MD, PhD, MAE, FMedSci, FRSB, FRCP, FRCPEd.

meta-analysis

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Placebo effects are a fascinating subject. In so-called alternative medicine (SCAM), they are particularly important because much of SCAM seems to rely on little more than placebo effects. Therefore, I think this new paper is of some relevance to us.

The aim of this systematic review was to quantify the placebo effect of intraarticular injections for knee osteoarthritis in terms of pain, function, and objective outcomes. Factors influencing placebo effect were investigated.

The authors concluded that the placebo effect of knee injections is significant, with functional improvements lasting even longer than those reported for pain perception. The high, long-lasting, and heterogeneous effects on the scales commonly used in clinical trials further highlight that the impact of placebo should not be overlooked in the research on and management of knee osteoarthritis.

The authors furthermore confirmed that “the main finding of this meta-analysis is that placebo is an important component of the effect of injective treatments for patients with KOA, with saline injections being able to provide relevant and long-lasting results not only in terms of pain relief but also with respect to stiffness resolution and function improvement. These results are both statistically and clinically significant and can be perceived by patients up to 6 months.”

I would dispute that!

To explain why it might help to read our 1995 BMJ paper on the subject:

We often and wrongly equate the response seen in the placebo arm of a clinical trial with the placebo effect. In order to obtain the true placebo effect, other non-specific effects can be identified by including an untreated control group in clinical trials. A review of the literature shows that most authors confuse the perceived placebo effect with the true placebo effect. The true placebo effect is highly variable, depending on several factors that are not fully understood. A distinction between the perceived and the true placebo effects would be helpful in understanding the complex phenomena involved in a placebo response.

In other words, what the authors picked up in their analysis (i.e. the changes that occurred in the placebo groups between the start of a trial and after placebo application) is not just the placebo response; it is, in fact, a combination of a placebo effect, concomitant interventions/care, regression towards the mean, natural history of the condition and possibly other factors.

Does it matter?

Yes, it does!

Placebo effects are not nearly as powerful and long-lasting as the authors conclude. And this means virtually all their implications for clinical practice are incorrect.

Zinc has been in the limelight recently. The reason is that it has been recommended as a preventative and/or treatment of COVID infections. The basis for such recommendations has been some trial evidence suggesting it is effective for viral respiratory tract infections (RTIs). But the evidence has been full of contradictions which means, we need a systematic review that critically evaluated the totality of the available data.

This systematic review was aimed at evaluating the benefits and risks of zinc formulations compared with controls for the prevention or treatment of acute RTIs in adults.

Seventeen English and Chinese databases were searched in April/May 2020 for randomized clinical trials (RCTs), and from April/May 2020 to August 2020 for SARS-CoV-2 RCTs. Cochrane rapid review methods were applied. Quality appraisals used the Risk of Bias 2.0 and Grading of Recommendations, Assessment, Development and Evaluation (GRADE) approach.

Twenty-eight RCTs with 5446 participants were identified. None were specific to SARS-CoV-2. Compared with placebo, oral or intranasal zinc prevented 5 RTIs per 100 person-months (95% CI 1 to 8, numbers needed to treat (NNT)=20, moderate-certainty/quality). Sublingual zinc did not prevent clinical colds following human rhinovirus inoculations (relative risk, RR 0.96, 95% CI 0.77 to 1.21, moderate-certainty/quality). On average, symptoms resolved 2 days earlier with sublingual or intranasal zinc compared with placebo (95% CI 0.61 to 3.50, very low-certainty/quality) and 19 more adults per 100 were likely to remain symptomatic on day 7 without zinc (95% CI 2 to 38, NNT=5, low-certainty/quality). There were clinically significant reductions in day 3 symptom severity scores (mean difference, MD -1.20 points, 95% CI -0.66 to -1.74, low-certainty/quality), but not average daily symptom severity scores (standardised MD -0.15, 95% CI -0.43 to 0.13, low-certainty/quality). Non-serious adverse events (AEs) (eg, nausea, mouth/nasal irritation) were higher (RR 1.41, 95% CI 1.17 to 1.69, NNHarm=7, moderate-certainty/quality). Compared with active controls, there were no differences in illness duration or AEs (low-certainty/quality). No serious AEs were reported in the 25 RCTs that monitored them (low-certainty/quality).

The authors concluded that in adult populations unlikely to be zinc deficient, there was some evidence suggesting zinc might prevent RTIs symptoms and shorten duration. Non-serious AEs may limit tolerability for some. The comparative efficacy/effectiveness of different zinc formulations and doses were unclear. The GRADE-certainty/quality of the evidence was limited by a high risk of bias, small sample sizes and/or heterogeneity. Further research, including SARS-CoV-2 clinical trials is warranted.

