MD, PhD, FMedSci, FRSB, FRCP, FRCPEd

methodology

The new guidelines by the American College of Physicians entitled ‘Noninvasive Treatments for Acute, Subacute, and Chronic Low Back Pain: A Clinical Practice Guideline From the American College of Physicians’ have already been the subject of the previous post. Today, I want to have a closer look at a small section of these guidelines which, I think, is crucial. It is entitled ‘HARMS OF NONPHARMACOLOGIC THERAPIES’. I have taken the liberty of copying it below:

“Evidence on adverse events from the included RCTs and systematic reviews was limited, and the quality of evidence for all available harms data is low. Harms were poorly reported (if they were reported at all) for most of the interventions.

Low-quality evidence showed no reported harms or serious adverse events associated with tai chi, psychological interventions, multidisciplinary rehabilitation, ultrasound, acupuncture, lumbar support, or traction (9,95,150,170–174). Low-quality evidence showed that when harms were reported for exercise, they were often related to muscle soreness and increased pain, and no serious harms were reported. All reported harms associated with yoga were mild to moderate (119). Low-quality evidence showed that none of the RCTs reported any serious adverse events with massage, although 2 RCTs reported soreness during or after massage therapy (175,176). Adverse events associated with spinal manipulation included muscle soreness or transient increases in pain (134). There were few adverse events reported and no clear differences between MCE and controls. Transcutaneous electrical nerve stimulation was associated with an increased risk for skin site reaction but not serious adverse events (177). Two RCTs (178,179) showed an increased risk for skin flushing with heat compared with no heat or placebo, and no serious adverse events were reported. There were no data on cold therapy. Evidence was insufficient to determine harms of electrical muscle stimulation, LLLT, percutaneous electrical nerve stimulation, interferential therapy, short-wave diathermy, and taping.”

The first thing that strikes me is the brevity of the section. Surely, guidelines of this nature must include a full discussion of the risks of the treatments in question!

The second thing that is noteworthy is the fact that the authors confirm the fact I have been banging on about for years: clinical trials of alternative therapies far too often fail to mention adverse effects.  I have often pointed out that the failure to report adverse effects in clinical trials is an unacceptable violation of medical ethics. By contrast, the guideline authors seem not to feel strongly about this omission.

The third thing that is noteworthy is that the guidelines evaluate the harms of the treatments purely on the basis of the adverse effects reported in the clinical trials and systematic reviews included in their efficacy assessments. This is nonsensical for at least two reasons:

  1. The guideline authors themselves are aware that the trials very often fail to mention adverse effects.
  2. For any assessment of harm, one has to go far beyond the evidence of clinical trials, because trials tend to be too small to pick up rare adverse effects, and because they are always conducted under optimally controlled conditions where adverse effects are less likely to occur than in real life.

Together, these features of the assessment of harms explain why the guideline authors arrive at conclusions which are oddly misguided; I would even feel that they resemble a white-wash. Here are two of the most overt misjudgements:

  • no harms associated with acupuncture,
  • only trivial harm associated with spinal manipulations.

The best evidence we have today shows that acupuncture leads to mild adverse effects in about 10% of all cases and is also associated with very severe complications (e.g. pneumothorax, cardiac tamponade, infections, deaths) in an unknown number of patients. More details can be found for instance here, here, here and here.

And the best evidence available shows that spinal manipulation leads to moderately severe adverse effects in ~50% of all cases. In addition, we know of hundreds of cases of very severe complications resulting in stroke, permanent neurological deficits or deaths. More details can be found for instance here, here, here and here.

In the introduction, I stated that this small section of the guidelines is crucial.

Why?

The reason is simple: any responsible therapeutic decision has to be based not just on the efficacy of the treatment in question but on its risk/benefit balance. The evidence shows that the risks of some alternative therapies can be considerable, a fact that is almost totally neglected in the guidelines. Therefore, the recommendations of the new guidelines by the American College of Physicians entitled ‘Noninvasive Treatments for Acute, Subacute, and Chronic Low Back Pain: A Clinical Practice Guideline From the American College of Physicians’ are in several aspects not entirely correct and need to be reconsidered.

The BMJ has always been my favourite Medical journal. (Need any proof for this statement? A quick Medline search tells me that I have over 60 publications in the BMJ.) But occasionally, the BMJ also disappoints me a great deal.

One of the most significant disappointments was recently published under the heading of STATE OF THE ART REVIEW. A review that is ‘state of the art’ must fulfil certain criteria; foremost it should be informative, unbiased and correct. The paper I am discussing here has, I think, neither of these qualities. It is entitled ‘Management of chronic pain using complementary and integrative medicine’, and here is its abstract:

Complementary and integrative medicine (CIM) encompasses both Western-style medicine and complementary health approaches as a new combined approach to treat a variety of clinical conditions. Chronic pain is the leading indication for use of CIM, and about 33% of adults and 12% of children in the US have used it in this context. Although advances have been made in treatments for chronic pain, it remains inadequately controlled for many people. Adverse effects and complications of analgesic drugs, such as addiction, kidney failure, and gastrointestinal bleeding, also limit their use. CIM offers a multimodality treatment approach that can tackle the multidimensional nature of pain with fewer or no serious adverse effects. This review focuses on the use of CIM in three conditions with a high incidence of chronic pain: back pain, neck pain, and rheumatoid arthritis. It summarizes research on the mechanisms of action and clinical studies on the efficacy of commonly used CIM modalities such as acupuncture, mind-body system, dietary interventions and fasting, and herbal medicine and nutrients.

