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Often referred to as “Psychological acupressure”, the emotional freedom technique (EFT) works by releasing blockages within the energy system which are the source of emotional intensity and discomfort. These blockages in our energy system, in addition to challenging us emotionally, often lead to limiting beliefs and behaviours and an inability to live life harmoniously. Resulting symptoms are either emotional and/ or physical and include lack of confidence and self esteem, feeling stuck anxious or depressed, or the emergence of compulsive and addictive behaviours. It is also now finally widely accepted that emotional disharmony is a key factor in physical symptoms and dis-ease and for this reason these techniques are being extensively used on physical issues, including chronic illness with often astounding results. As such these techniques are being accepted more and more in medical and psychiatric circles as well as in the range of psychotherapies and healing disciplines.

An EFT treatment involves the use of fingertips rather than needles to tap on the end points of energy meridians that are situated just beneath the surface of the skin. The treatment is non-invasive and works on the ethos of making change as simple and as pain free as possible.

EFT is a common sense approach that draws its power from Eastern discoveries that have been around for over 5,000 years. In fact Albert Einstein also told us back in the 1920’s that everything (including our bodies) is composed of energy. These ideas have been largely ignored by Western Healing Practices and as they are unveiled in our current times, human process is reopening itself to the forgotten truth that everything is Energy and the potential that this offers us.


If you ask me, this sounds as though EFT combines pseudo-psychological with acupuncture-BS.

But I may be wrong.

What does the evidence tell us?

A systematic review included 14 RCTs of EFT with a total of 658 patients.  The pre-post effect size for the EFT treatment group was 1.23 (95% confidence interval, 0.82-1.64; p < 0.001), whereas the effect size for combined controls was 0.41 (95% confidence interval, 0.17-0.67; p = 0.001). Emotional freedom technique treatment demonstrated a significant decrease in anxiety scores, even when accounting for the effect size of control treatment. However, there were too few data available comparing EFT to standard-of-care treatments such as cognitive behavioural therapy, and further research is needed to establish the relative efficacy of EFT to established protocols.  Meta-analyses indicate large effect sizes for posttraumatic stress disorder, depression, and anxiety; however, treatment effects may be due to components EFT shares with other therapies.

Another, more recent analysis reviewed whether EFTs acupressure component was an active ingredient. Six studies of adults with diagnosed or self-identified psychological or physical symptoms were compared (n = 403), and three (n = 102) were identified. Pretest vs. posttest EFT treatment showed a large effect size, Cohen’s d = 1.28 (95% confidence interval [CI], 0.56 to 2.00) and Hedges’ g = 1.25 (95% CI, 0.54 to 1.96). Acupressure groups demonstrated moderately stronger outcomes than controls, with weighted posttreatment effect sizes of d = -0.47 (95% CI, -0.94 to 0.0) and g = -0.45 (95% CI, -0.91 to 0.0). Meta-analysis indicated that the acupressure component was an active ingredient and outcomes were not due solely to placebo, nonspecific effects of any therapy, or non-acupressure components.

From these and other reviews, one could easily get the impression that my above-mentioned suspicion is erroneous and EFT is an effective therapy. But I still do have my doubts.


These reviews conveniently forget to mention that the primary studies tend to be of poor or even very poor quality. The most common flaws include tiny sample sizes, wrong statistical approach, lack of blinding, lack of control of placebo and other nonspecific effects. Reviews of such studies thus turn out to be a confirmation of the ‘rubbish in, rubbish out’ principle: any summary of flawed studies are likely to produce a flawed result.

Until I have good quality trials to convince me otherwise, EFT is in my view:

  1. implausible and
  2. not of proven effectiveness for any condition.

Aromatherapy usually involves the application of diluted essential (volatile) oils via a gentle massage of the body surface. The chemist Rene-Maurice Gattefosse (1881-1950) coined the term ‘aromatherapy’ after experiencing that lavender oil helped to cure a severe burn of his hand. In 1937, he published a book on the subject: Aromathérapie: Les Huiles Essentielles, Hormones Végétales. Later, the French surgeon Jean Valnet used essential oils to help heal soldiers’ wounds in World War II.

Aromatherapy is currently one of the most popular of all alternative therapies. The reason for its popularity seems simple: it is an agreeable, luxurious form of pampering. Whether it truly merits to be called a therapy is debatable.

The authors of this systematic review stated that they wanted to critically assess the effect of aromatherapy on the psychological symptoms as noted in the postmenopausal and elderly women. They conducted electronic literature searches and fount 4 trials that met their inclusion criteria. The findings demonstrated that aromatherapy massage significantly improves psychological symptoms in menopausal, elderly women as compared to controls. In one trial, aromatherapy massage was no more effective than the untreated group regarding their experience of symptoms such as nervousness.

The authors concluded that aromatherapy may be beneficial in attenuating the psychological symptoms that these women may experience, such as anxiety and depression, but it is not considered as an effective treatment to manage nervousness symptom among menopausal women. This finding should be observed in light of study limitations.

