MD, PhD, FMedSci, FSB, FRCP, FRCPEd

false positive

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Guest post by Jan Oude-Aost

ADHD is a common disorder among children. There are evidence based pharmacological treatments, the best known being methylphenidate (MPH). MPH has kind of a bad reputation, but is effective and reasonably safe. The market is also full of alternative treatments, pharmacological and others, some of them under investigation, some unproven and many disproven. So I was not surprised to find a study about Ginkgo biloba as a treatment for ADHD. I was surprised, however, to find this study in the German Journal of Child and Adolescent Psychiatry and Psychotherapy, officially published by the “German Society of Child and Adolescent Psychiatry and Psychotherapy“ (Deutsche Gesellschaft für Kinder- und Jugendpsychiatrie und Psychotherapie). The journal’s guidelines state that studies should provide new scientific results.

The study is called “Ginkgo biloba Extract EGb 761® in Children with ADHD“. EGb 761® is the key ingredient in “Tebonin®“, a herbal drug made by “Dr. Wilma Schwabe GmbH“. The abstract states:

One possible treatment, at least for cognitive problems, might be the administration of Ginkgo biloba, though evidence is rare.This study tests the clinical efficacy of a Ginkgo biloba special extract (EGb 761®) (…) in children with ADHD (…).

Eine erfolgversprechende, bislang kaum untersuchte Möglichkeit zur Behandlung kognitiver Aspekte ist die Gabe von Ginkgo biloba. Ziel der vorliegenden Studie war die Prüfung klinischer Wirksamkeit (…) von Ginkgo biloba-Extrakt Egb 761® bei Kindern mit ADHS.“ (Taken from the English and German abstracts.)

The study sample (20!) was recruited among children who “did not tolerate or were unwilling“ to take MPH. The unwilling part struck me as problematic. There is likely a strong selection bias towards parents who are unwilling to give their children MPH. I guess it is not the children who are unwilling to take MPH, but the parents who are unwilling to administer it. At least some of these parents might be biased against MPH and might already favor CAMmodalities.

The authors state three main problems with “herbal therapy“ that require more empirical evidence: First of all the question of adverse reactions, which they claim occur in about 1% of cases with “some CAMs“ (mind you, not “herbal therapy“). Secondly, the question of drug interactions and thirdly, the lack of information physicians have about the CAMs their patients use.

A large part of the study is based on results of an EEG-protocol, which I choose to ignore, because the clinical results are too weak to give the EEG findings any clinical relevance.

Before looking at the study itself, let’s look at what is known about Ginkgo biloba as a drug. Ginkgo is best known for its use in patients with dementia, cognitive impairment und tinnitus. A Cochrane review from 2009 concluded:

There is no convincing evidence that Ginkgo biloba is efficacious for dementia and cognitive impairment“ [1].

The authors of the current Study cite Sarris et al. (2011), a systematic review of complementary treatment of ADHD. Sarris et al. mention Salehi et al. (2010) who tested Ginkgo against MPH. MPH turned out to be much more effective than Ginkgo, but Sarris et al. argue that the duration of treatment (6 weeks) might have been too short to see the full effects of Ginkgo.

Given the above information it is unclear why Ginkgo is judged a “possible“ treatment, properly translated from German even “promising”, and why the authors state that Ginkgo has been “barely studied“.

In an unblinded, uncontrolled study with a sample likely to be biased toward the tested intervention, anything other than a positive result would be odd. In the treatment of autism there are several examples of implausible treatments that worked as long as parents knew that their children were getting the treatment, but didn’t after proper blinding (e.g. secretin).

This study’s aim was to test clinical efficacy, but the conclusion begins with how well tolerated Ginkgo was. The efficacy is mentioned subsequently: “Following administration, interrelated improvements on behavioral ratings of ADHD symptoms (…) were detected (…).“ But the way they where “detected“ is interesting. The authors used an established questionnaire (FBB-HKS) to let parents rate their children. Only the parents. The children and their teachers where not given the FBB-HKS-questionnaires, inspite of this being standard clinical practice (and inspite of giving children questionnaires to determine changes in quality of life, which were not found).

