scientific misconduct

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Can intercessory prayer improve the symptoms of sick people?

Why should it? It’s utterly implausible!

Because the clinical evidence says so?

No, the current Cochrane review concluded that [the] findings are equivocal and, although some of the results of individual studies suggest a positive effect of intercessory prayer, the majority do not and the evidence does not support a recommendation either in favour or against the use of intercessory prayer. We are not convinced that further trials of this intervention should be undertaken and would prefer to see any resources available for such a trial used to investigate other questions in health care.

Yet, not all seem to agree with this; and some even continue to investigate prayer as a medical therpy.

For this new study (published in EBCAM), the Iranian investigators randomly assigned 92 patients in 2 groups to receive either 40 mg of propranolol twice a day for 2 month (group “A”) or 40 mg of propranolol twice a day for 2 months with prayer (group “B”). At the beginning of study and 3 months after intervention, patients’ pain was measured using the visual analogue scale.

All patients who participate in present study were Muslim. At the beginning of study and before intervention, the mean score of pain in patients in groups A and B were 5.7 ± 1.6 and 6.5 ± 1.9, respectively. According to results of independent t test, mean score of pain intensity at the beginning of study were similar between patients in 2 groups (P > .05). Three month after intervention, mean score of pain intensity decreased in patients in both groups. At this time, the mean scores of pain intensity were 5.4 ± 1.1 and 4.2 ± 2.3 in patients in groups A and B, respectively. This difference between groups was statistically significant (P < .001).


The above figure shows the pain score in patients before and after the intervention.

The authors concluded that the present study revealed that prayer can be used as a nonpharmacologic pain coping strategy in addition to pharmacologic intervention for this group of patients.

Extraordinary claims require extraordinary proof. This study is, in fact, extraordinary – but only in the sense of being extraordinarily poor, or at least it is extraordinary in its quality of reporting. For instance, all we learn in the full text article about the two treatments applied to the patient groups is this: “The prayer group participated in an 8-week, weekly, intercessory prayer program with each session lasting 45 minutes. Pain reduction was measured at baseline and after 3 months, by registered nurses who were specialist in pain management and did not know which patients were in which groups (control or intervention), using a visual analogue scale.”

Intercessory prayer is the act of praying on behalf of others. This mans that the patients receiving prayer might have been unaware of being ‘treated’. In this case, the patients could have been adequately blinded. But this is not made clear in the article.

More importantly perhaps, the authors fail to provide any numeric results. All that we are given is the above figure. It is not possible therefore to run any type of check on the data. We are simply asked to believe what the authors have written. I for one have great difficulties in doing so. All I do believe in relation to this article is that

  • the journal EBCAM is utter trash,
  • constantly publishing rubbish is unethical and a disservice to everyone,
  • prayer does not need further research of this nature,
  • and poor studies often generate false-positive findings.

This meta-analysis was performed “to ascertain the effectiveness of oral aloe vera consumption on the reduction of fasting blood glucose (FBG) and hemoglobin A1c (HbA1c).”

PubMed, CINAHL, Natural Medicines Comprehensive Database, and Natural Standard databases were searched. The searches were limited to clinical trials or observational studies conducted in humans and published in English. Studies of aloe vera’s effect on FBG, HbA1c, homeostasis model assessment-estimated insulin resistance (HOMA-IR), fasting serum insulin, fructosamine, and oral glucose tolerance test (OGTT) in prediabetic and diabetic populations were examined.

Nine studies were included in the FBG parameter (n = 283); 5 of these studies included HbA1c data (n = 89). Aloe vera decreased FBG by 46.6 mg/dL (p < 0.0001) and HbA1c by 1.05% (p = 0.004). Significant reductions of both endpoints were maintained in all subgroup analyses. Additionally, the data suggested that patients with an FBG ≥200 mg/dL may see a greater benefit. A mean FBG reduction of 109.9 mg/dL was observed in this population (p ≤ 0.0001). There was evidence of publication bias with FBG but not with HbA1c.

The authors concluded that the results of this meta-analysis support the use of oral aloe vera for significantly reducing both FBG (46.6 mg/dL) and HbA1c (1.05%) in prediabetic and diabetic patients. However, given the current overall quality and relative scarcity of data, further clinical studies that are more robust and better controlled are warranted to confirm and further explore these findings.

Oh no, the results do not support the use of aloe vera at all!!


Because this ‘meta-analysis’ is of unacceptably poor quality. Here are just some of the flaws that render it totally useless, particularly for issuing advice such as above:

  • The authors included uncontrolled observational studies which make no attempt to control for non-specific effects.
  • In several studies, the use of concomitant anti-diabetic medications was allowed; therefore it is not possible to establish cause and effect by aloe vera.
  • The search strategy was woefully inadequate; for instance non-English publications were not considered.
  • There was no assessment of the scientific rigor of the included studies; this totally invalidates the reliably of the conclusions.
  • The included studies used preparations of widely different aloe vera preparations, and there is no way of knowing the does of the active ingredients.