The authors provide a short comment on the assumed mode of action of zinc. The rationale for topical intranasal and sublingual zinc is based on the in vitro effects of zinc ions that can inhibit viral replication, stabilize cell membranes and reduce mucosal inflammation. Other conceivable mechanisms include the activation of T lymphocytes, monocytes, and granulocytes.

The authors also remind us to be cautious: clinicians and consumers need to be aware that considerable uncertainty remains regarding the clinical efficacy of different zinc formulations, doses, and administration routes, and the extent to which efficacy might be influenced by the ever changing epidemiology of the viruses that cause RTIs. The largest body of evidence comes from sublingual lozenges and zinc gluconate and acetate salts, suggesting these are suitable choices. Yet, this does not mean that other administration routes and zinc salts are less effective. The new evidence on the prophylactic effects of low-dose nasal sprays adds weight to the otherwise inconclusive findings from the handful of RCTs evaluating zinc nasal sprays or gels for acute treatment. A minimum therapeutic dose for zinc is also yet to be determined. An earlier review suggested the minimum dose for sublingual lozenges is 75 mg. However, the present analysis does not support this conclusion. Furthermore, a daily oral dose of 15 mg has been shown to upregulate lymphocytes within days, so it is plausible that much lower doses might also be effective.

Should Acupuncture-Related Therapies be Considered in Prediabetes Control?

No!

If you are pre-diabetic, consult a doctor and follow his/her advice. Do NOT do what acupuncturists or other self-appointed experts tell you. Do NOT become a victim of quackery.

But the authors of a new paper disagree with my view.

So, let’s have a look at the evidence.

Their systematic review was aimed at evaluating the effects and safety of acupuncture-related therapy (AT) interventions on glycemic control for prediabetes. The Chinese researchers searched 14 databases and 5 clinical registry platforms from inception to December 2020. Randomized controlled trials involving AT interventions for managing prediabetes were included.

Of the 855 identified trials, 34 articles were included for qualitative synthesis, 31 of which were included in the final meta-analysis. Compared with usual care, sham intervention, or conventional medicine, AT treatments yielded greater reductions in the primary outcomes, including fasting plasma glucose (FPG) (standard mean difference [SMD] = -0.83; 95% confidence interval [CI], -1.06, -0.61; P < .00001), 2-hour plasma glucose (2hPG) (SMD = -0.88; 95% CI, -1.20, -0.57; P < .00001), and glycated hemoglobin (HbA1c) levels (SMD = -0.91; 95% CI, -1.31, -0.51; P < .00001), as well as a greater decline in the secondary outcome, which is the incidence of prediabetes (RR = 1.43; 95% CI, 1.26, 1.63; P < .00001).

The authors concluded that AT is a potential strategy that can contribute to better glycemic control in the management of prediabetes. Because of the substantial clinical heterogeneity, the effect estimates should be interpreted with caution. More research is required for different ethnic groups and long-term effectiveness.

But this is clearly a positive result!

Why do I not believe it?

There are several reasons:

  • There is no conceivable mechanism by which AT prevents diabetes.
  • The findings heavily rely on Chinese RCTs which are known to be of poor quality and often even fabricated. To trust such research would be a dangerous mistake.
  • Many of the primary studies were designed such that they failed to control for non-specific effects of AT. This means that a causal link between AT and the outcome is doubtful.
  • The review was published in a 3rd class journal of no impact. Its peer-review system evidently failed.

So, let’s just forget about this rubbish paper?

If only it were so easy!

Journalists always have a keen interest in exotic treatments that contradict established wisdom. Predictably, they have been reporting about the new review thus confusing or misleading the public. One journalist, for instance, stated:

Acupuncture has been used for thousands of years to treat a variety of illnesses — and now it could also help fight one of the 21st century’s biggest health challenges.

New research from Edith Cowan University has found acupuncture therapy may be a useful tool in avoiding type 2 diabetes.

The team of scientists investigated dozens of studies covering the effects of acupuncture on more than 3600 people with prediabetes. This is a condition marked by higher-than-normal blood glucose levels without being high enough to be diagnosed as diabetes.

According to the findings, acupuncture therapy significantly improved key markers, such as fasting plasma glucose, two-hour plasma glucose, and glycated hemoglobin. Additionally, acupuncture therapy resulted in a greater decline in the incidence of prediabetes.