In the discussion section, the authors state that to the best of our knowledge, this is the first meta-analysis evaluating the effect of aromatherapy on the psychological symptoms. I believe that they might be mistaken. Here are two of my own papers (other researchers have published further reviews) on the subject:

  1. Aromatherapy is the therapeutic use of essential oil from herbs, flowers, and other plants. The aim of this overview was to provide an overview of systematic reviews evaluating the effectiveness of aromatherapy. We searched 12 electronic databases and our departmental files without restrictions of time or language. The methodological quality of all systematic reviews was evaluated independently by two authors. Of 201 potentially relevant publications, 10 met our inclusion criteria. Most of the systematic reviews were of poor methodological quality. The clinical subject areas were hypertension, depression, anxiety, pain relief, and dementia. For none of the conditions was the evidence convincing. Several SRs of aromatherapy have recently been published. Due to a number of caveats, the evidence is not sufficiently convincing that aromatherapy is an effective therapy for any condition.
  2. Aromatherapy is becoming increasingly popular; however there are few clear indications for its use. To systematically review the literature on aromatherapy in order to discover whether any clinical indication may be recommended for its use, computerised literature searches were performed to retrieve all randomised controlled trials of aromatherapy from the following databases: MEDLINE, EMBASE, British Nursing Index, CISCOM, and AMED. The methodological quality of the trials was assessed using the Jadad score. All trials were evaluated independently by both authors and data were extracted in a pre-defined, standardised fashion. Twelve trials were located: six of them had no independent replication; six related to the relaxing effects of aromatherapy combined with massage. These studies suggest that aromatherapy massage has a mild, transient anxiolytic effect. Based on a critical assessment of the six studies relating to relaxation, the effects of aromatherapy are probably not strong enough for it to be considered for the treatment of anxiety. The hypothesis that it is effective for any other indication is not supported by the findings of rigorous clinical trials.

Omitting previous research may be odd, but it is not a fatal flaw. What makes this review truly dismal is the fact that the authors fail to discuss the poor quality of the primary studies. They are of such deplorable rigor that one can really not draw any conclusion at all from them. I therefore find the conclusions of this new paper unacceptable and think that our statement (even though a few years old) is much more accurate: the evidence is not sufficiently convincing that aromatherapy is an effective therapy for any condition.

I remember reading this paper entitled ‘Comparison of acupuncture and other drugs for chronic constipation: A network meta-analysis’ when it first came out. I considered discussing it on my blog, but then decided against it for a range of reasons which I shall explain below. The abstract of the original meta-analysis is copied below:

The objective of this study was to compare the efficacy and side effects of acupuncture, sham acupuncture and drugs in the treatment of chronic constipation. Randomized controlled trials (RCTs) assessing the effects of acupuncture and drugs for chronic constipation were comprehensively retrieved from electronic databases (such as PubMed, Cochrane Library, Embase, CNKI, Wanfang Database, VIP Database and CBM) up to December 2017. Additional references were obtained from review articles. With quality evaluations and data extraction, a network meta-analysis (NMA) was performed using a random-effects model under a frequentist framework. A total of 40 studies (n = 11032) were included: 39 were high-quality studies and 1 was a low-quality study. NMA showed that (1) acupuncture improved the symptoms of chronic constipation more effectively than drugs; (2) the ranking of treatments in terms of efficacy in diarrhoea-predominant irritable bowel syndrome was acupuncture, polyethylene glycol, lactulose, linaclotide, lubiprostone, bisacodyl, prucalopride, sham acupuncture, tegaserod, and placebo; (3) the ranking of side effects were as follows: lactulose, lubiprostone, bisacodyl, polyethylene glycol, prucalopride, linaclotide, placebo and tegaserod; and (4) the most commonly used acupuncture point for chronic constipation was ST25. Acupuncture is more effective than drugs in improving chronic constipation and has the least side effects. In the future, large-scale randomized controlled trials are needed to prove this. Sham acupuncture may have curative effects that are greater than the placebo effect. In the future, it is necessary to perform high-quality studies to support this finding. Polyethylene glycol also has acceptable curative effects with fewer side effects than other drugs.


This meta-analysis has now been retracted. Here is what the journal editors have to say about the retraction:

After publication of this article [1], concerns were raised about the scientific validity of the meta-analysis and whether it provided a rigorous and accurate assessment of published clinical studies on the efficacy of acupuncture or drug-based interventions for improving chronic constipation. The PLOS ONE Editors re-assessed the article in collaboration with a member of our Editorial Board and noted several concerns including the following:

  • Acupuncture and related terms are not mentioned in the literature search terms, there are no listed inclusion or exclusion criteria related to acupuncture, and the outcome measures were not clearly defined in terms of reproducible clinical measures.
  • The study included acupuncture and electroacupuncture studies, though this was not clearly discussed or reported in the Title, Methods, or Results.
  • In the “Routine paired meta-analysis” section, both acupuncture and sham acupuncture groups were reported as showing improvement in symptoms compared with placebo. This finding and its implications for the conclusions of the article were not discussed clearly.
  • Several included studies did not meet the reported inclusion criteria requiring that studies use adult participants and assess treatments of >2 weeks in duration.
  • Data extraction errors were identified by comparing the dataset used in the meta-analysis (S1 Table) with details reported in the original research articles. Errors included aspects of the study design such as the experimental groups included in the study, the number of study arms in the trial, number of participants, and treatment duration. There are also several errors in the Reference list.
  • With regard to side effects, 22 out of 40 studies were noted as having reported side effects. It was not made clear whether side effects were assessed as outcome measures for the other 18 studies, i.e. did the authors collect data clarifying that there were no side effects or was this outcome measure not assessed or reported in the original article. Without this clarification the conclusion comparing side effect frequencies is not well supported.
  • The network geometry presented in Fig 5 is not correct and misrepresents some of the study designs, for example showing two-arm studies as three-arm studies.
  • The overall results of the meta-analysis are strongly reliant on the evidence comparing acupuncture versus lactulose treatment. Several of the trials that assessed this comparison were poorly reported, and the meta-analysis dataset pertaining to these trials contained data extraction errors. Furthermore, potential bias in studies assessing lactulose efficacy in acupuncture trials versus lactulose efficacy in other trials was not sufficiently addressed.