Diabetes is a serious condition that affects millions worldwide. If some of these patients are sufficiently gullible to follow the conclusions of this paper, they might be dead within a matter of days. This makes this article one of the most dangerous papers that I have seen in the ‘peer-reviewed’ literature of alternative medicine.

Who publishes such utter and irresponsible rubbish?

You may well ask.

The journal has been discussed on this blog  before for the junk that regularly appears in its pages, and so has its editor in chief. The authors (and the reviewers) are not known to me, but one thing is for sure: they don’t know the first thing about conducting a decent systematic review/meta-analysis.

The common cold is one of the indications for which homeopathy is deemed to be effective… by homeopaths that is! Non-homeopaths are understandably critical about this claim, not least because there is no good evidence for it. But, hold on, there is a new study which might change all this.

This study was recently published in COMPLEMENTARY THERAPIES IN MEDICINE which is supposed to be one of the better journals in this area. According to its authors, it was conducted “to determine if a homeopathic syrup was effective in treating cold symptoms in preschool children.” Children diagnosed with an upper respiratory tract infection were randomized to receive a commercial homeopathic cold syrup containing allium cepa 6X, hepar sulf calc 12X, natrum muriaticum 6X, phosphorous 12X, pulsatilla 6X, sulphur 12X, and hydrastasis 6X or placebo. Parents administered the study medication as needed for 3 days. The primary outcome was change in symptoms one hour after each dose. Parents also assessed the severity of each of the symptoms of runny nose, cough, congestion and sneezing at baseline and twice daily for 3 days, using a 4-point rating scale. A composite cold score was calculated by combining the values for each of the four symptoms. Among 261 eligible participants, data on 957 doses of study medication in 154 children were analyzed. There was no significant difference in improvement one hour after the dose for any symptom between the two groups. Analysis of twice daily data on the severity of cold symptoms compared to baseline values found that improvements in sneezing, cough and the composite cold score were significantly greater at both the first and second assessments among those receiving the cold syrup compared to placebo recipients.

The authors concluded that the homeopathic syrup appeared to be effective in reducing the severity of cold symptoms in the first day after beginning treatment.

Where to start? There are so many problems with this study that I find it difficult to chose the most crucial ones:

  • The study had a clearly defined primary endpoint; it was not affected by the homeopathic treatment which doubtlessly makes the study a negative trial. The only correct conclusion therefore is that THE HOMEOPATHIC SYRUP FAILED TO AFFECT THE PRIMARY OUTCOME MEASURE OF THIS STUDY. THEREFORE THE TRIAL DID NOT PRODUCE ANY EVIDENCE TO ASSUME THAT THE EXPERIMENTAL TREATMENT WAS EFFICACIOUS.
  • I don’t think that many of the primary or secondary outcome measures are validated or reliable.
  • All the positive results reported in the abstract and the article relate to secondary endpoints which are purely explanatory by nature. They should, in my view, not be mentioned in the conclusions at all.
  • The fact that some results turned out to be positive can be explained by the fact that the investigators ran dozens of tests for statistical significance which means that, by simple chance, some will turn out to produce a positive result.
  • A further explanation for the seemingly positive results might be the fact disclosed in the text of the article that the children in the homeopathy group received more conventional drugs than those in the placebo group.
  • Whatever the reason for these positive results, they certainly had nothing to do with the homeopathic syrup.
  • The study was funded by the company producing the syrup and for which one of the authors was employed as a consultant. This might be an explanation for the abominably poor science. In other words, this paper is not an exercise in testing a hypothesis but one in marketing.

While I might forgive the company for trying to maximise their sales figures, I do find it harder to forgive the authors, reviewers and editors for publishing such overtly false conclusions. In my view, they are all guilty of scientific misconduct.

This randomized, double-blind study evaluated the efficacy of a homeopathic treatment in preventing excessive weight gain during pregnancy in overweight or obese women who were suspected of having a common mental disorder. For the homeopathic group (n=62), 9 homeopathic remedies were pre-selected: (1) Pulsatilla nigricans, (2) Sepia succus, (3) Lycopodium clavatum, (4) sulphur, (5) Lachesis trigonocephalus, (6) Nux vomica, (7) Calcarea carbonica, (8) phosphorus; and (9) Conium maculatum. From those 9 drugs, one was prioritized for administration for each participant. After the first appointment, a re-selection or selection of a new, more appropriate drug occurred, using the list of preselected drugs. The dosage was 6 drops orally 2 ×/day, in the morning and at night, on 4 consecutive days each week, with an interval of 3 d between doses, up until the next appointment medical appointment. The control group (n=72) took placebos. Both groups also received a diet orientation.

Weight change during pregnancy was defined as the difference between the body mass index (BMI) at the initial evaluation and that recorded at the final evaluation, adjusted for 40 weeks of gestation. In addition, the APGAR index in the newborn  (a measure of the health of the baby) was evaluated. The mean variation between baseline BMI and BMI at week 40 of gestation was +4.95 kg/m2 in the control group and +5.05 kg/m2 in the homeopathy group. The difference between the two groups was not significant. APGAR 10 at 5 min (59.6% in the homeopathy group and 36.4% in the control group) was statistically significant (P = .016).