The review can thus serve as a prime example for demonstrating how irresponsible research has the power to mislead millions. This is why I have often said that poor research is a danger to public health.

And what can be done about this more and more prevalent problem?

The answer is easy: people need to behave more responsibly; this includes:

  • trialists,
  • review authors,
  • editors,
  • peer-reviewers,
  • journalists.

Yes, the answer is easy in theory – but the practice is far from it!

As promised, I would like to correct the errors in my previous assessment of this paper. To remind everyone:

This systematic review evaluated individualized homeopathy as a treatment for children with attention deficit and hyperactivity disorder (ADHD) when compared to placebo or usual care alone.

Thirty-seven online sources were searched up to March 2021. Studies investigating the effects of individualized homeopathy against any control in ADHD were eligible. Data were extracted to a predefined excel sheet independently by two reviewers.

Six studies were analyzed:

  • 5 were RCTs
  • 2 were controlled against standard treatments;
  • 4 were placebo-controlled and double-blinded.

The meta-analysis revealed a significant effect size across studies of Hedges’ g = 0.542 (95% CI 0.311-0.772; z = 4,61; p < 0.001) against any control and of g = 0.605 (95% CI 0.05-1.16; z = 2.16, p = 0.03) against placebo. The effect estimations are based on studies with an average sample size of 52 participants.

The authors concluded that individualized homeopathy showed a clinically relevant and statistically robust effect in the treatment of ADHD.

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Now that I was able to access the full papers, I would like to offer a thorough analysis.

To get included in the review, primary studies had to be:

  • Published after 1980,
  • Investigating an individualized homeopathic intervention in childhood ADHD,
  • Comparing the intervention to a control condition (placebo, standard care or treatment as usual, both of which are referred to as “active control”) in a randomized or non-randomized parallel-group study
    design with one or more arms.

Six studies were included:

  • Fibert, P., Peasgood, T. & Relton, C. Rethinking ADHD intervention trials: feasibility testing of two treatments and a methodology. Eur. J. Pediatr. 178, 983–993 (2019). – DOI
  • Fibert, P., Relton, C., Heirs, M. & Bowden, D. A comparative consecutive case series of 20 children with a diagnosis of ADHD receiving homeopathic treatment, compared with 10 children receiving usual care. Homeopathy 105, 194–201 (2016). – DOI
  • Jacobs, J., Williams, A. L., Girard, C., Njike, V. Y. & Katz, D. Homeopathy for attention-deficit/hyperactivity disorder: a pilot randomized-controlled trial. J. Altern. Complement. Med. 11, 799–806 (2005). – DOI
  • Jones, M. The efficacy of homoeopathic simillimum in the treatment of attention-deficit/hyperactivity disorder (AD/HD) in schoolgoing children aged 6-11 years. https://openscholar.dut.ac.za/bitstream/10321/534/1/Jones_2009.pdf (2009).
  • Frei, H. et al. Homeopathic treatment of children with attention deficit hyperactivity disorder: a randomised, double blind, placebo controlled crossover trial. Eur. J. Pediatr. 164, 758–767 (2005). – DOI
  • Oberai, P. et al. Homoeopathic management of attention deficit hyperactivity disorder: a randomised placebo-controlled pilot trial. Indian J. Res. Homoeopathy 7, 158–167 (2013).

Exclusion criteria were:

  • Homeopathic intervention not individualized,
  • Serious methodological flaws, such as incidental unblinding, failure to report important data, or insufficient data for meta-analysis.

One study was excluded:

  • Lamont, J. Homoeopathic treatment of attention deficit hyperactivity disorder. Br. Homeopathic J. 86, 196–200 (1997). – DOI

I will first make several points about Walach’s systematic review itself and then have a look at the primary studies that it included. Finally, I will try to draw some conclusions.

The review authors state in their introduction that “beneficial effects of this intervention [homeopathy] have been shown for various kinds of medical conditions, including child diarrhea, supportive care in cancer, fibromyalgia, or ADHD.” In other words, already in the introduction, they disclose their strong pro-homeopathy bias; it would, of course, not be difficult to find investigations that contradict their optimism.

Despite the stated inclusion/exclusion criteria, the authors did include the Frei-study that did not follow a parallel-group design (see also below).

The authors included two active-controlled studies both of which did not report the type of treatment received by the control group. In other words, these trials failed to report important data which was a stated exclusion criterium (see below).

In their discussion section, the authors state that “all included studies employed individualized homeopathy and were of comparable, solid quality, hence a lack of methodological rigor is unlikely the reason for the difference between homeopathy and controls…” This, I think, is grossly misleading; even according to the authors’ own assessments, one study was deemed to have a high risk of bias and in two studies the risk of bias was “unclear”.