The full text of this article is such that I could take issue with almost every second statement in it. Obviously, this would be too long and too boring for this blog. So, to keep it crisp and entertaining, let me copy the (tongue in cheek) ‘letter to the editor’ some of us published in the BMJ as a response to the review:

“Alternative facts are fashionable in politics these days, so why not also in healthcare? The article by Chen and Michalsen on thebmj.com provides a handy set of five instructions for smuggling alternative facts into medicine.

1. Create your own terminology: the term ‘complementary and integrated medicine’ (CIM) is nonsensical. Integrated medicine (a hotly disputed field) already covers complementary and conventional medicine.

2. Pretend to be objective: Chen and Michalsen elaborate on the systematic searches they conducted. But they omit hundreds of sources which do not support their message, which cherry-picks only evidence for the efficacy of the treatments they promote.

3. Avoid negativity: they bypass any material that might challenge what they include. For instance, when discussing therapeutic risks, they omit the disturbing lack of post-marketing surveillance: the reason we lack information on adverse events. They even omit to mention the many fatalities caused by their ‘CIM’.

4. Create an impression of thoroughness: Chen and Michalsen cite a total of 225 references. This apparent scholarly attention to detail masks their misuse of many of they list. Reference 82, for example, is employed to back up the claim that “satisfaction was lowest among complementary medicine users with rheumatoid arthritis, vasculitis, or connective tissue diseases”. In fact, it shows nothing of the sort.

5. Back up your message with broad generalisations: Chen and Michalsen conclude that “Taken together, CIM has an increasing role in the management of chronic pain, but high quality research is needed”. The implication is that all the CIMs mentioned in their figure 1 are candidates for pain control – even discredited treatments such as homeopathy.

In our view, these authors render us a service: they demonstrate to the novice how alternative facts may be used in medicine.”

James May, Edzard Ernst, Nick Ross, on behalf of HealthWatch UK

END OF QUOTE

I am sure you have your own comments and opinions, and I encourage you to post them here or (better) submit them to the BMJ or (best) both.

Shiatsu is one of those alternative therapies where there is almost no research. Therefore, every new study is of interest, and I was delighted to find this new trial.

Italian researchers tested the efficacy and safety of combining shiatsu and amitriptyline to treat refractory primary headaches in a single-blind, randomized, pilot study. Subjects with a diagnosis of primary headache and who experienced lack of response to ≥2 different prophylactic drugs were randomized in a 1:1:1 ratio to receive one of the following treatments:

  1. shiatsu plus amitriptyline,
  2. shiatsu alone,
  3. amitriptyline alone

The treatment period lasted 3 months and the primary endpoint was the proportion of patients experiencing ≥50%-reduction in headache days. Secondary endpoints were days with headache per month, visual analogue scale, and number of pain killers taken per month.

After randomization, 37 subjects were allocated to shiatsu plus amitriptyline (n = 11), shiatsu alone (n = 13), and amitriptyline alone (n = 13). Randomization ensured well-balanced demographic and clinical characteristics at baseline.

The results show that all the three groups improved in terms of headache frequency, visual analogue scale score, and number of pain killers and there was no between-group difference in the primary endpoint. Shiatsu (alone or in combination) was superior to amitriptyline in reducing the number of pain killers taken per month. Seven (19%) subjects reported adverse events, all attributable to amitriptyline, while no side effects were related with shiatsu treatment.

The authors concluded that shiatsu is a safe and potentially useful alternative approach for refractory headache. However, there is no evidence of an additive or synergistic effect of combining shiatsu and amitriptyline. These findings are only preliminary and should be interpreted cautiously due to the small sample size of the population included in our study.

Yes, I would advocate great caution indeed!

The results could easily be said to demonstrate that shiatsu is NOT effective. There is NO difference between the groups when looking at the primary endpoint. This plus the lack of a placebo-group renders the findings uninterpretable:

  • If we take the comparison 2 versus 3, this might indicate efficacy of shiatsu.
  • If we take the comparison 1 versus 3, it would indicate the opposite.
  • If we finally take the comparison 1 versus 2, it would suggest that the drug was ineffective.

So, we can take our pick!

Moreover, I do object to the authors’ conclusion that “shiatsu is a safe”. For such a statement, we would need sample sizes that are about two dimensions greater that those of this study.

So, what might be an acceptable conclusion from this trial? I see only one that is in accordance with the design and the results of this study:

 

POORLY DESIGNED RESEARCH CANNOT LEAD TO ANY CONCLUSIONS ABOUT THERAPEUTIC EFFICACY OR SAFETY. IT IS A WASTE OF RESOURCES AND A VIOLATION OF RESEARCH ETHICAL.

On this blog, we have had (mostly unproductive) discussions with homeopath so often that sometimes they sound like a broken disk. I don’t want to add to this kerfuffle; what I hope to do today is to summarise  a certain line of argument which, from the homeopaths’ point of view, seems entirely logical. I do this in the form of a fictitious conversation between a scientist (S) and a classical homeopath (H). My aim is to make the reader understand homeopaths better so that, future debates might be better informed.

HERE WE GO:

S: I have studied the evidence from studies of homeopathy in some detail, and I have to tell you, it fails to show that homeopathy works.

H: This is not true! We have plenty of evidence to prove that patients get better after seeing a homeopath.

S: Yes, but this is not because of the remedy; it is due to non-specific effect like the empathetic consultation with a homeopath. If one controls for these factors in adequately designed trials, the result usually is negative.