While some of the above issues could be addressed with additional clarifications and corrections to the text, the concerns about study inclusion, the accuracy with which the primary studies’ research designs and data were represented in the meta-analysis, and the reporting quality of included studies directly impact the validity and accuracy of the dataset underlying the meta-analysis. As a consequence, we consider that the overall conclusions of the study are not reliable. In light of these issues, the PLOS ONE Editors retract the article. We apologize that these issues were not adequately addressed during pre-publication peer review.

LZ disagreed with the retraction. YM and XD did not respond.


Let me start by explaining why I initially decided not to discuss this paper on my blog. Already the first sentence of the abstract put me off, and an entire chorus of alarm-bells started ringing once I read further.

  • A meta-analysis is not a ‘study’ in my book, and I am somewhat weary of researchers who employ odd or unprecise language.
  • We all know (and I have discussed it repeatedly) that studies of acupuncture frequently fail to report adverse effects (in doing this, their authors violate research ethics!). So, how can it be a credible aim of a meta-analysis to compare side-effects in the absence of adequate reporting?
  • The methodology of a network meta-analysis is complex and I know not a lot about it.
  • Several things seemed ‘too good to be true’, for instance, the funnel-plot and the overall finding that acupuncture is the best of all therapeutic options.
  • Looking at the references, I quickly confirmed my suspicion that most of the primary studies were in Chinese.

In retrospect, I am glad I did not tackle the task of criticising this paper; I would probably have made not nearly such a good job of it as PLOS ONE eventually did. But it was only after someone raised concerns that the paper was re-reviewed and all the defects outlined above came to light.

While some of my concerns listed above may have been trivial, my last point is the one that troubles me a lot. As it also related to dozens of Cochrane reviews which currently come out of China, it is worth our attention, I think. The problem, as I see it, is as follows:

  • Chinese (acupuncture, TCM and perhaps also other) trials are almost invariably reporting positive findings, as we have discussed ad nauseam on this blog.
  • Data fabrication seems to be rife in China.
  • This means that there is good reason to be suspicious of such trials.
  • Many of the reviews that currently flood the literature are based predominantly on primary studies published in Chinese.
  • Unless one is able to read Chinese, there is no way of evaluating these papers.
  • Therefore reviewers of journal submissions tend to rely on what the Chinese review authors write about the primary studies.
  • As data fabrication seems to be rife in China, this trust might often not be justified.
  • At the same time, Chinese researchers are VERY keen to publish in top Western journals (this is considered a great boost to their career).
  • The consequence of all this is that reviews of this nature might be misleading, even if they are published in top journals.

I have been struggling with this problem for many years and have tried my best to alert people to it. However, it does not seem that my efforts had even the slightest success. The stream of such reviews has only increased and is now a true worry (at least for me). My suspicion – and I stress that it is merely that – is that, if one would rigorously re-evaluate these reviews, their majority would need to be retracted just as the above paper. That would mean that hundreds of papers would disappear because they are misleading, a thought that should give everyone interested in reliable evidence sleepless nights!

So, what can be done?

Personally, I now distrust all of these papers, but I admit, that is not a good, constructive solution. It would be better if Journal editors (including, of course, those at the Cochrane Collaboration) would allocate such submissions to reviewers who:

  • are demonstrably able to conduct a CRITICAL analysis of the paper in question,
  • can read Chinese,
  • have no conflicts of interest.

In the case of an acupuncture review, this would narrow it down to perhaps just a handful of experts worldwide. This probably means that my suggestion is simply not feasible.

But what other choice do we have?

One could oblige the authors of all submissions to include full and authorised English translations of non-English articles. I think this might work, but it is, of course, tedious and expensive. In view of the size of the problem (I estimate that there must be around 1 000 reviews out there to which the problem applies), I do not see a better solution.

(I would truly be thankful, if someone had a better one and would tell us)

I have often cautioned my readers about the ‘evidence’ supporting acupuncture (and other alternative therapies). Rightly so, I think. Here is yet another warning.

This systematic review assessed the clinical effectiveness of acupuncture in the treatment of postpartum depression (PPD). Nine trials involving 653 women were selected. A meta-analysis demonstrated that the acupuncture group had a significantly greater overall effective rate compared with the control group. Moreover, acupuncture significantly increased oestradiol levels compared with the control group. Regarding the HAMD and EPDS scores, no difference was found between the two groups. The Chinese authors concluded that acupuncture appears to be effective for postpartum depression with respect to certain outcomes. However, the evidence thus far is inconclusive. Further high-quality RCTs following standardised guidelines with a low risk of bias are needed to confirm the effectiveness of acupuncture for postpartum depression.

What a conclusion!

What a review!

What a journal!

What evidence!

Let’s start with the conclusion: if the authors feel that the evidence is ‘inconclusive’, why do they state that ‘acupuncture appears to be effective for postpartum depression‘. To me this does simply not make sense!