The authors concluded that homeopathy does not appear to prevent excessive body mass gain in pregnant women who are overweight or obese and suspected of having a common mental disorder. Homeopathy did not change the APGAR score to modified clinical attention at delivery room. However, the evidence observed at APGAR 10 at minute 5 suggests that  homeopathy had a modulating effect on the vitality of newborns, warranting further studies designed to investigate it.

I have seen many odd studies in my time, but this must be one of the oddest?

  • What is the rationale for assuming that homeopathy might affect body weight?
  • Why take pregnant women with a weight problem who were suspected of having a common mental disorder?
  • Why try to turn a clearly negative result into a finding that is (at least partly) positive?

The last point seems the most important one to me. The primary outcome measure of this study (weight gain) was clearly defined and was not affected by the therapy. Yet the authors feel it justified to add to their conclusions that homeopathy had a modulating effect on the vitality of newborns (almost certainly nothing but a chance finding).

Are they for real?

I suppose they are: they are real pseudo-scientific promoters of quackery!

Dietary and herbal supplements (DHS) are currently popular. They are being promoted as being natural and therefore safe – an assumption that is clearly wrong: some DHS can contain toxic substances or they might cause interactions with drugs or other DHS.

This study explored whether adverse events were actually associated with such interactions and examined specific characteristics among inpatient DHS users prone to such adverse events. It was designed as a cross-sectional survey of 947 patients hospitalized in 12 departments of a tertiary academic medical centre in Haifa, Israel. It evaluated the rate of DHS use among inpatients, the potential for interactions, and actual adverse events during hospitalization associated with DHS use. It also assessed whether DHS consumption was documented in patients’ medical files. Statistical analysis was used to delineate DHS users at risk for adverse events associated with interactions with conventional drugs or other DHS.

The results show that about half of all patients took DHS. In 17 (3.7%) of the 458 DHS users, an adverse event may have been caused by DHS-drug-DHS interactions. According to the Drug Interaction Probability Scale, 14 interactions “probably” caused the adverse events, and 11 “possibly” caused them. Interactions occurred more frequently in older patients (p = 0.025, 95% CI: 2.26-19.7), patients born outside Israel (p = 0.025, 95% CI: 0.03-0.42), those with ophthalmologic (p = 0.032, 95% CI: 0.02-0.37) or gastrointestinal (p = 0.008, 95% CI: 0.05-0.46) comorbidities, and those using higher numbers of DHS (p < 0.0001, 95% CI: 0.52-2.48) or drugs (p = 0.027, 95% CI: 0.23-3.77).

The authors concluded that approximately one in 55 hospitalizations in this study may have been caused by adverse events associated with DHS-drug-DHS interactions. To minimize the actual occurrence of adverse events, medical staff education regarding DHS should be improved.

This seems to be a good study and it generated interesting findings on an important topic.

Why do I have nevertheless a problem with it?

The answer is simple but not pleasant: very similar results have been published almost simultaneously in more than one journal. The link above is to an article in the BR J CLIN PHARMACOL of October this year. The following text is from the abstract of an article in INTERN EMERG MED also of October this year:

Of 927 patients who agreed to answer the questionnaire, 458 (49.4 %) reported the use of 89 different DHS. Potential DHS-DHS interactions were identified in 12.9 % of DHS users. Three interactions were associated with the actual occurrence of adverse events. Patients at risk of DHS-DHS interactions included females (p = 0.026) and patients with greater numbers of concomitant medications (p < 0.0001) and of consumed DHS (p < 0.0001). In 88.9 % of DHS users, DHS use was not reported in medical files and only 18 % of the DHS involved in interactions were documented. Potential DHS-DHS interactions are common in inpatients, and may lead to hospitalization or worsen existing medical conditions. The causal relationship between potential interactions and actual adverse events requires further study.


And to my surprise, I also found a third article also from the October issue of INTERN EMERG MED reporting on this survey. Here is part of its abstract:

DHS users were determined via a questionnaire. The Natural Medicine database was used to search for potential DHS-drug interactions for identified DHS, and the clinical significance was evaluated using Lexi-interact online interaction analysis. Medical files were assessed for documentation of DHS use. Univariate and multivariate logistic regression analyses were used to characterize potential risk factors for DHS-drug interactions. Of 927 patients consenting to answer the questionnaire, 458 (49 %) reported DHS use. Of these, 215 (47 %) had at least one potential interaction during hospitalization (759 interactions). Of these interactions, 116 (15 %) were potentially clinically significant. Older age [OR = 1.02 (1.01-1.04), p = 0.002], males [OR = 2.11 (1.35-3.29), p = 0.001] and increased number of used DHS [OR = 4.28 (2.28-8.03), p < 0.001] or drugs [OR = 1.95 (1.17-3.26), p = 0.011] were associated with potential interactions in DHS users. Physicians documented only 16.5 % of DHS involved in these interactions in patients’ medical files. In conclusion, a substantial number of inpatients use DHS with potential interactions with concomitant medications. Medical staff should be aware of this, question patients on DHS usage and check for such interactions.