I will re-phrase my claim: the evidence fails to show that highly diluted homeopathic remedies are more effective than placebos.

H: I disagree, there are positive studies as well.

S: Let’s not cherry pick. We must always consider the totality of the reliable evidence. We now have a meta-analysis published by homeopaths that demonstrates the ineffectiveness of homeopathy quite clearly.

H: This is because homeopathy was not used correctly in the primary trials. Homeopathy must be individualised for each unique patient; no two cases are alike! Remember: homeopathy is based on the principle that like cures like!!!

S: Are you saying that all other forms of using homeopathy are wrong?

H: They are certainly not adhering to what Hahnemann told us to do; therefore you cannot take their ineffectiveness as proof that homeopathy does not work.

S: This means that much, if not most of homeopathy as it is used today is to be condemned as fake.

H: I would not go that far, but it is definitely not the real thing; it does not obey the law of similars.

S: Let’s leave this to one side for the moment. If you insist on individualised homeopathy, I must tell you that this approach can also be tested in clinical trials.

H: I know; and there is a meta-analysis which proves that it is effective.

S: Not quite; it concluded that 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.

If you call this a proof of efficacy, I would have to disagree with you. The effect was tiny and at least two of the best studies relevant to the subject were left out. If anything, this paper is yet another proof that homeopathy is useless!

H: You simply don’t understand homeopathy enough to say that. I tried to tell you that the remedy must be carefully chosen to fit each unique patient. This is a very difficult task, and sometimes it is not successful – mainly because the homeopaths employed in clinical trials are not skilled enough to find it. This means that, in these studies, we will always have a certain failure rate which, in turn, is responsible for the small average effect size.

S: But these studies are always conducted by experienced homeopaths, and only the very best, most experienced homeopaths were chosen to cooperate in them. Your argument that the trials are negative because of the ineffectiveness of the homeopaths – rather than the ineffectiveness of homeopathy – is therefore nonsense.

H: This is what you say because you don’t understand homeopathy!

S: No, it is what you say because you don’t understand science. How else would you prove that your hypothesis is correct?

H: Simple! Just look at individual cases from the primary studies within this meta-analysis . You will see that there are always patients who did improve. These cases are the proof we need. The method of the RCT is only good for defining average effects; this is not what we should be looking at, and it is certainly not what homeopaths are interested in.

S: Are you saying that the method of the RCT is wrong?

H: It is not always wrong. Some RCTs of homeopathy are positive and do very clearly prove that homeopathy works. These are obviously the studies where homeopathy has been applied correctly. We have to make a meta-analysis of such trials, and you will see that the result turns out to be positive.

S: So, you claim that all the positive studies have used the correct method, while all the negative ones have used homeopathy incorrectly.

H: If you insist to put it like that, yes.

S: I see, you define a trial to have used homeopathy correctly by its result. Essentially you accept science only if it generates the outcome you like.

H: Yes, that sounds odd to you – because you don’t understand enough of homeopathy.

S: No, what you seem to insist on is nothing short of double standards. Or would you accept a drug company claiming: some patients did feel better after taking our new drug, and this is proof that it works?

H: You see, not understanding homeopathy leads to serious errors.

S: I give up.

The aim of this pragmatic study was “to investigate the effectiveness of acupuncture in addition to routine care in patients with allergic asthma compared to treatment with routine care alone.”

Patients with allergic asthma were included in a controlled trial and randomized to receive up to 15 acupuncture sessions over 3 months plus routine care, or to a control group receiving routine care alone. Patients who did not consent to randomization received acupuncture treatment for the first 3 months and were followed as a cohort. All trial patients were allowed to receive routine care in addition to study treatment. The primary endpoint was the asthma quality of life questionnaire (AQLQ, range: 1–7) at 3 months. Secondary endpoints included general health related to quality of life (Short-Form-36, SF-36, range 0–100). Outcome parameters were assessed at baseline and at 3 and 6 months.

A total of 1,445 patients were randomized and included in the analysis (184 patients randomized to acupuncture plus routine care and 173 to routine care alone, and 1,088 in the nonrandomized acupuncture plus routine care group). In the randomized part, acupuncture was associated with an improvement in the AQLQ score compared to the control group (difference acupuncture vs. control group 0.7 [95% confidence interval (CI) 0.5–1.0]) as well as in the physical component scale and the mental component scale of the SF-36 (physical: 2.5 [1.0–4.0]; mental 4.0 [2.1–6.0]) after 3 months. Treatment success was maintained throughout 6 months. Patients not consenting to randomization showed similar improvements as the randomized acupuncture group.

The authors concluded that in patients with allergic asthma, additional acupuncture treatment to routine care was associated with increased disease-specific and health-related quality of life compared to treatment with routine care alone.

We have been over this so many times (see for instance here, here and here) that I am almost a little embarrassed to explain it again: it is fairly easy to design an RCT such that it can only produce a positive result. The currently most popular way to achieve this aim in alternative medicine research is to do a ‘A+B versus B’ study, where A = the experimental treatment, and B = routine care. As A always amounts to more than nothing – in the above trial acupuncture would have placebo effects and the extra attention would also amount to something – A+B must always be more than B alone. The easiest way of thinking of this is to imagine that A and B are both finite amounts of money; everyone can understand that A+B must always be more than B!

Why then do acupuncture researchers not get the point? Are they that stupid? I happen to know some of the authors of the above paper personally, and I can assure you, they are not stupid!