None of the three problems that the authors describe as important (adverse reactions, drug interactions, lack of information) can be answered by this study. I am no expert in statistics but it seems unlikely to me to meaningfully determine adverse effects in just 20 patients especially when adverse effects occur at a rate of 1%. The authors claim they found an incidence rate of 0,004% in “700 observation days“. Well, if they say so.

The authors conclude:

Taken together, the current study provides some preliminary evidence that Ginkgo biloba Egb 761® seems to be well tolerated in the short term and may be a clinically useful treatment for children with ADHD. Double-blind randomized trials are required to clarify the value of the presented data.

Given the available information mentioned earlier, one could have started with that conclusion and conducted a double blind RCT in the first place!

Clinical Significance

The trends of this preliminary open study may suggest that Ginkgo biloba Egb 761® might be considered as a complementary or alternative medicine for treating children with ADHD.“

So, why do I care? If preliminary evidence “may suggest“ that something “might be considered“ as a treatment? Because I think that this study does not answer any important questions or give us any new or useful knowledge. Following the journal’s guidelines, it should therefore not have been published. I also think it is an example of bad science. Bad not just because of the lack of critical thinking. It also adds to the misinformation about possible ADHD treatments spreading through the internet. The study was published in September. In November I found a website citing the study and calling it “clinical proof“ when it is not. But child psychiatrists will have to explain that to many parents, instead of talking about their children’s health.

I somehow got the impression that this study was more about marketing than about science. I wonder if Schwabe will help finance the necessary double-blind randomized trial…

[1] See more at: http://summaries.cochrane.org/CD003120/DEMENTIA_there-is-no-convincing-evidence-that-ginkgo-biloba-is-efficacious-for-dementia-and-cognitive-impairment#sthash.oqKFrSCC.dpuf

Acupuncture seems to be as popular as never before – many conventional pain clinics now employ acupuncturists, for instance. It is probably true to say that acupuncture is one of the best-known types of all alternative therapies. Yet, experts are still divided in their views about this treatment – some proclaim that acupuncture is the best thing since sliced bread, while others insist that it is no more than a theatrical placebo. Consumers, I imagine, are often left helpless in the middle of these debates. Here are 7 important bits of factual information that might help you make up your mind, in case you are tempted to try acupuncture.

  1. Acupuncture is ancient; some enthusiast thus claim that it has ‘stood the test of time’, i. e. that its long history proves its efficacy and safety beyond reasonable doubt and certainly more conclusively than any scientific test. Whenever you hear such arguments, remind yourself that the ‘argumentum ad traditionem’ is nothing but a classic fallacy. A long history of usage proves very little – think of how long blood letting was used, even though it killed millions.
  2. We often think of acupuncture as being one single treatment, but there are many different forms of this therapy. According to believers in acupuncture, acupuncture points can be stimulated not just by inserting needles (the most common way) but also with heat, electrical currents, ultrasound, pressure, etc. Then there is body acupuncture, ear acupuncture and even tongue acupuncture. Finally, some clinicians employ the traditional Chinese approach based on the assumption that two life forces are out of balance and need to be re-balanced, while so-called ‘Western’ acupuncturists adhere to the concepts of conventional medicine and claim that acupuncture works via scientifically explainable mechanisms that are unrelated to ancient Chinese philosophies.
  3. Traditional Chinese acupuncturists have not normally studied medicine and base their practice on the Taoist philosophy of the balance between yin and yang which has no basis in science. This explains why acupuncture is seen by traditional acupuncturists as a ‘cure all’ . In contrast, medical acupuncturists tend to cite neurophysiological explanations as to how acupuncture might work. However, it is important to note that, even though they may appear plausible, these explanations are currently just theories and constitute no proof for the validity of acupuncture as a medical intervention.
  4. The therapeutic claims made for acupuncture are legion. According to the traditional view, acupuncture is useful for virtually every condition affecting mankind; according to the more modern view, it is effective for a relatively small range of conditions only. On closer examination, the vast majority of these claims can be disclosed to be based on either no or very flimsy evidence. Once we examine the data from reliable clinical trials (today several thousand studies of acupuncture are available – see below), we realise that acupuncture is associated with a powerful placebo effect, and that it works better than a placebo only for very few (some say for no) conditions.
  5. The interpretation of the trial evidence is far from straight forward: most of the clinical trials of acupuncture originate from China, and several investigations have shown that very close to 100% of them are positive. This means that the results of these studies have to be taken with more than a small pinch of salt. In order to control for patient-expectations, clinical trials can be done with sham needles which do not penetrate the skin but collapse like miniature stage-daggers. This method does, however, not control for acupuncturists’ expectations; blinding of the therapists is difficult and therefore truly double (patient and therapist)-blind trials of acupuncture do hardly exist. This means that even the most rigorous studies of acupuncture are usually burdened with residual bias.
  6. Few acupuncturists warn their patients of possible adverse effects; this may be because the side-effects of acupuncture (they occur in about 10% of all patients) are mostly mild. However, it is important to know that very serious complications of acupuncture are on record as well: acupuncture needles can injure vital organs like the lungs or the heart, and they can introduce infections into the body, e. g. hepatitis. About 100 fatalities after acupuncture have been reported in the medical literature – a figure which, due to lack of a monitoring system, may disclose just the tip of an iceberg.
  7. Given that, for the vast majority of conditions, there is no good evidence that acupuncture works beyond a placebo response, and that acupuncture is associated with finite risks, it seems to follow that, in most situations, the risk/benefit balance for acupuncture fails to be convincingly positive.