What is the difference between the three articles? The first one in INTERN EMERG MED authored by Levy I, Attias S, Ben Arye E, Goldstein L, Schiff E evaluated “potential DHS-DHS interactions among inpatients”. The second one in INTERN EMERG MED also authored by Levy I, Attias S, Ben Arye E, Goldstein L, Schiff E evaluated “potentially dangerous interactions of DHS with prescribed medications among inpatients”. Finally the one in BR J CLIN PHARMACOL also authored by Levy I, Attias S, Ben-Arye E, Goldstein L, Schiff E  assessed in addition the interactions between DHS and prescription drugs.

Dual publications are usually considered to be a violation of research ethics. Publication of different aspects of one single data-set in multiple articles is called ‘salami-slicing’ and is often considered to be poor form.

My question to you, the reader of this post, is: What type of scientific misconduct do we have here?

On 25 and 26 May of this year I wrote two posts about an acupuncture trial that, in my view, was dodgy. To refresh your memory, here is the relevant part of the 2nd post:

This new study was designed as a randomized, sham-controlled trial of acupuncture for persistent allergic rhinitis in adults investigated possible modulation of mucosal immune responses. A total of 151 individuals were randomized into real and sham acupuncture groups (who received twice-weekly treatments for 8 weeks) and a no acupuncture group. Various cytokines, neurotrophins, proinflammatory neuropeptides, and immunoglobulins were measured in saliva or plasma from baseline to 4-week follow-up.

Statistically significant reduction in allergen specific IgE for house dust mite was seen only in the real acupuncture group. A mean (SE) statistically significant down-regulation was also seen in pro-inflammatory neuropeptide substance P (SP) 18 to 24 hours after the first treatment. No significant changes were seen in the other neuropeptides, neurotrophins, or cytokines tested. Nasal obstruction, nasal itch, sneezing, runny nose, eye itch, and unrefreshed sleep improved significantly in the real acupuncture group (post-nasal drip and sinus pain did not) and continued to improve up to 4-week follow-up.

The authors concluded that acupuncture modulated mucosal immune response in the upper airway in adults with persistent allergic rhinitis. This modulation appears to be associated with down-regulation of allergen specific IgE for house dust mite, which this study is the first to report. Improvements in nasal itch, eye itch, and sneezing after acupuncture are suggestive of down-regulation of transient receptor potential vanilloid 1.

…the trial itself raises a number of questions:

  1. Which was the primary outcome measure of this trial?
  2. What was the power of the study, and how was it calculated?
  3. For which outcome measures was the power calculated?
  4. How were the subjective endpoints quantified?
  5. Were validated instruments used for the subjective endpoints?
  6. What type of sham was used?
  7. Are the reported results the findings of comparisons between verum and sham, or verum and no acupuncture, or intra-group changes in the verum group?
  8. What other treatments did each group of patients receive?
  9. Does anyone really think that this trial shows that “acupuncture is a safe, effective and cost-effective treatment for allergic rhinitis”?

In the comments section, the author wrote: “after you have read the full text and answered most of your questions for yourself, it might then be a more appropriate time to engage in any meaningful discussion, if that is in fact your intent”, and I asked him to send me his paper. As he does not seem to have the intention to do so, I will answer the questions myself and encourage everyone to have a close look at the full paper [which I can supply on request].

  1. The myriad of lab tests were defined as primary outcome measures.
  2. Two sentences are offered, but they do not allow me to reconstruct how this was done.
  3. No details are provided.
  4. Most were quantified with a 3 point scale.
  5. Mostly not.
  6. Needle insertion at non-acupoints.
  7. The results are a mixture of inter- and intra-group differences.
  8. Patients were allowed to use conventional treatments and the frequency of this use was reported in patient diaries.
  9. I don’t think so.

So, here is my interpretation of this study:

  • It lacked power for many outcome measures, certainly the clinical ones.
  • There were hardly any differences between the real and the sham acupuncture group.
  • Most of the relevant results were based on intra-group changes, rather than comparing sham with real acupuncture, a fact, which is obfuscated in the abstract.
  • In a controlled trial fluctuations within one group must never be interpreted as caused by the treatment.
  • There were dozens of tests for statistical significance, and there seems to be no correction for multiple testing.
  • Thus the few significant results that emerged when comparing sham with real acupuncture might easily be false positives.
  • Patient-blinding seems questionable.
  • McDonald as the only therapist of the study might be suspected to have influenced his patients through verbal and non-verbal communications.

I am sure there are many more flaws, particularly in the stats, and I leave it to others to identify them. The ones I found are, however, already serious enough, in my view, to call for a withdrawal of this paper. Essentially, the authors seem to have presented a study with largely negative findings as a trial with positive results showing that acupuncture is an effective therapy for allergic rhinitis. Subsequently, McDonald went on social media to inflate his findings even more. One might easily ask: is this scientific misconduct or just poor science?