So, why?

I am afraid there is only one reason I can think of: they know perfectly well that such an RCT can only produce a positive finding, and precisely that is their reason for conducting such a study. In other words, they are not using science to test a hypothesis, they deliberately abuse it to promote their pet therapy or hypothesis.

As I stated above, it is fairly easy to design an RCT such that it can only produce a positive result. Yet, it is arguably also unethical, perhaps even fraudulent, to do this. In my view, such RCTs amount to pseudoscience and scientific misconduct.

The recent meta-analysis by Mathie et al for non-individualised homeopathy (recently discussed here) identified just 3 RCTs that were rated as  ‘reliable evidence’. But just how rigorous are these ‘best’ studies? Let’s find out!

THE FIRST STUDY

The objective of the first trial was “to evaluate the efficacy of the non-hormonal treatment BRN-01 in reducing hot flashes in menopausal women.” Its design was that of a multicentre (35 centres in France), randomized, double-blind, placebo-controlled. One hundred and eight menopausal women, ≥50 years of age, were enrolled in the study. The eligibility criteria included menopause for <24 months and ≥5 hot flashes per day with a significant negative effect on the women’s professional and/or personal life. Treatment was either BRN-01 tablets, a registered homeopathic medicine [not registered in the UK] containing Actaea racemosa (4 centesimal dilutions [4CH]), Arnica montana (4CH), Glonoinum (4CH), Lachesis mutus (5CH), and Sanguinaria canadensis (4CH), or placebo tablets, prepared by Laboratoires Boiron according to European Pharmacopoeia standards [available OTC in France]. Oral treatment (2 to 4 tablets per day) was started on day 3 after study enrolment and was continued for 12 weeks. The main outcome measure was the hot flash score (HFS) compared before, during, and after treatment. Secondary outcome criteria were the quality of life (QoL) [measured using the Hot Flash Related Daily Interference Scale (HFRDIS)], severity of symptoms (measured using the Menopause Rating Scale), evolution of the mean dosage, and compliance. All adverse events (AEs) were recorded. One hundred and one women were included in the final analysis (intent-to-treat population: BRN-01, n = 50; placebo, n = 51). The global HFS over the 12 weeks, assessed as the area under the curve (AUC) adjusted for baseline values, was significantly lower in the BRN-01 group than in the placebo group (mean ± SD 88.2 ± 6.5 versus 107.2 ± 6.4; p = 0.0411). BRN-01 was well tolerated; the frequency of AEs was similar in the two treatment groups, and no serious AEs were attributable to BRN-01. The authors concluded that BRN-01 seemed to have a significant effect on the HFS, compared with placebo. According to the results of this clinical trial, BRN-01 may be considered a new therapeutic option with a safe profile for hot flashes in menopausal women who do not want or are not able to take hormone replacement therapy or other recognized treatments for this indication.

Laboratoires Boiron provided BRN-01, its matching placebo, and financial support for the study. Randomization and allocation were carried out centrally by Laboratoires Boiron. I would argue that the treatment time in this study was way too short for generating a therapeutic response. The evolution of the HFS in the two groups was assessed by analysis of the area under the curve (AUC) of the mean scores recorded weekly from each patient in each group over the duration of the study, including those at enrollment (before any treatment). I wonder whether this method was chosen only when the researchers noted that the HFS at the pre-defined time points did not yield a significant result or whether it was pre-determined (elsewhere in the methods section we are told that “The primary evaluation criterion was the effect of BRN-01 on the HFS, compared with placebo. The HFS was defined as the product of the daily frequency and intensity of all hot flashes experienced by the patient, graded by the women from 1 to 4 (1 = mild; 2 = moderate; 3 = strong; 4 = very strong). These data were recorded by the women on a self-administered questionnaire, assisted by a telephone call from a clinical research associate. Data were collected (i) during the first 2 days after enrolment and before any medication had been taken; (ii) then every Tuesday and Wednesday of each week until the 11th week of treatment, inclusive; and (iii) finally, every day of the 12th week of treatment.”). Two of the authors of this paper are employees of Boiron.

THE SECOND STUDY

The second trial was aimed at finding out “whether a well-known and frequently prescribed homeopathic preparation could mitigate post-operative pain.” It was a randomized, double-blind, placebo-controlled trial to evaluate the efficacy of the homeopathic preparation Traumeel S® in minimizing post-operative pain and analgesic consumption following surgical correction of hallux valgus. Eighty consecutive patients were randomized to receive either Traumeel tablets or an indistinguishable placebo, and took primary and rescue oral analgesics as needed. Maximum numerical pain scores at rest and consumption of oral analgesics were recorded on day of surgery and for 13 days following surgery. Traumeel was not found superior to placebo in minimizing pain or analgesic consumption over the 14 days of the trial, however a transient reduction in the daily maximum post-operative pain score favoring the Traumeel arm was observed on the day of surgery, a finding supported by a treatment-time interaction test (p = 0.04). The authors concluded that Traumeel was not superior to placebo in minimizing pain or analgesic consumption over the 14 days of the trial. A transient reduction in the daily maximum post-operative pain score on the day of surgery is of questionable clinical importance.