The overall positive effect of homeopathy demonstrated by the review was determined almost exclusively by the study of Oberai et al (p-value = 0.000). In fact, the studies by Jones and by Jacobs were negative, and the one by Frei was borderline positive with a p-value of 0.46. The authors address this crucial issue repeatedly and claim that excluding Oberai et al would still generate an overall positive meta-analytic result. Yet, they do not mention that the overall result would no longer be clinically relevant.

Looking at the included primary studies, I should make the following points:

  • The two Filbert studies, as mentioned, failed to report important data and should, according to the stated exclusion criteria, not have been included.
  • The study by Jacobs was a pilot study and generated negative findings.
  • The study by Jones is a non-peer-reviewed thesis. In my view, it should never have been included.
  • The study by Frei was a cross-over trial. According to the exclusion/inclusion criteria of the authors, it should not have been included.
  • The study by Oberai et al is the trial that has by far the largest effect size and thus is the driver of the overall result of the review. It is therefore important to have a closer look at it.

Here is the abstract:

Objective: To evaluate the usefulness of individualised homoeopathic medicines in treatment of Attention Deficit Hyperactivity Disorder (ADHD).
Design: Randomised placebo-controlled single-blind pilot trial.
Setting: Central Research Institute (Homoeopathy), Kottayam, Kerala, India from June 2009 to November 2011.
Participants: Children aged 6-15 years meeting the Diagnostic Statistical Manual of mental disorders (DSM-IV) criteria for ADHD.
Interventions: A total of 61 patients (Homoeopathy = 30, placebo = 31) were randomised to receive either individualised homoeopathic medicine in fifty millesimal (LM) potency or placebo for a period of one year.
Outcome measures: Conner’s Parent Rating Scale-Revised: Short (CPRS-R (S)), Clinical Global Impression-Severity Scale (CGI-SS), Clinical Global Impression- Improvement Scale (CGI-IS) and Academic performance.
Results: A total of 54 patients (homoeopathy = 27, placebo = 27) were analysed under modified intention to treat (ITT). All patients in homoeopathy group showed better outcome in baseline adjusted General Linear Model (GLM) repeated measures ANCOVA for oppositional, cognition problems, hyperactivity and ADHD Index (domains of CPRS-R (S)) and CGI-IS at T3, T6, T9 and T12 (P = 0.0001). The mean baseline-adjusted treatment difference between groups at month 12 from baseline for all individual outcome measures favoured homoeopathy group; Oppositional (−16.4, 95% CI – 20.5 to − 12.2, P = 0.0001), Cognition problems (−15.5, 95% CI − 19.2 to − 11.8, P = 0.0001), Hyperactivity (−20.6, 95% CI − 25.6 to − 15.4, P = 0.0001), ADHD I (−15.6, 95% CI − 19.5 to − 11.6, P = 0.0001), Academic performance 14.4%, 95% CI 8.3 to 20.5, P = 0.0001), CGISS (−1.6, 95% CI − 1.9 to − 1.2, P = 0.0001), CGIIS (−1.6, 95% CI − 2.3 to -0.9, P = 0.0001).
Conclusion: This pilot study provides evidence to support the therapeutic effects of individualised homoeopathic medicines in ADHD children. However, the results need to be validated in multi-center randomised double-blind placebo-controlled clinical trial.

Here are a few points of concern related to the Oberai et al:

  • The trial was a mere pilot study.
  • Despite the fact that it is now 9 years old, the authors never published a definitive trial.
  • The study was published in an obscure journal that is not Medline-listed.
  • The study is very poorly reported.
  • It is unclear how the diagnosis of ADHD for including the patients was verified.
  • The control patients were treated for one year with a placebo and no other therapies. In my view, this is not ethical.
  • The method of randomization is unclear.
  • The authors state that acute symptoms were treated throughout the study period with homeopathy, even in the control group. This seems odd and defies the principle of a placebo-controlled trial.
  • The authors state that only the patients were blind, not the investigators. This opens the door wide for all sorts of biases. It is, for example, likely that it also de-blinded the patients (the verum could be adjusted and changed, while the placebo remained constant).

All in all, this paper is of poor quality, Its findings are far from trustworthy and were not meant to be definitive. According to the following exclusion criteria, it should have been excluded:

  • It had several serious methodological flaws.
  • It did not blind the investigators.
  • It is likely that patients were de-blinded.
  • It failed to report important data.