This and the previous post created lots of discussion and comments. However, the question whether the study in question amounted to scientific misconduct was never satisfactorily resolved. Therefore, I decided to write to the editor of ‘Ann Allergy Asthma Immunol‘ where the trial had been published. He answered by saying I would need to file an official complaint for him to address the issue. On 13 June, I therefore sent him the following email:

Thank you for your letter of 3/6/2016 suggesting I make a formal complaint about the paper entitled ‘EFFECT OF ACUPUNCTURE ON HOUSE DUST MITE…’ [ Ann Allergy Asthma Immunol 2016] by McDonald et al. I herewith wish to file such a complaint.

The article in question reports an RCT of acupuncture for persistent allergic rhinitis. It followed a parallel group design with 3 groups receiving the following interventions:

1.       Acupuncture

2.       Sham-acupuncture

3.       No treatment

There was a plethora of outcome measures and time points on which they were measured. A broad range of parameters was defined as primary endpoints.

The conclusion reached by the authors essentially was that acupuncture affected several outcome measures in a positive sense, thus supporting the notion that acupuncture is efficacious [“Symptoms and quality of life improved significantly and were still continuing to improve 4 weeks after treatment ceased.”] This conclusion, however, is misleading and needs correcting.

The main reasons for this are as follows:

·         Despite the fact that the authors did many dozens of statistical tests for significance, they did not correct for this multiplicity of tests. Consequently, some or most of the significant results are likely to be false positive.

·         Many of the positive results of this paper were not obtained by comparing one group to another but by doing before/after comparisons within one group. This approach defies the principle of a controlled clinical trial. For doing intra-group comparisons, we obviously do not need any control group at all. The findings from intra-group comparisons are prominently reported in the paper, for instance in the abstract, giving the impression that they originate from inter-group comparisons. One has to read the paper very carefully to find that, when inter-group comparisons were conducted, their results did NOT confirm the findings from the reported intra-group comparisons. As this is the case for most of the symptomatic endpoints, the impression given is seriously misleading and needs urgent correction.

On the whole, the article is a masterpiece of obfuscation and misrepresentation of the actual data. I urge you to consider the harm than can be done by such a misleading publication. In my view, the best way to address this problem is to withdraw the article.

I look forward to your decision.


E Ernst


I had to send several reminders but my most recent one prompted the following response dated 7/11/ 2016:

Dear Professor Ernst,
Thank you for your patience while we worked through the process of considering your complaints levied on the article entitled ‘EFFECT OF ACUPUNCTURE ON HOUSE DUST MITE…’ [ Ann Allergy Asthma Immunol 2016] by McDonald et al. I considered the points that you made in your previous letter, sought input from our editorial team (including our biostatistics editor) , our publisher and the authors themselves. I sent the the  charges ( point by point) anonymously to the authors and allowed them time to respond which they did. I had their responses reviewed by selected editors and , as a result of this process, have decided not to pursue any corrective or punitive action based upon the following :
  1. Our editorial team recognizes that this is not the best clinical trial we have published in the Annals of Allergy, Asthma and Immunology. However, neither is is the worst. As in most published research studies, there are always things that could have been done better to make it a stronger paper. Never-the-less, the criticism falls fall short of any sort of remedy that would include withdrawal of the manuscript.
  2. Regarding your accusation that the multiple positive endpoint resulted in the authors making specific therapeutic claims, our assessment is that no specific therapeutic claim was made but rather the authors maintained that the data support the value of acupuncture in improving symptoms and quality of life in patients with AR. We do not believe there was overreach in those statements.
  3. The authors’ stated intent was to show immune changes associated with clinical markers of improvement in the active acupuncture group compared to controls. The authors maintain (and our editors agree) that their data assessments were primarily based upon three statistical tests not “dozens” (as stated in your original letter of complaint).  The power analysis and sample size calculations were presented to us and deemed adequate , making the probability of a type I error quite low.
  4. The authors acknowledge in their paper that there could be limitations to their data interpretation based upon potential disparities between intra- and intergroup comparisons. The editors felt their transparency was adequately disclosed.
In summary, as editor-in-chief of the Annals of Allergy, Asthma and Immunology, I did not find sufficient merit in your charges to initiate any corrective or punitive action for this manuscript. I understand you will strongly disagree with this decision and I regret that. However, in the final analysis, my primary intent is to preserve the objectivity, fairness, and integrity of our journal and its review process. I believe I have accomplished that in this instance.
This seems to settle the issue: the study in question does not involve scientific misconduct!
Or does it?
I would be grateful for the view of the readers of this post.

I have warned you before to be sceptical about Chinese studies. This is what I posted on this blog more than 2 years ago, for instance:

Imagine an area of therapeutics where 100% of all findings of hypothesis-testing research are positive, i.e. come to the conclusion that the treatment in question is effective. Theoretically, this could mean that the therapy is a miracle cure which is useful for every single condition in every single setting. But sadly, there are no miracle cures. Therefore something must be badly and worryingly amiss with the research in an area that generates 100% positive results.

Acupuncture is such an area; we and others have shown that Chinese trials of acupuncture hardly ever produce a negative finding. In other words, one does not need to read the paper, one already knows that it is positive – even more extreme: one does not need to conduct the study, one already knows the result before the research has started. But you might not believe my research nor that of others. We might be chauvinist bastards who want to discredit Chinese science. In this case, you might perhaps believe Chinese researchers.