Traumeel is a mixture of 6 ingredients, 4 of which are in the D2 potency. Thus it neither is administered as a homeopathic remedy (no ‘like cures like’) nor is it highly diluted. In fact, it is not homeopathy at all but belongs to a weird offspring of homeopathy called ‘homotoxicology’ [this is an explanation from my book: Homotoxicology is a method inspired by homeopathy which was developed by Hans Heinrich Reckeweg (1905 – 1985). He believed that all or most illness is caused by an overload of toxins in the body. The toxins originate, according to Reckeweg, both from the environment and from the malfunction of physiological processes within the body. His treatment consists mainly in applying homeopathic remedies which usually consist of combinations of single remedies, because health cannot be achieved without ridding the body of toxins. The largest manufacturer and promoter of remedies used in homotoxicology is the German firm Heel.] The HEEL Company (Baden-Baden, Germany) provided funding for the performance and monitoring of this project, supplied the study medication and placebo, and prepared the randomization list. The positive outcome mentioned in the authors’ conclusion refers to a secondary endpoint. I would argue that the authors should not have noted it there and should have made it clear that the trial generated a negative result.

THE THIRD STUDY

Finally, the third of the 3 ‘rigorous’ studies “evaluated the effectiveness of the homeopathic preparation Plumbum Metallicum  (PM) in reducing the blood lead levels of workers exposed to this metal.” The Brazilian researchers recruited 131 workers to this RCT who took PM in the CH15 potency or placebo for 35 days (10 drops twice daily). Thereafter, the percentage of workers whose lead level had fallen by at least 25% did not differ between the groups, both on intention to treat and per protocol analyses. The authors concluded that PM “had no effect in this study in terms of reducing serum lead in workers exposed to lead.”

This study lacks a power calculation, and arguably the period might have been too short to show an effect. The trial was published in the journal HOMEOPATHY which, some might argue, has not the most rigorous of peer-review procedures.

CONCLUDING REMARKS

The third study seems the most rigorous by far, in my view. The other two trials are seriously under-whelming in several respects, primarily because we cannot be sure how much influence the commercial interests of the sponsor had on their findings. I am sure others will spot weaknesses in all three trials that I failed to see.

Mathie et al partly disagree with my assessment when they write in their paper: “We report separately our model validity assessments of these trials, evaluating consequently their overall quality based on a GRADE-like principle of ‘downgrading’ [14]: two trials [23, 25] rated here as reliable evidence were downgraded to ‘low quality’ overall due to the inadequacy of their model validity; the remaining trial with reliable evidence [24] was judged to have adequate model validity. The latter study [24] thus comprises the sole RCT that can be designated ‘high quality’ overall by our approach, a stark finding that reveals further important aspects of the preponderantly low quality of the current body of evidence in non-individualised homeopathy.”

References 23, 24 and 25 are Padilha (the paper on Plumbum Metallicum), Colau (the RCT on menopausal women) and Singer (the Traumeel trial) respectively. This means that – as per Mathie’s assessment – just the Colau study remains as the sole trial with ‘reliable evidence’ for non-individualised homeopathy.

What Mathie et al seem to forget entirely is that none of the 3 RCTs is a trial of homeopathy as defined by treatment according to the ‘like cures like’ principle. The authors of the second study acknowledge this fact by stating: “Homeopathic purists may find fault in the administration of a standardized combination homeopathic formula to all patients, based upon clinical diagnosis – as opposed to the individualized manner dictated by standard homeopathic practice.”

So, which ever way we look upon this evidence, we cannot possibly deny that the evidence for non-individualised homeopathy is rubbish.

&nbsp;

This new systematic review by proponents of homeopathy (and supported by a grant from the Manchester Homeopathic Clinic) tested the null hypothesis that “the main outcome of treatment using a non-individualised (standardised) homeopathic medicine is indistinguishable from that of placebo“. An additional aim was to quantify any condition-specific effects of non-individualised homeopathic treatment. In reporting this paper, I will stay very close to the published text hoping that this avoids both misunderstandings and accusations of bias on my side:

Literature search strategy, data extraction and statistical analysis followed the methods described in a pre-published protocol. A trial comprised ‘reliable evidence’ if its risk of bias was low or it was unclear in one specified domain of assessment. ‘Effect size’ was reported as standardised mean difference (SMD), with arithmetic transformation for dichotomous data carried out as required; a negative SMD indicated an effect favouring homeopathy.

The authors excluded the following types of trials: studies of crossover design; of radionically prepared homeopathic medicines; of homeopathic prophylaxis; of homeopathy combined with other (complementary or conventional) intervention; for other specified reasons. The final explicit exclusion criterion was that there was obviously no blinding of participants and practitioners to the assigned intervention.

Forty-eight different clinical conditions were represented in 75 eligible RCTs; 49 were classed as ‘high risk of bias’ and 23 as ‘uncertain risk of bias’; the remaining three trials displayed sufficiently low risk of bias to be designated reliable evidence. Fifty-four trials had extractable data: pooled SMD was -0.33 (95% confidence interval (CI) -0.44, -0.21), which was attenuated to -0.16 (95% CI -0.31, -0.02) after adjustment for publication bias. The three trials with reliable evidence yielded a non-significant pooled SMD: -0.18 (95% CI -0.46, 0.09). There was no single clinical condition for which meta-analysis produced reliable evidence.

A meta-regression was performed to test specifically for within-group differences for each sub-group. The results showed that there were no significant differences between studies that were and were not:

  • included in previous meta-analyses (p = 0.447);
  • pilot studies (p = 0.316);
  • greater than the median sample (p = 0.298);
  • potency ≥ 12C (p = 0.221);
  • imputed for meta-analysis (p = 0.384);
  • free from vested interest (p = 0.391);
  • acute/chronic (p = 0.796);
  • different types of homeopathy (p = 0.217).