Reiki is a form of energy healing that evidently has been getting so popular that, according to the ‘Shropshire Star’, even stressed hedgehogs are now being treated with this therapy. In case you argue that this publication is not cutting edge when it comes to reporting of scientific advances, you may have a point. So, let us see what evidence we find on this amazing intervention.

A recent systematic review of the therapeutic effects of Reiki concludes that the serious methodological and reporting limitations of limited existing Reiki studies preclude a definitive conclusion on its effectiveness. High-quality randomized controlled trials are needed to address the effectiveness of Reiki over placebo. Considering that this article was published in the JOURNAL OF ALTERNATIVE AND COMPLEMENTARY MEDICINE, this is a fairly damming verdict. The notion that Reiki is but a theatrical placebo recently received more support from a new clinical trial.

This pilot study examined the effects of Reiki therapy and companionship on improvements in quality of life, mood, and symptom distress during chemotherapy. Thirty-six breast cancer patients received usual care, Reiki, or a companion during chemotherapy. Data were collected from patients while they were receiving usual care. Subsequently, patients were randomized to either receive Reiki or a companion during chemotherapy. Questionnaires assessing quality of life, mood, symptom distress, and Reiki acceptability were completed at baseline and chemotherapy sessions 1, 2, and 4. Reiki was rated relaxing and caused no side effects. Both Reiki and companion groups reported improvements in quality of life and mood that were greater than those seen in the usual care group.

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

This is an odd conclusion, if there ever was one. Clearly the ‘companionship’ group was included to see whether Reiki has effects beyond simply providing sympathetic attention. The results show that this is not the case. It follows, I think, that Reiki is a placebo; its perceived relaxing effects are the result of non-specific phenomena which have nothing to do with Reiki per se. The fact that the authors fail to spell this out more clearly makes me wonder whether they are researchers or promoters of Reiki.

Some people will feel that it does not matter how Reiki works, the main thing is that it does work. I beg to differ!

If its effects are due to nothing else than attention and companionship, we do not need ‘trained’ Reiki masters to do the treatment; anyone who has time, compassion and sympathy can do it. More importantly, if Reiki is a placebo, we should not mislead people that some super-natural energy is at work. This only promotes irrationality – and, as Voltaire once said: those who make you believe in absurdities can make you commit atrocities.

Acute tonsillitis (AT) is an upper respiratory tract infection which is prevalent, particularly in children. The cause is usually a viral or, less commonly, a bacterial infection. Treatment is symptomatic and usually consists of ample fluid intake and pain-killers; antibiotics are rarely indicated, even if the infection is bacterial by nature. The condition is self-limiting and symptoms subside normally after one week.

