the point in question.

Domain I: Sequence generation:
“The remedy selected was then mailed to a notary public who held a stock of placebos. The notary threw a dice and mailed either the homeopathic remedy or an appropriate placebo. The notary was provided with a blank randomisation list.”
Rating: UNCLEAR (Medium risk of bias)

“For each of these medications, there was a box of tubes in sequentially numbered order which had been previously randomized into treatment or control medication using a random numbers table in blocks of four”
Rating: YES (Low risk of bias)

Domain IIIb: Blinding of outcome assessor
“The notary was provided with a blank randomization list which was an absolutely unique document. It was only handed out after the biometrician (WG) had deposited all coded original data as a printout at the notary’s office. (…) Data entry was performed blindly by personnel not involved in the study. ”
Rating: UNCLEAR (Medium risk of bias)

“All statistical analyses were done before breaking the randomisation code, using the program …”
Rating: YES (Low risk of bias)

Domain V: Selective outcome reporting

Study protocol was published in 1991 prior to enrollment of participants, all primary outcome variables were reported with respect to all participants and the endpoints.
Rating: NO (high risk of bias)

No prior publication of protocol, but a pilot study exists. However this was published in 1993 only after the trial was performed in 1991. Primary outcome defined (duration of diarrhea), reported but table and graph do not match, secondary outcome (number of unformed stools on day 3) seems defined post hoc, for this is the only one point in time, this outcome yielded a significant result.
Rating: YES (low risk of bias)

Domain VI: Other sources of bias:

Rating: NO (high risk of bias), no details given

Imbalance of group properties (size, weight and age of children), that might have some impact on course of disease, high impact of parallel therapy (rehydration) by far exceeding effect size of homeopathic treatment
Rating: YES (low risk of bias), no details given

In a nutshell: I fail to see the basis for the different ratings in the studies themselves. I assume bias of the authors of the review.


So, what about the question posed in the title of this article? The meta-analysis is clearly not a ‘proof of concept’. But is it proof for misconduct? I asked Mathie and he answered as follows: No, your statement does not reflect the situation at all. As for each and every paper, we selected the main outcome measure for your trial using the objective WHO classification approach (in which quality of life is clearly of lower rank than severity). This is all clearly described in our prospective protocol. Under no circumstances did we approach this matter retrospectively, in the way you are implying. 

Some nasty sceptics might have assumed that the handful of rigorous studies with negative results were well-known to most researchers of homeopathy. In this situation, it would have been hugely tempting to write the protocol such that these studies must be excluded. I am thrilled to be told that the authors of the current new meta-analysis (who declared all sorts of vested interests at the end of the article) resisted this temptation.

As I have said on several occasions before: I am constantly on the lookout for new rigorous science that supports the claims of alternative medicine. Thus I was delighted to find a recent and potentially important article with some positive evidence.

Fish oil has been studied extensively in terms of its effects on health. We know that it has powerful anti-inflammatory properties and might thus benefit a wide range of conditions. However, the effects of FO in rheumatoid arthritis (RA) have not been examined in the context of contemporary treatment of early RA.

A new study has tried to fill this gap by examining the effects of high versus low dose FO in early RA employing a ‘treat-to-target’ protocol of combination disease-modifying anti-rheumatic drugs (DMARDs).

Patients with RA <12 months’ duration and who were DMARD-naïve were enrolled and randomised 2:1 to FO at a high dose or low dose (for masking). These groups, designated FO and control, were given 5.5 or 0.4 g/day, respectively, of the omega-3 fats, eicosapentaenoic acid + docosahexaenoic acid. All patients received methotrexate (MTX), sulphasalazine and hydroxychloroquine, and DMARD doses were adjusted according to an algorithm taking disease activity and toxicity into account. DAS28-erythrocyte sedimentation rate, modified Health Assessment Questionnaire (mHAQ) and remission were assessed three monthly. The primary outcome measure was failure of triple DMARD therapy.

In the FO group, failure of triple DMARD therapy was lower (HR=0.28 (95% CI 0.12 to 0.63; p=0.002) unadjusted and 0.24 (95% CI 0.10 to 0.54; p=0.0006) following adjustment for smoking history, shared epitope and baseline anti–cyclic citrullinated peptide. The rate of first American College of Rheumatology (ACR) remission was significantly greater in the FO compared with the control group (HRs=2.17 (95% CI 1.07 to 4.42; p=0.03) unadjusted and 2.09 (95% CI 1.02 to 4.30; p=0.04) adjusted). There were no differences between groups in MTX dose, DAS28 or mHAQ scores, or adverse events.

The authors concluded that FO was associated with benefits additional to those achieved by combination ‘treat-to-target’ DMARDs with similar MTX use. These included reduced triple DMARD failure and a higher rate of ACR remission.

So here we have a dietary supplement that actually might generate more good than harm! There is a mountain of data of good research on the subject. We understand the mechanism of action and we have encouraging clinical evidence. Some people might still say that we do not need to take supplements in order to benefit from the health effects of FO, consuming fatty fish regularly might have the same effects. This is true, of course, but the amount of fish that one would need to eat every day would probably be too large for most people’s taste.

The drawback (from the perspective of alternative medicine) in all this is, of course, that some experts might deny that FO has much to do with alternative medicine. Again: what do we call alternative medicine that works? We call it MEDICINE! And perhaps FO is an excellent example of exactly that.

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