So, why did Walach and his co-authors include it?

Could it be because, without the Oberai-study, the overall findings of the review would at best have turned out to be borderline significant and not clinically relevant?

This systematic review evaluated individualized homeopathy as a treatment for children with attention deficit and hyperactivity disorder (ADHD) when compared to placebo or usual care alone.

Thirty-seven online sources were searched up to March 2021. Studies investigating the effects of individualized homeopathy against any control in ADHD were eligible. Data were extracted to a predefined excel sheet independently by two reviewers.

Six studies were analyzed:

  • 5 were RCTs
  • 2 were controlled against standard treatments;
  • 4 were placebo-controlled and double-blinded.

The meta-analysis revealed a significant effect size across studies of Hedges’ g = 0.542 (95% CI 0.311-0.772; z = 4,61; p < 0.001) against any control and of g = 0.605 (95% CI 0.05-1.16; z = 2.16, p = 0.03) against placebo. The effect estimations are based on studies with an average sample size of 52 participants.

The authors concluded that individualized homeopathy showed a clinically relevant and statistically robust effect in the treatment of ADHD.

This is a counter-intuitive result (to put it mildly), and it is, therefore, wise to have a look at the 6 included studies:

1.Frei, H. et al. Homeopathic treatment of children with attention deficit hyperactivity disorder: a randomised, double blind, placebo controlled crossover trial. Eur. J. Pediatr. 164, 758–767 (2005).

This was a trial with just 62 patients who had previously responded to homeopathy. The study was conducted by known proponents of homeopathy and had a highly unusual design. The results suggested that homeopathy was better than placebo.

2. Oberai, P. et al. Homoeopathic management of attention deficit hyperactivity disorder: a randomised placebo-controlled pilot trial. Indian J. Res. Homoeopathy 7, 158–167 (2013).

This one was published in an obscure journal that I could not access.

3. Jacobs, J., Williams, A. L., Girard, C., Njike, V. Y. & Katz, D. Homeopathy for attention-deficit/hyperactivity disorder: a pilot randomized-controlled trial. J. Altern. Complement. Med. 11, 799–806 (2005)

This study showed that there were no statistically significant differences between homeopathic remedy and placebo groups on the primary or secondary outcome variables.

4. Jones, M. The efficacy of homoeopathic simillimum in the treatment of attention-deficit/hyperactivity disorder (AD/HD) in schoolgoing children aged 6-11 years (2009).

This was a small unpublished (and not peer-reviewed) thesis. Its results showed no statistically significant effect of treatment.

5. Lamont, J. Homoeopathic treatment of attention deficit hyperactivity disorder. Br. Homeopathic J. 86, 196–200 (1997)

This was a small (n=46) trial with an unusual design. Its results suggested that homeopathy was better than placebo.

6. von Ammon, K. et al. Homeopathic RCT embedded in a long-term observational study of children with ADHD—a successful model of whole systems CAM research. Eur. J. Integr. Med. 1, 27 (2008).

Even though the journal is Medline-listed, I was unable to find this paper. I did, however, find a paper by the same authors with the same title. It turned out to be a duplication of the paper by Frei et al listed above.

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All in all, this brief analysis of the available abstracts (most full papers are behind paywalls) leaves many questions as to the trustworthiness of this systematic review unanswered. The fact that H. Walach (and other apologists of homeopathy) is its senior author does not inspire me with overwhelming confidence. In any case, I very much doubt that the authors’ conclusion is correct. I therefore would encourage someone with access to all full papers to initiate a more thorough analysis; the abstracts obviously leave many questions unanswered. For instance, it would be crucial to know how many of the trials followed an A+B versus B design (I suspect most studies did, and this would completely invalidate the review’s conclusion). I am more than happy to co-operate with such an evaluation.

Many systematic reviews have summarized the evidence on spinal manipulative therapy (SMT) for low back pain (LBP) in adults. Much less is known about the older population regarding the effects of SMT. This paper assessed the effects of SMT on pain and function in older adults with chronic LBP in an individual participant data (IPD) meta-analysis.

Electronic databases were searched from 2000 until June 2020; reference lists of eligible trials and related reviews were also searched. Randomized controlled trials (RCTs) were considered if they examined the effects of SMT in adults with chronic LBP compared to interventions recommended in international LBP guidelines. The authors of trials eligible for the IPD meta-analysis were contacted and invited to share data. Two review authors conducted a risk of bias assessment. Primary results were examined in a one-stage mixed model, and a two-stage analysis was conducted in order to confirm the findings. The main outcomes and measures were pain and functional status examined at 4, 13, 26, and 52 weeks.