Homeopaths believe that their remedies are effective for AT – but is there any evidence? A recent trial seems to suggest there is.

It aimed, according to its authors, to determine the efficacy of a homeopathic complex on the symptoms of acute viral tonsillitis in African children in South Africa.

The double-blind, placebo-controlled RCT was a 6-day “pilot study” and included 30 children aged 6 to 12 years, with acute viral tonsillitis. Participants took two tablets 4 times per day. The treatment group received lactose tablets medicated with the homeopathic complex (Atropa belladonna D4, Calcarea phosphoricum D4, Hepar sulphuris D4, Kalium bichromat D4, Kalium muriaticum D4, Mercurius protoiodid D10, and Mercurius biniodid D10). The placebo consisted of the unmedicated vehicle only. The Wong-Baker FACES Pain Rating Scale was used for measuring pain intensity, and a Symptom Grading Scale assessed changes in tonsillitis signs and symptoms.

The results showed that the treatment group had a statistically significant improvement in the following symptoms compared with the placebo group: pain associated with tonsillitis, pain on swallowing, erythema and inflammation of the pharynx, and tonsil size.

The authors drew the following conclusions: the homeopathic complex used in this study exhibited significant anti-inflammatory and pain-relieving qualities in children with acute viral tonsillitis. No patients reported any adverse effects. These preliminary findings are promising; however, the sample size was small and therefore a definitive conclusion cannot be reached. A larger, more inclusive research study should be undertaken to verify the findings of this study.

Personally, I agree only with the latter part of the conclusion and very much doubt that this study was able to “determine the efficacy” of the homeopathic product used. The authors themselves call their trial a “pilot study”. Such projects are not meant to determine efficacy but are usually designed to determine the feasibility of a trial design in order to subsequently mount a definitive efficacy study.

Moreover, I have considerable doubts about the impartiality of the authors. Their affiliation is “Department of Homoeopathy, University of Johannesburg, Johannesburg, South Africa”, and their article was published in a journal known to be biased in favour of homeopathy. These circumstances in itself might not be all that important, but what makes me more than a little suspicious is this sentence from the introduction of their abstract:

“Homeopathic remedies are a useful alternative to conventional medications in acute uncomplicated upper respiratory tract infections in children, offering earlier symptom resolution, cost-effectiveness, and fewer adverse effects.”

A useful alternative to conventional medications (there are no conventional drugs) for earlier symptom resolution?

If it is true that the usefulness of homeopathic remedies has been established, why conduct the study?

If the authors were so convinced of this notion (for which there is, of course, no good evidence) how can we assume they were not biased in conducting this study?

I think that, in order to agree that a homeopathic remedy generates effects that differ from those of placebo, we need a proper (not a pilot) study, published in a journal of high standing by unbiased scientists.

Rigorous research into the effectiveness of a therapy should tell us the truth about the ability of this therapy to treat patients suffering from a given condition — perhaps not one single study, but the totality of the evidence (as evaluated in systematic reviews) should achieve this aim. Yet, in the realm of alternative medicine (and probably not just in this field), such reviews are often highly contradictory.

A concrete example might explain what I mean.

There are numerous systematic reviews assessing the effectiveness of acupuncture for fibromyalgia syndrome (FMS). It is safe to assume that the authors of these reviews have all conducted comprehensive searches of the literature in order to locate all the published studies on this subject. Subsequently, they have evaluated the scientific rigor of these trials and summarised their findings. Finally they have condensed all of this into an article which arrives at a certain conclusion about the value of the therapy in question. Understanding this process (outlined here only very briefly), one would expect that all the numerous reviews draw conclusions which are, if not identical, at least very similar.

However, the disturbing fact is that they are not remotely similar. Here are two which, in fact, are so different that one could assume they have evaluated a set of totally different primary studies (which, of course, they have not).

One recent (2014) review concluded that acupuncture for FMS has a positive effect, and acupuncture combined with western medicine can strengthen the curative effect.

Another recent review concluded that a small analgesic effect of acupuncture was present, which, however, was not clearly distinguishable from bias. Thus, acupuncture cannot be recommended for the management of FMS.