Such oddities are abundant in the review. The abstract does not mention the fact that all trials were from China (published in Chinese which means that people who cannot read Chinese are unable to check any of the reported findings), and their majority was of very poor quality – two good reasons to discard the lot without further ado and conclude that there is no reliable evidence at all.

The authors also tell us very little about the treatments used in the control groups. In the paper, they state that “the control group needed to have received a placebo or any type of herb, drug and psychological intervention”. But was acupuncture better than all or any of these treatments? I could not find sufficient data in the paper to answer this question.

Moreover, only three trials seem to have bothered to mention adverse effects. Thus the majority of the studies were in breach of research ethics. No mention is made of this in the discussion.

In the paper, the authors re-state that “this meta-analysis showed that the acupuncture group had a significantly greater overall effective rate compared with the control group. Moreover, acupuncture significantly increased oestradiol levels compared with the control group.” This is, I think, highly misleading (see above).

Finally, let’s have a quick look at the journal ‘Acupuncture in Medicine’ (AiM). Even though it is published by the BMJ group (the reason for this phenomenon can be found here: “AiM is owned by the British Medical Acupuncture Society and published by BMJ”; this means that all BMAS-members automatically receive the journal which thus is a resounding commercial success), it is little more than a cult-newsletter. The editorial board is full of acupuncture enthusiasts, and the journal hardly ever publishes anything that is remotely critical of the wonderous myths of acupuncture.

My conclusion considering all this is as follows: we ought to be very careful before accepting any ‘evidence’ that is currently being published about the benefits of acupuncture, even if it superficially looks ok. More often than not, it turns out to be profoundly misleading, utterly useless and potentially harmful pseudo-evidence.


Acupunct Med. 2018 Jun 15. pii: acupmed-2017-011530. doi: 10.1136/acupmed-2017-011530. [Epub ahead of print]

Effectiveness of acupuncture in postpartum depression: a systematic review and meta-analysis.

Li S, Zhong W, Peng W, Jiang G.

Most people probably think of acupuncture as being used mainly as a therapy for pain control. But acupuncture is currently being promoted (and has traditionally been used) for all sorts of conditions. One of them is stroke. It is said to speed up recovery and even improve survival rates after such an event. There are plenty of studies on this subject, but their results are far from uniform. What is needed in this situation, is a rigorous summary of the evidence.

The authors of this Cochrane review wanted to assess whether acupuncture could reduce the proportion of people suffering death or dependency after acute ischaemic or haemorrhagic stroke. They included all randomized clinical trials (RCTs) of acupuncture started within 30 days after stroke onset. Acupuncture had to be compared with placebo or sham acupuncture or open control (no placebo) in people with acute ischaemic or haemorrhagic stroke, or both. Comparisons were made versus (1) all controls (open control or sham acupuncture), and (2) sham acupuncture controls.

The investigators included 33 RCTs with 3946 participants. Outcome data were available for up to 22 trials (2865 participants) that compared acupuncture with any control (open control or sham acupuncture) but for only 6 trials (668 participants) comparing acupuncture with sham acupuncture.

When compared with any control (11 trials with 1582 participants), findings of lower odds of death or dependency at the end of follow-up and over the long term (≥ three months) in the acupuncture group were uncertain and were not confirmed by trials comparing acupuncture with sham acupuncture. In trials comparing acupuncture with any control, findings that acupuncture was associated with increases in the global neurological deficit score and in the motor function score were uncertain. These findings were not confirmed in trials comparing acupuncture with sham acupuncture.Trials comparing acupuncture with any control showed little or no difference in death or institutional care or death at the end of follow-up.The incidence of adverse events (eg, pain, dizziness, faint) in the acupuncture arms of open and sham control trials was 6.2% (64/1037 participants), and 1.4% of these patients (14/1037 participants) discontinued acupuncture. When acupuncture was compared with sham acupuncture, findings for adverse events were uncertain.

The authors concluded that this updated review indicates that apparently improved outcomes with acupuncture in acute stroke are confounded by the risk of bias related to use of open controls. Adverse events related to acupuncture were reported to be minor and usually did not result in stopping treatment. Future studies are needed to confirm or refute any effects of acupuncture in acute stroke. Trials should clearly report the method of randomization, concealment of allocation, and whether blinding of participants, personnel, and outcome assessors was achieved, while paying close attention to the effects of acupuncture on long-term functional outcomes.

This Cochrane review seems to be thorough, but it is badly written (Cochrane reviewers: please don’t let this become the norm!). It contains some interesting facts. The majority of the studies came from China. This review confirmed the often very poor methodological quality of acupuncture trials which I have frequently mentioned before.

In particular, the RCTs originating from China were amongst those that most overtly lacked rigor, also a fact that has been discussed regularly on this blog.

For me, by far the most important finding of this review is that studies which at least partly control for placebo effects fail to show positive results. Depending on where you stand in the never-ending debate about acupuncture, this could lead to two dramatically different conclusions:

  1. If you are a believer in or earn your living from acupuncture, you might say that these results suggest that the trials were in some way insufficient and therefore they produced false-negative results.
  2. If you are a more reasonable observer, you might feel that these results show that acupuncture (for acute stroke) is a placebo therapy.

Regardless to which camp you belong, one thing seems to be certain: acupuncture for stroke (and other indications) is not supported by sound evidence. And that means, I think, that it is not responsible to use it in routine care.