A total of 10 studies were retrieved, including 786 individuals; 261 were between 65 and 91 years of age. There was moderate-quality evidence that SMT results in similar outcomes at 4 weeks (pain: mean difference [MD] – 2.56, 95% confidence interval [CI] – 5.78 to 0.66; functional status: standardized mean difference [SMD] – 0.18, 95% CI – 0.41 to 0.05). Second-stage and sensitivity analysis confirmed these findings.

The authors concluded that SMT provides similar outcomes to recommended interventions for pain and functional status in the older adult with chronic LBP. SMT should be considered a treatment for this patient population.

This is a fine analysis. Unfortunately, its results are less than fine. Its results confirm what I have been saying ad nauseam: we do not currently have a truly effective therapy for back pain, and most options are as good or as bad as the rest. This is most frustrating for everyone concerned, but it is certainly no reason to promote SMT as usually done by chiropractors or osteopaths.

The only logical solution, in my view, is to use those options that:

  • are associated with the least risks,
  • are the least expensive,
  • are widely available.

However you twist and turn the existing evidence, the application of these criteria does not come up with chiropractic or osteopathy as an optimal solution. The best treatment is therapeutic exercise initially taught by a physiotherapist and subsequently performed as a long-term self-treatment by the patient at home.

 

Practitioners of so-called alternative medicine (SCAM) often argue against treating back problems with drugs. They also frequently defend their own therapy by claiming it is backed by published guidelines. So, what should we think about guidelines for the management of back pain?

This systematic review was aimed at:

  1. systematically evaluating the literature for clinical practice guidelines (CPGs) that included the pharmaceutical management of non-specific LBP;
  2. appraising the methodological quality of the CPGs;
  3. qualitatively synthesizing the recommendations with the intent to inform non-prescribing providers who manage LBP.

The authors searched PubMed, Cochrane Database of Systematic Review, Index to Chiropractic Literature, AMED, CINAHL, and PEDro to identify CPGs that described the management of mechanical LBP in the prior five years. Two investigators independently screened titles and abstracts and potentially relevant full text were considered for eligibility. Four investigators independently applied the Appraisal of Guidelines for Research and Evaluation (AGREE) II instrument for critical appraisal. Data were extracted for pharmaceutical intervention, the strength of recommendation, and appropriateness for the duration of LBP.

Only nine guidelines with global representation met the eligibility criteria. These CPGs addressed pharmacological treatments with or without non-pharmacological treatments. All CPGs focused on the management of acute, chronic, or unspecified duration of LBP. The mean overall AGREE II score was 89.3% (SD 3.5%). The lowest domain mean score was for applicability, 80.4% (SD 5.2%), and the highest was Scope and Purpose, 94.0% (SD 2.4%). There were ten classifications of medications described in the included CPGs: acetaminophen, antibiotics, anticonvulsants, antidepressants, benzodiazepines, non-steroidal anti-inflammatory drugs (NSAIDs), opioids, oral corticosteroids, skeletal muscle relaxants (SMRs), and atypical opioids.

The authors concluded that nine CPGs, included ten medication classes for the management of LBP. NSAIDs were the most frequently recommended medication for the treatment of both acute and chronic LBP as a first line pharmacological therapy. Acetaminophen and SMRs were inconsistently recommended for acute LBP. Meanwhile, with less consensus among CPGs, acetaminophen and antidepressants were proposed as second-choice therapies for chronic LBP. There was significant heterogeneity of recommendations within many medication classes, although oral corticosteroids, benzodiazepines, anticonvulsants, and antibiotics were not recommended by any CPGs for acute or chronic LBP.

Oddly, this review was published by chiros in a chiro journal. The authors mention that nearly all guidelines the included CPGs recommended non-pharmacological treatments for non-specific LBP, however it was not always delineated as to precede or be used in conjunction with pharmacological intervention.

I find the review interesting because I think it suggests that:

  1. CPGs are not the most reliable form of evidence. Their guidance depends on how up-to-date they are and on the identity and purpose of the authors.
  2. Guidelines are therefore often contradictory.
  3. Back pain is a symptom for which currently no optimal treatment exists.
  4. The most reliable evidence will rarely come from CPGs but from rigorous, up-to-date, independent systematic reviews such as those from the Cochrane Collaboration.

So, the next time chiropractors osteopaths, acupuncturists, etc. tell you “BUT MY THERAPY IS RECOMMENDED IN THE GUIDELINES”, please take it with a pinch of salt.