How can this be?

By contrast to most systematic reviews of conventional medicine, systematic reviews of alternative therapies are almost invariably based on a small number of primary studies (in the above case, the total number was only 7 !). The quality of these trials is often low (all reviews therefore end with the somewhat meaningless conclusion that more and better studies are needed).

So, the situation with primary studies of alternative therapies for inclusion into systematic reviews usually is as follows:

  • the number of trials is low
  • the quality of trials is even lower
  • the results are not uniform
  • the majority of the poor quality trials show a positive result (bias tends to generate false positive findings)
  • the few rigorous trials yield a negative result

Unfortunately this means that the authors of systematic reviews summarising such confusing evidence often seem to feel at liberty to project their own pre-conceived ideas into their overall conclusion about the effectiveness of the treatment. Often the researchers are in favour of the therapy in question – in fact, this usually is precisely the attitude that motivated them to conduct a review in the first place. In other words, the frequently murky state of the evidence (as outlined above) can serve as a welcome invitation for personal bias to do its effect in skewing the overall conclusion. The final result is that the readers of such systematic reviews are being misled.

Authors who are biased in favour of the treatment will tend to stress that the majority of the trials are positive. Therefore the overall verdict has to be positive as well, in their view. The fact that most trials are flawed does not usually bother them all that much (I suspect that many fail to comprehend the effects of bias on the study results); they merely add to their conclusions that “more and better trials are needed” and believe that this meek little remark is sufficient evidence for their ability to critically analyse the data.

Authors who are not biased and have the necessary skills for critical assessment, on the other hand, will insist that most trials are flawed and therefore their results must be categorised as unreliable. They will also emphasise the fact that there are a few reliable studies and clearly point out that these are negative. Thus their overall conclusion must be negative as well.

In the end, enthusiasts will conclude that the treatment in question is at least promising, if not recommendable, while real scientists will rightly state that the available data are too flimsy to demonstrate the effectiveness of the therapy; as it is wrong to recommend unproven treatments, they will not recommend the treatment for routine use.

The difference between the two might just seem marginal – but, in fact, it is huge: IT IS THE DIFFERENCE BETWEEN MISLEADING PEOPLE AND GIVING RESPONSIBLE ADVICE; THE DIFFERENCE BETWEEN VIOLATING AND ADHERING TO ETHICAL STANDARDS.

A reader of this blog recently sent me the following message: “Looks like this group followed you recent post about how to perform a CAM RCT!” A link directed me to a new trial of ear-acupressure. Today is ‘national acupuncture and oriental medicine day’ in the US, a good occasion perhaps to have a critical look at it.

The aim of this study was to assess the effectiveness of ear acupressure and massage vs. control in the improvement of pain, anxiety and depression in persons diagnosed with dementia.

For this purpose, the researchers recruited a total of 120 elderly dementia patients institutionalized in residential homes. The participants were randomly allocated, to three groups:

  • Control group – they continued with their routine activities;
  • Ear acupressure intervention group – they received ear acupressure treatment (pressure was applied to acupressure points on the ear);
  • Massage therapy intervention group – they received relaxing massage therapy.

Pain, anxiety and depression were assessed with the Doloplus2, Cornell and Campbell scales. The study was carried out during 5 months; three months of experimental treatment and two months with no treatment. The assessments were done at baseline, each month during the treatment and at one and two months of follow-up.

A total of 111 participants completed the study. The ear acupressure intervention group showed better improvements than the two other groups in relation to pain and depression during the treatment period and at one month of follow-up. The best improvement in pain was achieved in the last (3rd) month of ear acupressure treatment. The best results regarding anxiety were also observed in the last month of treatment.

The authors concluded that ear acupressure and massage therapy showed better results than the control group in relation to pain, anxiety and depression. However, ear acupressure achieved more improvements.

The question is: IS THIS A RIGOROUS TRIAL?

My answer would be NO.

Now I better explain why, don’t I?

If we look at them critically, the results of this trial might merely prove that spending some time with a patient, being nice to her, administering a treatment that involves time and touch, etc. yields positive changes in subjective experiences of pain, anxiety and depression. Thus the results of this study might have nothing to do with the therapies per se.