My previous post praised the validity and trustworthiness of Cochrane reviews. This post continues in the same line.

Like osteoarthritis, acute stroke has been a condition for which acupuncture-fans prided themselves of being able to produce fairly good evidence. A Cochrane review of 2005, however, was inconclusive and concluded that the number of patients is too small to be certain whether acupuncture is effective for treatment of acute ischaemic or haemorrhagic stroke. Larger, methodologically-sound trials are required.

So, 13 years later, we do have more evidence, and it would be interesting to know what the best evidence tells us today. This new review will tell us because it is the update of the previous Cochrane Review originally published in 2005.

The authors sought randomized clinical trials (RCTs) of acupuncture started within 30 days from stroke onset compared with placebo or sham acupuncture or open control (no placebo) in people with acute ischemic or haemorrhagic stroke, or both. Needling into the skin was required for acupuncture. Comparisons were made versus (1) all controls (open control or sham acupuncture), and (2) sham acupuncture controls.

Two review authors applied the inclusion criteria, assessed trial quality and risk of bias, and extracted data independently. They contacted study authors to ask for missing data and assessed the quality of the evidence by using the GRADE approach. The primary outcome was defined as death or dependency at the end of follow-up.

In total, 33 RCTs with 3946 participants were included. Twenty new trials with 2780 participants had been completed since the previous review. Outcome data were available for up to 22 trials (2865 participants) that compared acupuncture with any control (open control or sham acupuncture) but for only six trials (668 participants) that compared acupuncture with sham acupuncture control. The authors downgraded the evidence to low or very low quality because of risk of bias in included studies, inconsistency in the acupuncture intervention and outcome measures, and imprecision in effect estimates.

When compared with any control (11 trials with 1582 participants), findings of lower odds of death or dependency at the end of follow-up and over the long term (≥ three months) in the acupuncture group were uncertain (odds ratio [OR] 0.61, 95% confidence interval [CI] 0.46 to 0.79; very low-quality evidence; and OR 0.67, 95% CI 0.53 to 0.85; eight trials with 1436 participants; very low-quality evidence, respectively) and were not confirmed by trials comparing acupuncture with sham acupuncture (OR 0.71, 95% CI 0.43 to 1.18; low-quality evidence; and OR 0.67, 95% CI 0.40 to 1.12; low-quality evidence, respectively).In trials comparing acupuncture with any control, findings that acupuncture was associated with increases in the global neurological deficit score and in the motor function score were uncertain (standardized mean difference [SMD] 0.84, 95% CI 0.36 to 1.32; 12 trials with 1086 participants; very low-quality evidence; and SMD 1.08, 95% CI 0.45 to 1.71; 11 trials with 895 participants; very low-quality evidence).

These findings were not confirmed in trials comparing acupuncture with sham acupuncture (SMD 0.01, 95% CI -0.55 to 0.57; low-quality evidence; and SMD 0.10, 95% CI -0.38 to 0.17; low-quality evidence, respectively).Trials comparing acupuncture with any control reported little or no difference in death or institutional care at the end of follow-up (OR 0.78, 95% CI 0.54 to 1.12; five trials with 1120 participants; low-quality evidence), death within the first two weeks (OR 0.91, 95% CI 0.33 to 2.55; 18 trials with 1612 participants; low-quality evidence), or death at the end of follow-up (OR 1.08, 95% CI 0.74 to 1.58; 22 trials with 2865 participants; low-quality evidence).

The incidence of adverse events (eg, pain, dizziness, fainting) in the acupuncture arms of open and sham control trials was 6.2% (64/1037 participants), and 1.4% of these (14/1037 participants) discontinued acupuncture. When acupuncture was compared with sham acupuncture, findings for adverse events were uncertain (OR 0.58, 95% CI 0.29 to 1.16; five trials with 576 participants; low-quality evidence).

The authors concluded that this updated review indicates that apparently improved outcomes with acupuncture in acute stroke are confounded by the risk of bias related to use of open controls. Adverse events related to acupuncture were reported to be minor and usually did not result in stopping treatment. Future studies are needed to confirm or refute any effects of acupuncture in acute stroke. Trials should clearly report the method of randomization, concealment of allocation, and whether blinding of participants, personnel, and outcome assessors was achieved, while paying close attention to the effects of acupuncture on long-term functional outcomes.

These cautious conclusions might be explained by the fact that Chinese researchers are reluctant to state anything overtly negative about any TCM therapy. Recently, one expert who spoke out was even imprisoned for criticising a TCM product! But in truth, this review really shows that acupuncture has no convincing effect in acute stroke.

And for me, this conclusion is fascinating. I have been involved in acupuncture/stroke research since the early 1990s.

Our RCT produced a resounding negative result concluding that acupuncture is not superior to sham treatment for recovery in activities of daily living and health-related quality of life after stroke, although there may be a limited effect on leg function in more severely affected patients.

Our 1996 systematic review concluded that the evidence that acupuncture is a useful adjunct for stroke rehabilitation is encouraging but not compelling.

By 2001, more data had become available but the conclusion became even less encouraging: there is no compelling evidence to show that acupuncture is effective in stroke rehabilitation.

Finally, by 2010, there were 10 RCT and we were able to do a meta-analysis of the data. We concluded that our meta-analyses of data from rigorous randomized sham-controlled trials did not show a positive effect of acupuncture as a treatment for functional recovery after stroke.