In this systematic review, all randomized controlled trials (RCTs) of acupuncture published in Chinese journals were identified by a team of Chinese scientists. A total of 840 RCTs were found, including 727 RCTs comparing acupuncture with conventional treatment, 51 RCTs with no treatment controls, and 62 RCTs with sham-acupuncture controls. Among theses 840 RCTs, 838 studies (99.8%) reported positive results from primary outcomes and two trials (0.2%) reported negative results. The percentages of RCTs concealment of the information on withdraws or sample size calculations were 43.7%, 5.9%, 4.9%, 9.9%, and 1.7% respectively.

The authors concluded that publication bias might be major issue in RCTs on acupuncture published in Chinese journals reported, which is related to high risk of bias. We suggest that all trials should be prospectively registered in international trial registry in future.


Now an even more compelling reason emerged for taking evidence from China with a pinch of salt:

A recent survey of clinical trials in China has revealed fraudulent practice on a massive scale. China’s food and drug regulator carried out a one-year review of clinical trials. They concluded that more than 80 percent of clinical data is “fabricated“. The review evaluated data from 1,622 clinical trial programs of new pharmaceutical drugs awaiting regulator approval for mass production. Officials are now warning that further evidence malpractice could still emerge in the scandal.
According to the report, much of the data gathered in clinical trials are incomplete, failed to meet analysis requirements or were untraceable. Some companies were suspected of deliberately hiding or deleting records of adverse effects, and tampering with data that did not meet expectations.

“Clinical data fabrication was an open secret even before the inspection,” the paper quoted an unnamed hospital chief as saying. Contract research organizations seem have become “accomplices in data fabrication due to cutthroat competition and economic motivation.”

A doctor at a top hospital in the northern city of Xian said the problem doesn’t lie with insufficient regulations governing clinical trials data, but with the failure to implement them. “There are national standards for clinical trials in the development of Western pharmaceuticals,” he said. “Clinical trials must be carried out in three phases, and they must be assessed at the very least for safety,” he said. “But I don’t know what happened here.”

Public safety problems in China aren’t limited to the pharmaceutical industry and the figure of 80 percent is unlikely to surprise many in a country where citizens routinely engage in the bulk-buying of overseas-made goods like infant formula powder. Guangdong-based rights activist Mai Ke said there is an all-pervasive culture of fakery across all products made in the country. “It’s not just the medicines,” Mai said. “In China, everything is fake, and if there’s a profit in pharmaceuticals, then someone’s going to fake them too.” He said the problem also extends to traditional Chinese medicines, which are widely used in conjunction with Western pharmaceuticals across the healthcare system.
“It’s just harder to regulate the fakes with traditional medicines than it is with Western pharmaceuticals, which have strict manufacturing guidelines,” he said.

According to Luo, academic ethics is an underdeveloped field in China, leading to an academic culture that is accepting of manipulation of data. “I don’t think that the 80 percent figure is overstated,” Luo said.

And what should we conclude from all this?

I find it very difficult to reach a verdict that does not sound hopelessly chauvinistic but feel that we have little choice but to distrust the evidence that originates from China. At the very minimum, I think, we must scrutinise it thoroughly; whenever it looks too good to be true, we ought to discard it as unreliable and await independent replications.

Some osteopaths – similar to their chiropractic, naturopathic, homeopathic, etc. colleagues – claim they can treat almost any condition under the sun. Even gynaecological ones? Sure! But is the claim true? Let’s find out.

The aim of this recent review was to evaluate the effects of the osteopathic manipulative treatment (OMT) on women with gynaecological and obstetric disorders. An extensive search from inception to April 2014 was conducted on MEDLINE, Embase, the Cochrane library using MeSH and free terms. Clinical studies investigating the effect of OMT in gynaecologic and obstetric conditions were included as well as unpublished works. Reviews and personal contributions were excluded. Studies were screened for population, outcome, results and adverse effects by two independent reviewers using an ad-hoc data extraction form. The high heterogeneity of the studies led to a narrative review.

In total, 24 studies were included. They addressed the following conditions: back pain and low back functioning in pregnancy, pain and drug use during labor and delivery, infertility and subfertility, dysmenorrhea, symptoms of (peri)menopause and pelvic pain. Overall, OMT was considered to be effective for pregnancy related back pain. For all other gynaecological and obstetrical conditions the evidence was considered to be uncertain. Only three studies mentioned adverse events after OMT.

The authors concluded that, although positive effects were found, the heterogeneity of study designs, the low number of studies and the high risk of bias of included trials prevented any indication on the effect of osteopathic care. Further investigation with more pragmatic methodology, better and detailed description of interventions and systematic reporting of adverse events are recommended in order to obtain solid and generalizable results.

Given the fact that the lead authors of this review come from the “Accademia Italiana Osteopatia Tradizionale, Pescara, Italy, we can probably answer the question in the title of this blog with a straight NO. I see no reason why OMT should work for gynaecological conditions, and I am not in the least surprised to read that there is no clinical evidence for this notion. Sadly, this is unlikely to stop osteopaths to claim otherwise and continue to prey on the desperate and the gullible.