And why would acupressure be more successful than massage therapy? Massage therapy is an ‘old hat’ for many patients; by contrast, acupressure is exotic and relates to mystical life forces etc. Features like that have the potential to maximise the placebo-response. Therefore it is conceivable that they have contributed to the superiority of acupressure over massage.

What I am saying is that the results of this trial can be interpreted in not just one but several ways. The main reason for that is the fact that the control group were not given an acceptable placebo, one that was indistinguishable from the real treatment. Patients were fully aware of what type of intervention they were getting. Therefore their expectations, possibly heightened by the therapists, determined the outcomes. Consequently there were factors at work which were totally beyond the control of the researchers and a clear causal link between the therapy and the outcome cannot be established.

An RCT that is aimed to test the effectiveness of a therapy but fails to establish such a causal link beyond reasonable doubt cannot be characterised as a rigorous study, I am afraid.

Sorry! Did I spoil your ‘national acupuncture and oriental medicine day’?

One of the most commonly ‘accepted’ indications for acupuncture is anxiety. Many trials have suggested that it is effective for that condition. But is this really true? To find out, we need someone to conduct a systematic review or meta-analysis.

Korean researchers have just published such a paper; they wanted to assess the preoperative anxiolytic efficacy of acupuncture therapy and therefore conducted a meta-analysis of all RCTs on the subject. Four electronic databases were searched up to February 2014. Data were included in the meta-analysis from RCTs in which groups receiving preoperative acupuncture treatment were compared with control groups receiving a placebo for anxiety.

Fourteen publications with a total of 1,034 patients were included. Six RCTs, using the State-Trait Anxiety Inventory-State (STAI-S), reported that acupuncture interventions led to greater reductions in preoperative anxiety relative to sham acupuncture. A further eight publications, employing visual analogue scales, also indicated significant differences in preoperative anxiety amelioration between acupuncture and sham acupuncture.

The authors concluded that aacupuncture therapy aiming at reducing preoperative anxiety has a statistically significant effect relative to placebo or nontreatment conditions. Well-designed and rigorous studies that employ large sample sizes are necessary to corroborate this finding.

From these conclusions most casual readers might get the impression that acupuncture is indeed effective. One has to dig a bit deeper to realise that is perhaps not so.

Why? Because the quality of the primary studies was often dismally poor. Most did not even mention adverse effects which, in my view, is a clear breach of publication ethics. What is more, all the studies were wide open to bias. The authors of the meta-analysis include in their results section the following short paragraph:

The 14 included studies exhibited various degrees of bias susceptibility (Figure 2 and Figure 3). The agreement rate, as measured using Cohen’s kappa, was 0.8 [32]. Only six studies reported concealed allocation; the other six described a method of adequate randomization, although the word “randomization” appeared in all of the articles. Thirteen studies prevented blinding of the participants. Participants in these studies had no previous experience of acupuncture. According to STRICTA, two studies enquired after patients’ beliefs as a group: there were no significant differences [20, 24].

There is a saying amongst experts about such meta-analyses: RUBBISH IN, RUBBISH OUT. It describes the fact that several poor studies, pooled meta-analytically, can never give a reliable result.

This does, however, not mean that such meta-analyses are necessarily useless. If the authors prominently (in the abstract) stress that the quality of the primary studies was wanting and that therefore the overall result is unreliable, they might inspire future researchers to conduct more rigorous trials and thus generate progress. Most importantly, by insisting on pointing out these limitations and by not drawing positive conclusions from flawed data, they would avoid misleading those health care professionals – and let’s face it, they are the majority – who merely read the abstract or even just the conclusions of such articles.

The authors of this review have failed to do any of this; they and the journal EBCAM have thus done a disservice to us all by contributing to the constant drip of misleading and false-positive information about the value of acupuncture.

After the usually challenging acute therapy is behind them, cancer patients are often desperate to find a therapy that might improve their wellbeing. At that stage they may suffer from a wide range of symptoms which can seriously limit their quality of life. Any treatment that can be shown to restore them to their normal mental and physical health would be more than welcome.