Yes, my reviews were on slightly different research questions. Yet, they do reveal how a critical assessment of the slowly emerging evidence had to arrive at more and more negative conclusions about the role of acupuncture in the management of stroke patients. For a long time, this message was in stark contrast to what acupuncture-fans were claiming. I wonder whether they will now finally change their mind.

An announcement (it’s in German, I’m afraid) proudly declaring that ‘homeopathy fulfils the criteria of evidence-based medicine‘ caught my attention.

Here is the story:

In 2016, Dr. Melanie Wölk, did a ‘Master of Science’* at the ‘Donau University’ in Krems, Austria investigating the question whether homeopathy follows the rules of evidence-based medicine (EBM). She arrived at the conclusion that YES, IT DOES! This pleased the leading Austrian manufacturer of homeopathics (Dr Peithner) so much and so durably that, on 23 March 2018, he gave her a ‘scientific’ award (the annual Peithner award) for her ‘research’.

So far so good.

Her paper is unpublished, or at least not available on Medline; therefore, I am unable to evaluate it directly. All I know about it from the announcement is that she did her ‘research at the ‘Zentrum für Traditionelle Chinesische Medizin und Komplementärmedizin‘ of the said university. A quick Medline search revealed that this unit has never published anything, not a single paper, it seems! Disappointed I search for Dr. Christine Schauhuber, the leader of the unit; and again I find no Medline-listed publications in her name. My interim conclusion is thus that this institution might not be at the cutting edge of science.

But what do we know about Dr. Melanie Wölk’s award-winning master thesis *?

The announcement tells us that she investigated all RCTs published between 2010 and 2016. In addition, she evaluated:

On that basis, she arrived at her positive verdict – not just tentatively, but without doubt (“Das Ergebnis steht fest”).

Dr Peithner, the owner of the company and awarder of the prize, was quoted stating that this is a very important piece of work for homeopathy; it shows yet again what we see in our daily routine, namely that homeopathics are effective. Wölk’s investigation demonstrates furthermore that high-quality trials of homeopathy do exist, and that it is time to end the witch-hunt aimed at discrediting an effective therapy. Conventional medicine and homeopathy ought to finally work hand in hand – for the benefit of our patients. (“Für die Homöopathie ist das eine sehr wichtige Arbeit, die wieder zeigt, was wir in der ärztlichen Praxis täglich erleben, nämlich dass homöopathische Arzneimittel wirken. Wölks Untersuchung zeigt weiters deutlich, dass es sehr wohl hochqualitative Homöopathie-Studien gibt und es an der Zeit ist, die Hexenjagd zu beenden, mit der eine wirksame medizinische Therapie diskreditiert werden soll. Konventionelle Medizin und Homöopathie sollten endlich Hand in Hand arbeiten – zum Wohle der Patientinnen und Patienten.”)

I do hope that Dr Wölk uses the prize money (by no means a fortune; see photo) to buy some time for publishing her work (one of my teachers, all those years ago, used to say ‘unpublished research is no research’) so that we can all benefit from it. Until it becomes available, I should perhaps mention that the description of her methodology (publications between 2010 and 2016 [plus a few other papers that nicely fitted the arguments?]; including one Linde review and not his more recent re-analysis [see above]) does not inspire me to think that Dr Wölk’s research was anywhere near rigorous, systematic or complete. In the same vein, I am tempted to point out that the Swiss report is probably the very last document I would select, if I wanted to generate an objective picture about the value of homeopathy.

Taking all this into account, I conclude that we seem to be dealing here with a

  • pseudo-prize (given by a commercial firm to further its business) for a piece of
  • pseudo-research (the project seems to have been aimed to white-wash homeopathy) into
  • pseudo-medicine (a treatment that has been tested extensively but has not been shown to work beyond placebo).

*Wölk, Melanie: Eminenz oder Evidenz: Die Homöopathie auf dem Prüfstand der Evidence based Medicine. Masterarbeit zur Erlangung des akademischen Abschlusses Master of Science im Universitätslehrgang Natural Medicine. Donau-Universität Krems, Department für Gesundheitswissenschaften und Biomedizin. Krems, Mai 2016.

We all know that there is a plethora of interventions for and specialists in low back pain (chiropractors, osteopaths, massage therapists, physiotherapists etc., etc.); and, depending whether you are an optimist or a pessimist, each of these therapies is as good or as useless as the next. Today, a widely-publicised series of articles in the Lancet confirms that none of the current options is optimal:

Almost everyone will have low back pain at some point in their lives. It can affect anyone at any age, and it is increasing—disability due to back pain has risen by more than 50% since 1990. Low back pain is becoming more prevalent in low-income and middle-income countries (LMICs) much more rapidly than in high-income countries. The cause is not always clear, apart from in people with, for example, malignant disease, spinal malformations, or spinal injury. Treatment varies widely around the world, from bed rest, mainly in LMICs, to surgery and the use of dangerous drugs such as opioids, usually in high-income countries.