After removal of ‘C’-rated trials, the pooled SMD still favoured homeopathy for all sub-groups, but was statistically non-significant for 10 of the 18 (included in previous meta-analysis; pilot study; sample size > median; potency ≥12C; data imputed; free of vested interest; not free of vested interest; combination medicine; single medicine; chronic condition). There remained no significant differences between sub-groups—with the exception of the analysis for sample size > median (p = 0.028).

Meta-analyses were possible for eight clinical conditions, each analysis comprising two to 5 trials. A statistically significant pooled SMD, favouring homeopathy, was observed for influenza (N = 2), irritable bowel syndrome (N = 2), and seasonal allergic rhinitis (N = 5). Each of the other five clinical conditions (allergic asthma, arsenic toxicity, infertility due to amenorrhoea, muscle soreness, post-operative pain) showed non-significant findings. Removal of ‘C’-rated trials negated the statistically significant effect for seasonal allergic rhinitis and left the non-significant effect for post-operative pain unchanged; no higher-rated trials were available for additional analysis of arsenic toxicity, infertility due to amenorrhoea or irritable bowel syndrome. There were no ‘C’-rated trials to remove for allergic asthma, influenza, or muscle soreness. Thus, influenza was the only clinical condition for which higher-rated trials indicated a statistically significant effect; neither of its contributing trials, however, comprised reliable evidence.

The authors concluded that the quality of the body of evidence is low. A meta-analysis of all extractable data leads to rejection of our null hypothesis, but analysis of a small sub-group of reliable evidence does not support that rejection. Reliable evidence is lacking in condition-specific meta-analyses, precluding relevant conclusions. Better designed and more rigorous RCTs are needed in order to develop an evidence base that can decisively provide reliable effect estimates of non-individualised homeopathic treatment.

I am sure that this paper will lead to lively discussions in the comments section of this blog. I will therefore restrict my comments to a bare minimum.

In my view, this new meta-analysis essentially yield a negative result and confirms most previous, similar reviews.

  • It confirms Linde’s conclusion that “insufficient evidence from these studies that homeopathy is clearly efficacious for any single clinical condition”.
  • It confirms Linde’s conclusion that “there was clear evidence that studies with better methodological quality tended to yield less positive results”.
  • It confirms Kleinjen’s conclusion that “most trials are of low methodological quality”.
  • It also confirms the results of the meta-analysis by Shang et al (much-maligned by homeopaths) than “finding is compatible with the notion that the clinical effects of homoeopathy are placebo effects.”
  • Finally, it confirms the conclusion of the analysis of the Australian National Health and Medical Research Council: “Homeopathy should not be used to treat health conditions that are chronic, serious, or could become serious. People who choose homeopathy may put their health at risk if they reject or delay treatments for which there is good evidence for safety and effectiveness. People who are considering whether to use homeopathy should first get advice from a registered health practitioner. Those who use homeopathy should tell their health practitioner and should keep taking any prescribed treatments.”

Another not entirely unimportant point that often gets missed in these discussions is this: even if we believe (which I do not) the most optimistic interpretation of these (and similar data) by homeopaths, we ought to point out that there is no evidence whatsoever that homeopathy cures anything. At the very best it provides marginal symptomatic relief. Yet, the claim of homeopaths that we hear constantly is that homeopathy is a causal and curative therapy.

The first author of the new meta-analysis is an employee of the Homeopathy Research Institute. We might therefore forgive him that he he repeatedly insists on dwelling on largely irrelevant (i. e. based on unreliable primary studies) findings. It seems obvious that firm conclusions can only be based on reliable data. I therefore disregard those analyses and conclusions that include such studies.

In the discussion, the authors of the new meta-analysis confirm my interpretation this by stating that they “reject the null hypothesis (non-individualised homeopathy is indistinguishable from placebo) on the basis of pooling all studies, but fail to reject the null hypothesis on the basis of the reliable evidence only.” And, in the long version of their conclusions, we find this remarkable statement: “Our meta-analysis of the current reliable evidence base therefore fails to reject the null hypothesis that the outcome of treatment using a non-individualised homeopathic medicine is not distinguishable from that using placebo.” A most torturous way of stating the obvious: the more reliable data show no difference between homeopathy and placebo.

Acupuncture is little more than a theatrical placebo! If we confront an acupuncture fan with this statement, he/she is bound to argue that there are some indications for which the evidence is soundly positive. One of these conditions, they would claim, is nausea and vomiting. But how strong are these data? A new study sheds some light on this question.

The objective of this RCT was to evaluate if consumption of antiemetics and eating capacity differed between patients receiving verum acupuncture, sham acupuncture, or standard care only during radiotherapy. Patients were randomized to verum (n = 100) or sham (n = 100) acupuncture (telescopic blunt sham needle) (12 sessions) and registered daily their consumption of antiemetics and eating capacity. A standard care group (n = 62) received standard care only.

The results show that more patients in the verum and the sham acupuncture group did not need any antiemetic medications, as compared to the standard care group after receiving 27 Gray dose of radiotherapy. More patients in the verum and the sham acupuncture group were capable of eating as usual, compared to the standard care group. Patients receiving acupuncture had lower consumption of antiemetics and better eating capacity than patients receiving standard antiemetic care, plausible by nonspecific effects of the extra care during acupuncture.