This meta-analysis was conducted by researchers affiliated to the Evangelical Clinics Essen-Mitte, Department of Internal and Integrative Medicine, Faculty of Medicine, University of Duisburg-Essen, Germany. (one of its authors is an early member of my ALTERNATIVE MEDICINE HALL OF FAME). The paper assessed the safety of acupuncture in oncological patients.

The PubMed, Cochrane Central Register of Controlled Trials, and Scopus databases were searched from their inception to August 7, 2020. Randomized controlled trials in oncological patients comparing invasive acupuncture with sham acupuncture, treatment as usual (TAU), or any other active control were eligible. Two reviewers independently extracted data on study characteristics and adverse events (AEs). Risk of bias was assessed using the Cochrane Risk of Bias Tool.

Of 4590 screened articles, 65 were included in the analyses. The authors observed that acupuncture was not associated with an increased risk of intervention-related AEs, nonserious AEs, serious AEs, or dropout because of AEs compared with sham acupuncture and active control. Compared with TAU, acupuncture was not associated with an increased risk of intervention-related AEs, serious AEs, or dropout because of AEs but was associated with an increased risk for nonserious AEs (odds ratio, 3.94; 95% confidence interval, 1.16-13.35; P = .03). However, the increased risk of nonserious AEs compared with TAU was not robust against selection bias. The meta-analyses may have been biased because of the insufficient reporting of AEs in the original randomized controlled trials.

The authors concluded that the current review indicates that acupuncture is as safe as sham acupuncture and active controls in oncological patients. The authors recommend researchers heed the CONSORT (Consolidated Standards of Reporting Trials) safety and harm extension for reporting to capture the side effects and better investigate the risk profile of acupuncture in oncology.

You might think this article is not too bad. So, why do I feel that this paper is so bad?

One reason is that the authors included evidence up to August 2020. Since then, there must have been hundreds of further papers on acupuncture. The article was therefore out of date before it was published.

But that is by no means my main reason. We know from numerous investigations that acupuncture studies often fail to report AEs (and thus violate publication ethics). This means that this new analysis is merely an amplification of the under-reporting. It is, in other words, a means of perpetuating a wrong message.

Yes, you might say, but the authors acknowledge this; they even state in the abstract that “The meta-analyses may have been biased because of the insufficient reporting of AEs in the original randomized controlled trials.” True, but this fact does not erase the mistake, it merely concedes it. At the very minimum, the authors should have phrased their conclusion differently, e.g.: the current review confirms that AEs of acupuncture are under-reported in RCTs. Therefore, a meta-analysis of RCTs is unable to verify whether acupuncture is safe. From other types of research, we know that it can cause serious AEs.

An even better solution would have been to abandon or modify the research project when they first came across the mountain of evidence showing that RCTs often fail to mention AEs.

As it stands, the conclusion that acupuncture is as safe as sham acupuncture is simply not true. Since the article probably looks sound to naive readers, I feel that is a particularly good candidate for the WORST PAPER OF 2022 COMPETITION.

 

PS

For those who are interested, here are 4 of my own peer-reviewed articles on the safety of acupuncture (much more can, of course, be found on this blog):

  1. Patient safety incidents from acupuncture treatments: a review of reports to the National Patient Safety Agency – PubMed (nih.gov)
  2. Acupuncture–a critical analysis – PubMed (nih.gov)
  3. Prospective studies of the safety of acupuncture: a systematic review – PubMed (nih.gov)
  4. The risks of acupuncture – PubMed (nih.gov)

I know, transcutaneous electrical nerve stimulation (TENS) is not really a so-called alternative medicine (SCAM) but it is used by many SCAM practitioners and pain patients. It is, therefore, worth knowing whether it works.

This systematic review investigated the efficacy and safety of transcutaneous electrical nerve stimulation (TENS) for the relief of pain in adults. All randomized clinical trials (RCTs) were considered which compared strong non-painful TENS at or close to the site of pain versus placebo or other treatments in adults with pain, irrespective of diagnosis.

Reviewers independently screened, extracted data, and assessed the risk of bias (RoB, Cochrane tool) and certainty of evidence (Grading and Recommendations, Assessment, Development, and Evaluation). The outcome measures were the mean pain intensity and the proportions of participants achieving reductions of pain intensity (≥30% or >50%) during or immediately after TENS. Random effect models were used to calculate standardized mean differences (SMD) and risk ratios. Subgroup analyses were related to trial methodology and characteristics of pain.