One might thus say that this review is totally unremarkable – but I would beg to differ: it highlights yet again one very important finding, namely the fact that trials of alternative therapies far too often fail to report adverse effects. I have stated this often already, but I will say it again: THIS OMISSION IS A VIOLATION OF RESEARCH ETHICS WHICH GIVES US A FALSE POSITIVE OVERALL PICTURE OF THE RISKS ASSOCIATED WITH ALTERNATIVE MEDICINE.


Deepak Chopra rarely publishes in medical journals (I suppose, he has better things to do). I was therefore intrigued when I saw a recent article of which he is a co-author.

The ‘study‘ in question allegedly examined the effects of a comprehensive residential mind–body program on well-being. The authors describe it as “a quasi-randomized trial comparing the effects of participation in a 6-day Ayurvedic system of medicine-based comprehensive residential program with a 6-day residential vacation at the same retreat location.” They included 69 healthy women and men who received the Ayurvedic intervention addressing physical and emotional well-being through group meditation and yoga, massage, diet, adaptogenic herbs, lectures, and journaling. Key components of the program include physical cleansing through ingestion of herbs, fiber, and oils that support the body’s natural detoxification pathways and facilitate healthy elimination; two Ayurvedic meals daily (breakfast and lunch) that provide a light plant-based diet; daily Ayurvedic oil massage treatments; and heating treatments through the use of sauna and/or steam. The program includes lectures on Ayurvedic principles and lifestyle as well as lectures on meditation and yoga philosophy. The study group also participated in twice-daily group meditation and daily yoga and practiced breathing exercises (pranayama) as well as emotional expression through a process of journaling and emotional support. During the program, participants received a 1-hour integrative medical consultation with a physician and follow-up with an Ayurvedic health educator.

The control group simply had a vacation without any of the above therapies in the same resort. They were asked to do what they would normally do on a resort vacation with the additional following restrictions: they were asked not to engage in more exercise than they would in their normal lifestyle and to refrain from using La Costa Resort spa services. They were also asked not to drink ginger tea or take Gingko biloba during the 2 days before and during the study week.

Recruitment was via email announcements on the University of California San Diego faculty and staff and Chopra Center for Wellbeing list-servers. Study flyers stated that the week-long Self-Directed Biological Transformation Initiative (SBTI) study would be conducted at the Chopra Center for Wellbeing, located at the La Costa Resort in Carlsbad, California, in order to learn more about the psychosocial and physiologic effects of the 6-day Perfect Health (PH) Program compared with a 6-day stay at the La Costa Resort. The study participants were not blinded, and site investigators and study personnel knew to which group participants were assigned.

Participants in the Ayurvedic program showed significant and sustained increases in ratings of spirituality and gratitude compared with the vacation group, which showed no change. The Ayurvedic participants also showed increased ratings for self-compassion as well as less anxiety at the 1-month follow-up.

The authors arrived at the following conclusion: Findings suggest that a short-term intensive program providing holistic instruction and experience in mind–body healing practices can lead to significant and sustained increases in perceived well-being and that relaxation alone is not enough to improve certain aspects of well-being.

This ‘study’ had ethical approval from the University of California San Diego and was supported by the Fred Foundation, the MCJ Amelior Foundation, the National Philanthropic Trust, the Walton Family Foundation, and the Chopra Foundation. The paper’s first author is director of research at the Chopra Foundation. Deepak Chopra is the co-founder of The Chopra Center for Wellbeing.

Did I promise too much?

Isn’t this paper hilarious?

Just for the record, let me formulate a short conclusion that actually fits the data from this ‘study’: Lots of TLC, attention and empathy does make some people feel better.

This is hardly something one needs to write home about; and certainly nothing to do a study on!

But which journal would publish such unadulterated advertising?

On this blog, I have mentioned the JACM several times before. Recently, I wrote about the new man in charge of it. I concluded stating WATCH THIS SPACE.

I think the wait is now over – this paper is from the latest issue of the JACM, and I am sure we all agree that the new editor has just shown us of what he is made and where he wants to take his journal.

Just as I thought that this cannot get any better, it did! It did so in the form of a second paper which is evidently reporting from the same ‘study’. Here is its abstract unaltered in its full beauty:

The effects of integrative medicine practices such as meditation and Ayurveda on human physiology are not fully understood. The aim of this study was to identify altered metabolomic profiles following an Ayurveda-based intervention. In the experimental group, 65 healthy male and female subjects participated in a 6-day Panchakarma-based Ayurvedic intervention which included herbs, vegetarian diet, meditation, yoga, and massage. A set of 12 plasma phosphatidylcholines decreased (adjusted p < 0.01) post-intervention in the experimental (n = 65) compared to control group (n = 54) after Bonferroni correction for multiple testing; within these compounds, the phosphatidylcholine with the greatest decrease in abundance was PC ae C36:4 (delta = -0.34). Application of a 10% FDR revealed an additional 57 metabolites that were differentially abundant between groups. Pathway analysis suggests that the intervention results in changes in metabolites across many pathways such as phospholipid biosynthesis, choline metabolism, and lipoprotein metabolism. The observed plasma metabolomic alterations may reflect a Panchakarma-induced modulation of metabotypes. Panchakarma promoted statistically significant changes in plasma levels of phosphatidylcholines, sphingomyelins and others in just 6 days. Forthcoming studies that integrate metabolomics with genomic, microbiome and physiological parameters may facilitate a broader systems-level understanding and mechanistic insights into these integrative practices that are employed to promote health and well-being.