The authors concluded that patients receiving acupuncture had lower consumption of antiemetics and better eating capacity than patients receiving standard antiemetic care, plausible by nonspecific effects of the extra care during acupuncture.

I find these conclusions odd because they seem to state that acupuncture was more effective than standard care. Subsequently – almost as an afterthought – they mention that its effects are brought about by nonspecific effects. This is grossly misleading, in my view.

The study was designed as a comparison between real and sham acupuncture, and the standard care group was not a randomised comparison group. Therefore, the main result and conclusion has to focus on the comparison between verum and sham acupuncture. This comparison shows that the two did not produce different result. Therefore, the study shows that acupuncture was not effective.

A much more reasonable conclusion would have been: THIS STUDY FAILED TO FIND SIGNIFICANT EFFECTS OF ACUPUNCTURE BEYOND PLACEBO.

Tui Na is a massage technique that is based on the Taoist principles of TCM. It involves a range of manipulations usually performed by an operator’s finger, hand, elbow, knee, or foot applied to muscle or soft tissue at specific parts of the body. According to one website of TCM-proponents “Tui Na makes use of various hand techniques in combination with acupuncture and other manipulation techniques. To enhance the healing process, the practitioner may recommend the use of Chinese herbs. Many of the techniques used in this massage resemble that of a western massage like gliding, kneading, vibration, tapping, friction, pulling, rolling, pressing and shaking. In Tui Na massage, the muscles and tendons are massaged with the help of hands, and an acupressure technique is applied to directly affect the flow of Qi at different acupressure points of the body, thus facilitating the healing process. It removes the blockages and keeps the energy moving through the meridians as well as the muscles. A typical session of Tui Na massage may vary from thirty minutes to an hour. The session timings may vary depending on the patient’s needs and condition. The best part of the therapy is that it relaxes as well as energizes the person. The main benefit of Tui Na massage is that it focuses on the specific problem, whether it is an acute or a chronic pain associated with the joints, muscles or a skeletal system. This technique is very beneficial in reducing the pain of neck, shoulders, hips, back, arms, highs, legs and ankle disorders. It is a very effective therapy for arthritis, pain, sciatica and muscle spasms. Other benefits of this massage therapy include alleviation of the stress related disorders like insomnia, constipation, headaches and other disorders related to digestive, respiratory and reproductive systems. The greatest advantage of Tui Na is that it focuses on maintaining overall balance with both physical and mental health. Any one who wants to avoid the side effects of drugs or a chemical based treatment can adopt this effective massage technique to alleviate their pain. Tui Na massage therapy is now becoming a more common therapy method due to its focus on specific problems rather than providing a general treatment.”

This clearly begs the question IS IT EFFECTIVE?

This systematic review assessed the evidence of Tui Na for cervical radiculopathy. Seven databases were searched. Randomised controlled trials (RCTs) incorporating Tui Na alone or Tui Na combined with conventional treatment were included. Five studies involving 448 patients were found. The pooled analysis from the 3 trials indicated that Tui Na alone showed a significant lowering immediate effects on pain score with moderate heterogeneity compared to cervical traction. The meta-analysis from 2 trials revealed significant immediate effects of Tui Na plus cervical traction in improving pain score with no heterogeneity compared to cervical traction alone. None of the RCTs mentioned adverse effects. There was very low quality or low quality evidence to support the results.

The authors concluded that “Tui Na alone or Tui Na plus cervical traction may be helpful to cervical radiculopathy patients, but supportive evidence seems generally weak. Future clinical studies with low risk of bias and adequate follow-up design are recommended.”

In my view, this is a misleading conclusion. A correct one would have been: THE CURRENT EVIDENCE IS INSUFFICIENT TO DRAW ANY CONCLUSIONS ABOUT THE EFFECTIVENESS OF TUI NA.

Why?

Here are some of the most obvious reasons:

Personally, I am getting very tired of conclusions stating ‘…XY MAY BE EFFECTIVE/HELPFUL/USEFUL/WORTH A TRY…’ It is obvious that the therapy in question MAY be effective, otherwise one would surely not conduct a systematic review. If a review fails to produce good evidence, it is the authors’ ethical, moral and scientific obligation to state this clearly. If they don’t, they simply misuse science for promotion and mislead the public. Strictly speaking, this amounts to scientific misconduct.

Drug and alcohol dependencies are notoriously difficult to treat effectively. Patients and their families are often desperate and willing to try anything. This seems like an ideal ground for acupuncturists who are, in my experience, experts in putting up smokescreens hiding the true value of their treatment.

The best way to determine the value of any intervention is probably conducting a systematic review of the evidence from rigorous clinical trials. Today we are in the fortunate position to have not just one of those articles; but do they really tell us the truth?

This brand-new systematic review investigated the effects of acupuncture on alcohol-related symptoms and behaviors in patients with this disorder. The PubMed database was searched until 23 August 2016, and reference lists from review studies were also reviewed. The inclusion criteria were the following: (1) being published in a peer-reviewed English-language journal, (2) use of randomized controlled trials (RCTs), (3) assessing the effects of acupuncture on psychological variables in individuals with a primary alcohol problem, and (4) reporting statistics that could be converted to effect sizes.