The Lancet publishes three papers on low back pain, by an international group of authors led by Prof Rachelle Buchbinder, Monash University, Melbourne, Australia, which address the issues around the disorder and call for worldwide recognition of the disability associated with the disorder and the removal of harmful practices. In the first paper, Jan Hartvigsen, Mark Hancock, and colleagues draw our attention to the complexity of the condition and the contributors to it, such as psychological, social, and biophysical factors, and especially to the problems faced by LMICs. In the second paper, Nadine Foster, Christopher Maher, and their colleagues outline recommendations for treatment and the scarcity of research into prevention of low back pain. The last paper is a call for action by Rachelle Buchbinder and her colleagues. They say that persistence of disability associated with low back pain needs to be recognised and that it cannot be separated from social and economic factors and personal and cultural beliefs about back pain.

Overview of interventions endorsed for non-specific low back pain in evidence-based clinical practice guidelines (Danish, US, and UK guidelines)

In this situation, it makes sense, I think, to opt for a treatment (amongst similarly effective/ineffective therapies) that is at least safe, cheap and readily available. This automatically rules out chiropractic, osteopathy and many others. Exercise, however, does come to mind – but what type of exercise?

The aim of this meta-analysis of randomized controlled trials was to gain insight into the effectiveness of walking intervention on pain, disability, and quality of life in patients with chronic low back pain (LBP) at post intervention and follow ups.

Six electronic databases (PubMed, Science Direct, Web of Science, Scopus, PEDro and The Cochrane library) were searched from 1980 to October 2017. Randomized controlled trials (RCTs) in patients with chronic LBP were included, if they compared the effects of walking intervention to non-pharmacological interventions. Pain, disability, and quality of life were the primary health outcomes.

Nine RCTs were suitable for meta-analysis. Data was analysed according to the duration of follow-up (short-term, < 3 months; intermediate-term, between 3 and 12 months; long-term, > 12 months). Low- to moderate-quality evidence suggests that walking intervention in patients with chronic LBP was as effective as other non-pharmacological interventions on pain and disability reduction in both short- and intermediate-term follow ups.

The authors concluded that, unless supplementary high-quality studies provide different evidence, walking, which is easy to perform and highly accessible, can be recommended in the management of chronic LBP to reduce pain and disability.

I know – this will hardly please the legions of therapists who earn their daily bread with pretending their therapy is the best for LBP. But healthcare is clearly not about the welfare of the therapists, it is/should be about patients. And patients should surely welcome this evidence. I know, walking is not always easy for people with severe LBP, but it seems effective and it is safe, free and available to everyone.

My advice to patients is therefore to walk (slowly and cautiously) to the office of their preferred therapist, have a little rest there (say hello to the staff perhaps) and then walk straight back home.

The plethora of dodgy meta-analyses in alternative medicine has been the subject of a recent post – so this one is a mere update of a regular lament.

This new meta-analysis was to evaluate evidence for the effectiveness of acupuncture in the treatment of lumbar disc herniation (LDH). (Call me pedantic, but I prefer meta-analyses that evaluate the evidence FOR AND AGAINST a therapy.) Electronic databases were searched to identify RCTs of acupuncture for LDH, and 30 RCTs involving 3503 participants were included; 29 were published in Chinese and one in English, and all trialists were Chinese.

The results showed that acupuncture had a higher total effective rate than lumbar traction, ibuprofen, diclofenac sodium and meloxicam. Acupuncture was also superior to lumbar traction and diclofenac sodium in terms of pain measured with visual analogue scales (VAS). The total effective rate in 5 trials was greater for acupuncture than for mannitol plus dexamethasone and mecobalamin, ibuprofen plus fugui gutong capsule, loxoprofen, mannitol plus dexamethasone and huoxue zhitong decoction, respectively. Two trials showed a superior effect of acupuncture in VAS scores compared with ibuprofen or mannitol plus dexamethasone, respectively.

The authors from the College of Traditional Chinese Medicine, Jinan University, Guangzhou, Guangdong, China, concluded that acupuncture showed a more favourable effect in the treatment of LDH than lumbar traction, ibuprofen, diclofenac sodium, meloxicam, mannitol plus dexamethasone and mecobalamin, fugui gutong capsule plus ibuprofen, mannitol plus dexamethasone, loxoprofen and huoxue zhitong decoction. However, further rigorously designed, large-scale RCTs are needed to confirm these findings.

Why do I call this meta-analysis ‘dodgy’? I have several reasons, 10 to be exact:

  1. There is no plausible mechanism by which acupuncture might cure LDH.
  2. The types of acupuncture used in these trials was far from uniform and  included manual acupuncture (MA) in 13 studies, electro-acupuncture (EA) in 10 studies, and warm needle acupuncture (WNA) in 7 studies. Arguably, these are different interventions that cannot be lumped together.
  3. The trials were mostly of very poor quality, as depicted in the table above. For instance, 18 studies failed to mention the methods used for randomisation. I have previously shown that some Chinese studies use the terms ‘randomisation’ and ‘RCT’ even in the absence of a control group.
  4. None of the trials made any attempt to control for placebo effects.
  5. None of the trials were conducted against sham acupuncture.
  6. Only 10 studies 10 trials reported dropouts or withdrawals.
  7. Only two trials reported adverse reactions.
  8. None of these shortcomings were critically discussed in the paper.
  9. Despite their affiliation, the authors state that they have no conflicts of interest.
  10. All trials were conducted in China, and, on this blog, we have discussed repeatedly that acupuncture trials from China never report negative results.

And why do I find the journal ‘dodgy’?