Most homeopaths believe that their remedies can do just that, particularly if they are tailored not to the disease but to the individual patient. Sadly, the evidence that this might be so is almost non-existent. Now, a new trial has become available; it was conducted by Jennifer Poole, a chartered psychologist and registered homeopath, and researcher and teacher at Nemeton Research Foundation, Romsey.

The aim of this study was to explore the benefits of a three-month course of individualised homeopathy (IH) for survivors of cancer.  Fifteen survivors of any type of cancer were recruited from a walk-in cancer support centre. Conventional treatment had to have taken place within the last three years. Patients saw a homeopath who prescribed IH. After three months of IH, they scored their total, physical and emotional wellbeing using the Functional Assessment of Chronic Illness Therapy for Cancer (FACIT-G). The results show that 11 of the 14 women had statistically positive outcomes for emotional, physical and total wellbeing.
The conclusions of the author are clear: Findings support previous research, suggesting CAM or IH could be beneficial for survivors of cancer.

This article was published in the NURSING TIMES, and the editor added a footnote informing us that “This article has been double-blind “.

I find this surprising. A decent peer-review should have picked up the point that a study of that nature cannot possibly produce results which tell us anything about the benefits of IH. The reasons for this are fairly obvious:

  • there was no control group,
  • therefore the observed outcomes are most likely due to 1) natural history, 2) placebo, 3) regression towards the mean and 4) social desirability; it seems most unlikely that IH had anything to do with the result
  • the sample size was tiny,
  • the patients elected to receive IH which means that had high expectations of a positive outcome,
  • only subjective outcome measures were used,
  • there is no good previous research suggesting that IH benefits cancer patients.

On the last point, a recent systematic review showed that the studies available on this topic had mixed results either showing a significantly greater improvement in QOL in the intervention group compared to the control group, or no significant difference between groups. The authors concluded that there existed significant gaps in the evidence base for the effectiveness of CAM on QOL in cancer survivors. Further work in this field needs to adopt more rigorous methodology to help support cancer survivors to actively embrace self-management and effective CAMs, without recommending inappropriate interventions which are of no proven benefit.

All this new study might tell us is that IH did not seem to harm these patients  – but even this finding is not certain; to be sure, we would need to include many more patients. Any conclusions about the effectiveness of IH are totally unwarranted. But are there ANY generalizable conclusions that can be drawn from this article? Yes, I can think of a few:

  • Some cancer patients can be persuaded to try the most implausible treatments.
  • Some journals will publish any rubbish.
  • Some peer-reviewers fail to spot the most obvious defects.
  • Some ‘researchers’ haven’t got a clue.
  • The attempts of misleading us about the value of homeopathy are incessant.

One might argue that this whole story is too trivial for words; who cares what dodgy science is published in the NURSING TIMES? But I think it does matter – not so much because of this one silly article itself, but because similarly poor research with similarly ridiculous conclusions is currently published almost every day. Subsequently it is presented to the public as meaningful science heralding important advances in medicine. It matters because this constant drip of bogus research eventually influences public opinion and determines far-reaching health care decisions.

Many proponents of alternative medicine seem somewhat suspicious of research; they have obviously understood that it might not produce the positive result they had hoped for; after all, good research tests hypotheses and does not necessarily confirm beliefs. At the same time, they are often tempted to conduct research: this is perceived as being good for the image and, provided the findings are positive, also good for business.

Therefore they seem to be tirelessly looking for a study design that cannot ‘fail’, i.e. one that avoids the risk of negative results but looks respectable enough to be accepted by ‘the establishment’. For these enthusiasts, I have good news: here is the study design that cannot fail.