Now that I managed to stop laughing about the first paper, I am not just amused but also puzzled by the amount of contradictions the second article seems to cause. Were there 65 or 69 individuals in the experimental group? Was the study randomised, quasi-randomised or not randomised? All of these versions are implied at different parts of the articles. It turns out that they randomised some patients, while allocating others without randomisation – and this clearly means the study was NOT randomised. Was the aim of the study ‘to identify altered metabolomic profiles following an Ayurveda-based intervention’ or ‘to examine the effects of a comprehensive residential mind–body program on well-being’?

I am sure that others will find further contradictions and implausibilites, if they look hard enough.

The funniest inconsistency, in my opinion, is that Deepak Chopra does not even seem to be sure to which university department he belongs. Is it the ‘Department of Family Medicine and Public Health, University of California, San Diego, La Jolla, CA.’ as indicated in the 1st paper or is it the ‘Department of Family and Preventive Medicine, University of California San Diego, La Jolla, California, USA’ as listed in the 2nd article?

Does he know from which planet he is?


It would be easy to continue this series on ‘tricks of the trade’ for quite a while. But this might get boring, and I have therefore decided to call it a day. So here is the last instalment (feel free to post further tricks that you may know of [in the comments section below]):


It is almost inevitable that, sooner or later, someone will object to some aspect of alternative medicine. In all likelihood, his or her arguments are rational and based on evidence. If that happens, the practitioner has several options to save his bacon (and income). One of the easiest and most popular is to claim that “of course, you cannot agree with me because you do not understand!”

The practitioner now needs to explain that, in order to achieve the level of expertise he has acquired, one has to do much more than to rationalise or know about science. In fact, one has to understand the subject on a much deeper level. One has to immerse oneself into it, open one’s mind completely and become a different human being altogether. This cannot be achieved by scientific study alone; it requires years of meditative work. And not everyone has the ability to go down this difficult path. It takes a lot of energy, insight and vision to become a true healer. A true Deepak Chopra is not born but trained through hard work, dedication and concentration.

Critics who disagree are really to be pitied. They fail to exist on quite the same level as those who ‘are in the know’. Therefore one must not get annoyed with those who disagree, they cannot understand because they have not seen the light.

My advice is to start thinking critically and read up about the NO TRUE SCOTSMAN FALLACY; this will quickly enable you to look beyond the charisma of these gurus and expose their charlatanry to the full.


Some critics stubbornly insist on evidence for the therapeutic claims made by quacks. That attitude can be awkward for the alternative practitioner – because usually there is no good evidence.

Cornered in this way, quacks often come up with a simple but effective conspiracy theory: the research has been done and it has produced fabulous results, but it has been supressed by… well, by whoever comes to mind. Usually BIG PHARMA or ‘the scientific establishment’ have to be dragged out into the frame again.

According to this theory, the pharmaceutical industry (or whoever comes in handy) was so shaken by the findings of the research that they decided to make it disappear. They had no choice, really; the alternative therapy in question was so very effective that it would have put BIG PHARMA straight out of business for ever. As we all know BIG PHARMA to be evil to the core, they had no ethical or moral qualms about committing such a crime to humanity. Profits must come before charity!

My advice is to explain to such charlatans that such conspiracy theories do, in fact, merely prove is that the quack’s treatment is not effective against their prosecution complex.


If  critics of alternative medicine become threatening to the quackery trade, an easy and much-used method is to discredit them by spreading lies about them. If the above-mentioned ploy “they cannot understand” fails to silence the nasty critics, the next step must be to claim they are corrupt. Why else would they spend their time exposing quackery?

Many people – alternative practitioners included – can only think of financial motivations; the possibility that someone might do a job for altruistic reasons does not occur to them. Therefore, it sounds most plausible that the critics of alternative medicine are doing it for money – after all, the quacks also quack for money.

My advice to potential users of alternative medicine who are confused by such allegations: do your own research and find out for yourself who is bought by whom and who has a financial interest in quackery selling well.


It is true, there are some Nobel Prize winners who defend homeopathy or other bogus treatments. Whenever this happens, the apologists of alternative medicine have a field day. They then cite the Nobel laureate ad nauseam and imply that his or her views prove their quackery to be correct.

Little do they know that they are merely milking yet another classical fallacy and that such regrettable events merely demonstrate that even bright people can make mistakes.

My advice is to check what the Nobel laureate actually said – more often than not, it turns out that a much-publicised quote is, in fact, a misquote – and what his or her qualifications are for making such a statement; a Nobel Prize in literature, for instance, is not a sufficient qualification for commenting on healthcare issues.


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