Seventeen studies were identified for a full-text inspection, and seven (243 patients) of these met our inclusion criteria. The outcomes assessed at the last post-treatment point and any available follow-up data were extracted from each of the studies. Five studies treated patients by inserting a needle into several acupoints in each ear. Two studies stimulated body points with or without ear stimulation. Four studies treated control patients with a placebo needle or under a completely different type of intervention, such as relaxation or transdermal stimulation, whereas the remaining studies inserted needles into nonspecific points. The patients were treated for 2 weeks to 3 months, and the treatment duration per session was 15–45 min. The results of the meta-analysis demonstrated that an acupuncture intervention had a stronger effect on reducing alcohol-related symptoms and behaviours than did the control intervention. A beneficial but weak effect of acupuncture treatment was also found in the follow-up data.

The authors concluded that although our analysis showed a significant difference between acupuncture and the control intervention in patients with alcohol use disorder, this meta-analysis is limited by the small number of studies included. Thus, a larger cohort study is required to provide a firm conclusion.

I am used to reading poor research papers, but this one is like a new dimension. Here are just the most obvious flaws:

  • by searching just one database, the likelihood of missing studies is huge,
  • by excluding non-English papers, the review automatically becomes non-systematic,
  • the included studies differed vastly in many respects and can therefore not be pooled.

As it happens, a further meta-analysis has just been published. Here is its abstract:

Acupuncture has been widely used as a treatment for alcohol dependence. An updated and rigorously conducted systematic review is needed to establish the extent and quality of the evidence on the effectiveness of acupuncture as an intervention for reducing alcohol dependence. This review aimed to ascertain the effectiveness of acupuncture for reducing alcohol dependence as assessed by changes in either craving or withdrawal symptoms.

Methods

In this systematic review, a search strategy was designed to identify randomised controlled trials (RCTs) published in either the English or Chinese literature, with a priori eligibility criteria. The following English language databases were searched from inception until June 2015: AMED, Cochrane Library, EMBASE, MEDLINE, PsycINFO, and PubMed; and the following Chinese language databases were similarly searched: CNKI, Sino-med, VIP, and WanFang. Methodological quality of identified RCTs was assessed using the Jadad Scale and the Cochrane Risk of Bias tool.

Results

Fifteen RCTs were included in this review, comprising 1378 participants. The majority of the RCTs were rated as having poor methodological rigour. A statistically significant effect was found in the two primary analyses: acupuncture reduced alcohol craving compared with all controls (SMD = −1.24, 95% CI = −1.96 to −0.51); and acupuncture reduced alcohol withdrawal symptoms compared with all controls (SMD = −0.50, 95% CI = −0.83 to −0.17). In secondary analyses: acupuncture reduced craving compared with sham acupuncture (SMD = −1.00, 95% CI = −1.79 to −0.21); acupuncture reduced craving compared with controls in RCTs conducted in Western countries (SMD = −1.15, 95% CI = −2.12 to −0.18); and acupuncture reduced craving compared with controls in RCTs with only male participants (SMD = −1.68, 95% CI = −2.62 to −0.75).

Conclusion

This study showed that acupuncture was potentially effective in reducing alcohol craving and withdrawal symptoms and could be considered as an additional treatment choice and/or referral option within national healthcare systems.

This Meta-analysis is only a little better than the first, I am afraid. What its conclusions do not sufficiently reflect, in my view, is the fact that the quality of the primary studies was mostly very poor – too poor to draw conclusions from (other than ‘acupuncture research is usually lousy’; see figure below). Therefore, I fail to see how the authors could draw the relatively firm and positive conclusions cited above. In my view, they should have stated something like this: DUE TO THE RISK OF BIAS IN MANY TRIALS, THE EFFECTIVENESS OF ACUPUNCTURE REMAINS UNPROVEN.

The authors of the first meta-analysis open the discussion by proudly declaring that “the present study is the first meta-analysis to examine the effect of acupuncture treatment on patients with alcohol use disorder and to provide data on the magnitude of this effect on alcohol-related clinical symptoms and behaviours.” They discretely overlook this meta-analysis from 2009 (and several others which even their rudimentary search would have identified):

Nineteen electronic databases, including English, Korean, Japanese, and Chinese databases, were systematically searched for RCTs of acupuncture for alcohol dependence up to June 2008 with no language restrictions. The methodological qualities of eligible studies were assessed using the criteria described in the Cochrane Handbook.

Eleven studies, which comprised a total of 1,110 individual cases, were systematically reviewed. Only 2 of 11 trials reported satisfactorily all quality criteria. Four trials comparing acupuncture treatment and sham treatments reported data for alcohol craving. Three studies reported that there were no significant differences. Among 4 trials comparing acupuncture and no acupuncture with conventional therapies, 3 reported significant reductions. No differences between acupuncture and sham treatments were found for completion rates (Risk Ratio = 1.07, 95% confidence interval, CI = 0.91 to 1.25) or acupuncture and no acupuncture (Risk Ratio = 1.15, 95% CI = 0.79 to 1.67). Only 3 RCTs reported acupuncture-related adverse events, which were mostly minimal.

The results of the included studies were equivocal, and the poor methodological quality and the limited number of the trials do not allow any conclusion about the efficacy of acupuncture for treatment of alcohol dependence. More research and well-designed, rigorous, and large clinical trials are necessary to address these issues.

One does not need to be an expert in interpreting meta-analyses, I think, to see that this paper is more rigorous than the new ones (which incidentally were published in the very dubious journals). And this is why I trust the conclusions of this last-named meta-analysis more than those of the new one: the efficacy of acupuncture remains unproven. And this means that we should not employ or promote it for routine care.

Gravityscan Badge

Recent Comments

Note that comments can be edited for up to five minutes after they are first submitted.


Click here for a comprehensive list of recent comments.

Categories