It is perhaps best outlined as a concrete example; for reasons that will become clear very shortly, I have chosen reflexology as a treatment of diabetic neuropathy, but you can, of course, replace both the treatment and the condition as it suits your needs. Here is the outline:

  • recruit a group of patients suffering from diabetic neuropathy – say 58, that will do nicely,
  • randomly allocate them to two groups,
  • the experimental group receives regular treatments by a motivated reflexologist,
  • the controls get no such therapy,
  • both groups also receive conventional treatments for their neuropathy,
  • the follow-up is 6 months,
  • the following outcome measures are used: pain reduction, glycemic control, nerve conductivity, and thermal and vibration sensitivities,
  • the results show that the reflexology group experience more improvements in all outcome measures than those of control subjects,
  • your conclusion: This study exhibited the efficient utility of reflexology therapy integrated with conventional medicines in managing diabetic neuropathy.

Mission accomplished!

This method is fool-proof, trust me, I have seen it often enough being tested, and never has it generated disappointment. It cannot fail because it follows the notorious A+B versus B design (I know, I have mentioned this several times before on this blog, but it is really important, I think): both patient groups receive the essential mainstream treatment, and the experimental group receives a useless but pleasant alternative treatment in addition. The alternative treatment involves touch, time, compassion, empathy, expectations, etc. All of these elements will inevitably have positive effects, and they can even be used to increase the patients’ compliance with the conventional treatments that is being applied in parallel. Thus all outcome measures will be better in the experimental compared to the control group.

The overall effect is pure magic: even an utterly ineffective treatment will appear as being effective – the perfect method for producing false-positive results.

And now we hopefully all understand why this study design is so very popular in alternative medicine. It looks solid – after all, it’s an RCT!!! – and it thus convinces even mildly critical experts of the notion that the useless treatment is something worth while. Consequently the useless treatment will become accepted as ‘evidence-based’, will be used more widely and perhaps even reimbursed from the public purse. Business will be thriving!

And why did I employ reflexology for diabetic neuropathy? Is that example not a far-fetched? Not a bit! I used it because it describes precisely a study that has just been published. Of course, I could also have taken the chiropractic trial from my last post, or dozens of other studies following the A+B versus B design – it is so brilliantly suited for misleading us all.

Chiropractors, like other alternative practitioners, use their own unique diagnostic tools for identifying the health problems of their patients. One such test is the Kemp’s test, a manual test used by most chiropractors to diagnose problems with lumbar facet joints. The chiropractor rotates the torso of the patient, while her pelvis is fixed; if manual counter-rotative resistance on one side of the pelvis by the chiropractor causes lumbar pain for the patient, it is interpreted as a sign of lumbar facet joint dysfunction which, in turn would be treated with spinal manipulation.

All diagnostic tests have to fulfil certain criteria in order to be useful. It is therefore interesting to ask whether the Kemp’s test meets these criteria. This is precisely the question addressed in a recent paper. Its objective was to evaluate the existing literature regarding the accuracy of the Kemp’s test in the diagnosis of facet joint pain compared to a reference standard.

All diagnostic accuracy studies comparing the Kemp’s test with an acceptable reference standard were located and included in the review. Subsequently, all studies were scored for quality and internal validity.

Five articles met the inclusion criteria. Only two studies had a low risk of bias, and three had a low concern regarding applicability. Pooling of data from studies using similar methods revealed that the test’s negative predictive value was the only diagnostic accuracy measure above 50% (56.8%, 59.9%).

The authors concluded that currently, the literature supporting the use of the Kemp’s test is limited and indicates that it has poor diagnostic accuracy. It is debatable whether clinicians should continue to use this test to diagnose facet joint pain.

The problem with chiropractic diagnostic methods is not confined to the Kemp’s test, but extends to most tests employed by chiropractors. Why should this matter?

If diagnostic methods are not reliable, they produce either false-positive or false-negative findings. When a false-negative diagnosis is made, the chiropractor might not treat a condition that needs attention. Much more common in chiropractic routine, I guess, are false-positive diagnoses. This means chiropractors frequently treat conditions which the patient does not have. This, in turn, is not just a waste of money and time but also, if the ensuing treatment is associated with risks, an unnecessary exposure of patients to getting harmed.

The authors of this review, chiropractors from Canada, should be praised for tackling this subject. However, their conclusion that “it is debatable whether clinicians should continue to use this test to diagnose facet joint pain” is in itself highly debatable: the use of nonsensical diagnostic tools can only result in nonsense and should therefore be disallowed.

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