The review included 381 RCTs (24 532 participants). Pain intensity was lower during or immediately after TENS compared with placebo (91 RCTs, 92 samples, n=4841, SMD=-0·96 (95% CI -1·14 to -0·78), moderate-certainty evidence). Methodological (eg, RoB, sample size) and pain characteristics (eg, acute vs chronic, diagnosis) did not modify the effect. Pain intensity was lower during or immediately after TENS compared with pharmacological and non-pharmacological treatments used as part of standard of care (61 RCTs, 61 samples, n=3155, SMD = -0·72 (95% CI -0·95 to -0·50], low-certainty evidence). Levels of evidence were downgraded because of small-sized trials contributing to imprecision in magnitude estimates. Data were limited for other outcomes including adverse events which were poorly reported, generally mild, and not different from comparators.

The authors concluded that there was moderate-certainty evidence that pain intensity is lower during or immediately after TENS compared with placebo and without serious adverse events.

This is an impressive review, not least because of its rigorous methodology and the large number of included trials. Its results are clear and convincing. In the words of the authors: “TENS should be considered in a similar manner to rubbing, cooling or warming the skin to provide symptomatic relief of pain via neuromodulation. One advantage of TENS is that users can adjust electrical characteristics to produce a wide variety of TENS sensations such as pulsate and paraesthesiae to combat the dynamic nature of pain. Consequently, patients need to learn how to use a systematic process of trial and error to select electrode positions and electrical characteristics to optimise benefits and minimise problems on a moment to moment basis.”

This systematic review and meta-analysis of clinical trials were performed to summarize the evidence of the effects of Urtica dioica (UD) consumption on metabolic profiles in patients with type 2 diabetes mellitus (T2DM).

Eligible studies were retrieved from searches of PubMed, Embase, Scopus, Web of Science, Cochrane Library, and Google Scholar databases until December 2019. Cochran (Q) and I-square statistics were used to examine heterogeneity across included clinical trials. Data were pooled using a fixed-effect or random-effects model and expressed as weighted mean difference (WMD) and 95% confidence interval (CI).

Among 1485 citations, thirteen clinical trials were found to be eligible for the current metaanalysis. UD consumption significantly decreased levels of fasting blood glucose (FBG) (WMD = – 17.17 mg/dl, 95% CI: -26.60, -7.73, I2 = 93.2%), hemoglobin A1c (HbA1c) (WMD = -0.93, 95% CI: – 1.66, -0.17, I2 = 75.0%), C-reactive protein (CRP) (WMD = -1.09 mg/dl, 95% CI: -1.64, -0.53, I2 = 0.0%), triglycerides (WMD = -26.94 mg/dl, 95 % CI = [-52.07, -1.82], P = 0.03, I2 = 90.0%), systolic blood pressure (SBP) (WMD = -5.03 mmHg, 95% CI = -8.15, -1.91, I2 = 0.0%) in comparison to the control groups. UD consumption did not significantly change serum levels of insulin (WMD = 1.07 μU/ml, 95% CI: -1.59, 3.73, I2 = 63.5%), total-cholesterol (WMD = -6.39 mg/dl, 95% CI: -13.84, 1.05, I2 = 0.0%), LDL-cholesterol (LDL-C) (WMD = -1.30 mg/dl, 95% CI: -9.95, 7.35, I2 = 66.1%), HDL-cholesterol (HDL-C) (WMD = 6.95 mg/dl, 95% CI: -0.14, 14.03, I2 = 95.4%), body max index (BMI) (WMD = -0.16 kg/m2, 95% CI: -1.77, 1.44, I2 = 0.0%), and diastolic blood pressure (DBP) (WMD = -1.35 mmHg, 95% CI: -2.86, 0.17, I2= 0.0%) among patients with T2DM.

The authors concluded that UD consumption may result in an improvement in levels of FBS, HbA1c, CRP, triglycerides, and SBP, but did not affect levels of insulin, total-, LDL-, and HDL-cholesterol, BMI, and DBP in patients with T2DM.

Several plants have been reported to affect the parameters of diabetes. Whenever I read such results, I cannot stop wondering whether this is a good or a bad thing. It seems to be positive at first glance, yet I can imagine at least two scenarios where such effects might be detrimental:

  • A patient reads about the antidiabetic effects and decides to swap his medication for the herbal remedy which is far less effective. Consequently, the patient’s metabolic control is insufficient.
  • A patient adds the herbal remedy to his therapy. Consequently, his blood sugar drops too far and he suffers a hypoglycemic episode.

My advice to diabetics is therefore this: if you want to try herbal antidiabetic treatments, please think twice. And if you persist, do it only under the close supervision of your doctor.

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