Because any journal that publishes such a paper is likely to be sub-standard. In the case of ‘Acupuncture in Medicine’, the official journal of the British Medical Acupuncture Society, I see such appalling articles published far too frequently to believe that the present paper is just a regrettable, one-off mistake. What makes this issue particularly embarrassing is, of course, the fact that the journal belongs to the BMJ group.

… but we never really thought that science publishing was about anything other than money, did we?

What an odd title, you might think.

Systematic reviews are the most reliable evidence we presently have!

Yes, this is my often-voiced and honestly-held opinion but, like any other type of research, systematic reviews can be badly abused; and when this happens, they can seriously mislead us.

new paper by someone who knows more about these issues than most of us, John Ioannidis from Stanford university, should make us think. It aimed at exploring the growth of published systematic reviews and meta‐analyses and at estimating how often they are redundant, misleading, or serving conflicted interests. Ioannidis demonstrated that publication of systematic reviews and meta‐analyses has increased rapidly. In the period January 1, 1986, to December 4, 2015, PubMed tags 266,782 items as “systematic reviews” and 58,611 as “meta‐analyses.” Annual publications between 1991 and 2014 increased 2,728% for systematic reviews and 2,635% for meta‐analyses versus only 153% for all PubMed‐indexed items. Ioannidis believes that probably more systematic reviews of trials than new randomized trials are published annually. Most topics addressed by meta‐analyses of randomized trials have overlapping, redundant meta‐analyses; same‐topic meta‐analyses may exceed 20 sometimes.

Some fields produce massive numbers of meta‐analyses; for example, 185 meta‐analyses of antidepressants for depression were published between 2007 and 2014. These meta‐analyses are often produced either by industry employees or by authors with industry ties and results are aligned with sponsor interests. China has rapidly become the most prolific producer of English‐language, PubMed‐indexed meta‐analyses. The most massive presence of Chinese meta‐analyses is on genetic associations (63% of global production in 2014), where almost all results are misleading since they combine fragmented information from mostly abandoned era of candidate genes. Furthermore, many contracting companies working on evidence synthesis receive industry contracts to produce meta‐analyses, many of which probably remain unpublished. Many other meta‐analyses have serious flaws. Of the remaining, most have weak or insufficient evidence to inform decision making. Few systematic reviews and meta‐analyses are both non‐misleading and useful.

The author concluded that the production of systematic reviews and meta‐analyses has reached epidemic proportions. Possibly, the large majority of produced systematic reviews and meta‐analyses are unnecessary, misleading, and/or conflicted.

Ioannidis makes the following ‘Policy Points’:

  • Currently, there is massive production of unnecessary, misleading, and conflicted systematic reviews and meta‐analyses. Instead of promoting evidence‐based medicine and health care, these instruments often serve mostly as easily produced publishable units or marketing tools.
  • Suboptimal systematic reviews and meta‐analyses can be harmful given the major prestige and influence these types of studies have acquired.
  • The publication of systematic reviews and meta‐analyses should be realigned to remove biases and vested interests and to integrate them better with the primary production of evidence.

Obviously, Ioannidis did not have alternative medicine in mind when he researched and published this article. But he easily could have! Virtually everything he stated in his paper does apply to it. In some areas of alternative medicine, things are even worse than Ioannidis describes.

Take TCM, for instance. I have previously looked at some of the many systematic reviews of TCM that currently flood Medline, based on Chinese studies. This is what I concluded at the time:

Why does that sort of thing frustrate me so much? Because it is utterly meaningless and potentially harmful:

  • I don’t know what treatments the authors are talking about.
  • Even if I managed to dig deeper, I cannot get the information because practically all the primary studies are published in obscure journals in Chinese language.
  • Even if I  did read Chinese, I do not feel motivated to assess the primary studies because we know they are all of very poor quality – too flimsy to bother.
  • Even if they were formally of good quality, I would have my doubts about their reliability; remember: 100% of these trials report positive findings!
  • Most crucially, I am frustrated because conclusions of this nature are deeply misleading and potentially harmful. They give the impression that there might be ‘something in it’, and that it (whatever ‘it’ might be) could be well worth trying. This may give false hope to patients and can send the rest of us on a wild goose chase.

So, to ease the task of future authors of such papers, I decided give them a text for a proper EVIDENCE-BASED conclusion which they can adapt to fit every review. This will save them time and, more importantly perhaps, it will save everyone who might be tempted to read such futile articles the effort to study them in detail. Here is my suggestion for a conclusion soundly based on the evidence, not matter what TCM subject the review is about:


On another occasion, I stated that 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.

In yet another post on the subject of systematic reviews, I wrote that if you have rubbish trials, you can produce a rubbish review and publish it in a rubbish journal (perhaps I should have added ‘rubbish researchers).

And finally this post about a systematic review of acupuncture: it is almost needless to mention that the findings (presented in a host of hardly understandable tables) suggest that acupuncture is of proven or possible effectiveness/efficacy for a very wide array of conditions. It also goes without saying that there is no critical discussion, for instance, of the fact that most of the included evidence originated from China, and that it has been shown over and over again that Chinese acupuncture research never seems to produce negative results.

The main point surely is that the problem of shoddy systematic reviews applies to a depressingly large degree to all areas of alternative medicine, and this is misleading us all.

So, what can be done about it?

My preferred (but sadly unrealistic) solution would be this:


Research is not fundamentally different from other professional activities; to do it well, one needs adequate training; and doing it badly can cause untold damage.

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