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

clinical trial

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In 2007, we published a systematic review summarizing the efficacy of homeopathic remedies used as a sole or additional therapy in cancer care. We have searched the literature using the databases: Amed (from 1985); CINHAL (from 1982); EMBASE (from 1974); Medline (from 1951); and CAMbase (from 1998). Randomized and non-randomized controlled clinical trials including patients with cancer or past experience of cancer receiving single or combined homeopathic interventions were included. The methodological quality of the trials was assessed by Jadad score. Six studies met our inclusion criteria (five were randomized clinical trials and one was a non-randomized study); but the methodological quality was variable including some high-standard studies. Our analysis of published literature on homeopathy thus found insufficient evidence to support the clinical efficacy of homeopathic therapy in cancer care.

Meanwhile, more trials have emerged, not least a dubious study by Frass et al which is currently under investigation. This means that a new evaluation of the totality of the available evidence might be called for. I am pleased to report that such an assessment has just been published.

In this systematic review, the researchers included clinical studies from 1800 until 2020 to evaluate evidence of the effectiveness of homeopathy on physical and mental conditions in patients during oncological treatment.

In February 2021 a systematic search was conducted searching five electronic databases (Embase, Cochrane, PsychInfo, CINAHL, and Medline) to find studies concerning the use, effectiveness, and potential harm of homeopathy in cancer patients.

From all 1352 search results, 18 studies with 2016 patients were included in this SR. The patients treated with homeopathy were mainly diagnosed with breast cancer. The therapy concepts include single and combination homeopathic remedies (used systemically or as mouth rinses) of various dilutions. Outcomes assessed were the influence on toxicity of cancer treatment (mostly hot flashes and menopausal symptoms), time to drain-removal in breast cancer patients after mastectomy, survival, quality of life, global health and subjective well-being, anxiety, and depression as well as safety and tolerance.

The included studies reported heterogeneous results: some studies described significant differences in quality of life or toxicity of cancer treatment favoring homeopathy, whereas others did not find an effect or reported significant differences to the disadvantage of homeopathy or side effects caused by homeopathy. The majority of the studies have low methodological quality.

The authors concluded that, for homeopathy, there is neither a scientifically based hypothesis of its mode of action nor conclusive evidence from clinical studies in cancer care.

I predict that, if we wait another 15 years, we will have even more studies. I also predict that some of them will be less than reliable or even fake. Finally, I predict that the overall result will still be mixed and unconvincing.

Why can I be so sure?

  1. Because homeopathy lacks biological plausibility as a treatment of cancer (or any other condition).
  2. Because highly diluted homeopathic remedies are pure placebos.
  3. Because homeopathy has developed into a cult where one is no longer surprised to see studies emerging that are too good to be true.

This multi-center, open-label, randomized controlled trial assessed the effects of anthroposophic treatments on toxicity related to intensive-phase chemotherapy treatment in children aged 1-18 with the primary outcome of the toxicity sum score. Secondary outcomes were chemotherapy-related toxicity, overall and event-free survival after 5 years in study patients.

The main sponsorship for the study was provided by: Helixor Heilmittel GmbH & Co. KG, Rosenfeld. Additional finacial support was provided by: WALA Heilmittel GmbH, Bad Boll/Eckwälden; Weleda AG, Schwäbisch Gmünd: Mahle Stiftung, Stuttgart; Software AG Stiftung, Darmstadt; Stiftung Helixor, Rosenfeld; and Injex Pharma AG, Berlin.

The intervention and control groups were both given standard chemotherapy according to malignancy & tumor type. The intervention arm was provided with anthroposophic supportive treatment (AST); given as anthroposophic base medication (AMP), as a base medication for all patients, and additional on-demand treatment tailored to the patient in the intervention groups. The control was given no AMP. The toxicity sum score (TSS) was assessed using NCI-CTC scales.

The AST consisted of base AMP including Helixor®, and on-demand supplementary AMP  given as needed for symptoms. Administration of the AST intervention and chemotherapy protocol were tailored for each type of pediatric malignancy included in the trial. This included both the base and the on-demand AMP, which were administered based on acute symptoms during intensive chemotherapy. The intervention group started the AST between the day of randomization and day 10 of the first chemotherapy cycle.

Data of 288 patients could be analyzed. The analysis did not reveal any statistically significant differences between the AST and the control group for the primary endpoint or the toxicity measures (secondary endpoints). Furthermore, groups did not differ significantly in the five-year overall and event-free survival follow-up.

The authors concluded that their findings showed that AST was able to be safely administered in a clinical setting, although no beneficial effects of AST between group toxicity scores, overall or event-free survival were shown.

In their discussion section, the authors explain the findings more clearly: “In the long term follow up, the explorative analysis of the data available for the 5-year follow up found no indications that efficacy of chemotherapy was influenced by AST. For long-term toxicities there were also no indications of an influence of AST.”

Question: what do we call a treatment that has neither adverse nor beneficial effects?

Could it be

PLACEBO?

It seems that no ancient treatment is daft enough for some researchers of so-called alternative medicine (SCAM) to not pick it up. Even bloodletting is back, it seems!

The aim of this study was to investigate the effects of therapeutic phlebotomy on ambulatory blood pressure in patients with grade 1 hypertension. In this randomized-controlled intervention study, patients with unmedicated hypertension grade 1 were randomized into an intervention group (phlebotomy group; 500 mL bloodletting at baseline and after 6 weeks) and a control group (waiting list) and followed up for 8 weeks. The primary endpoint was the 24-h ambulatory mean arterial pressure between the intervention and control groups after 8 weeks. Secondary outcome parameters included ambulatory/resting systolic/diastolic blood pressure, heart rate, and selected laboratory parameters (e.g., hemoglobin, hematocrit, erythrocytes, and ferritin). Resting systolic/diastolic blood pressure/heart rate and blood count were also assessed at 6 weeks before the second phlebotomy to ensure safety. A per-protocol analysis was performed.

Fifty-three hypertension participants (56.7 ± 10.5 years) were included in the analysis (n = 25 intervention group, n = 28 control group). The ambulatory measured mean arterial pressure decreased by -1.12 ± 5.16 mmHg in the intervention group and increased by 0.43 ± 3.82 mmHg in the control group (between-group difference: -1.55 ± 4.46, p = 0.22). Hemoglobin, hematocrit, erythrocytes, and ferritin showed more pronounced reductions in the intervention group in comparison with the control group, with significant between-group differences. Subgroup analysis showed trends regarding the effects on different groups classified by serum ferritin concentration, body mass index, age, and sex. Two adverse events (AEs) (anemia and dizziness) occurred in association with the phlebotomy, but no serious AEs.

The authors concluded that therapeutic phlebotomy resulted in only minimal reductions of 24-h ambulatory blood pressure measurement values in patients with unmedicated grade 1 hypertension. Further high-quality clinical studies are warranted, as this finding contradicts the results of other studies.

This paper requires a few short comments:

  1. The effect on blood pressure was not ‘minimal’, as the authors pretend, it was non-existent (i.e. not significant and due to chance only).
  2. This lack of effect had to be expected considering human physiology.
  3. The fact that hemoglobin, hematocrit, erythrocytes, and ferritin all change after bloodletting is equally expected.
  4. Mild adverse effects are also no surprise.
  5. What is a surprise, however, that such a trial was ever conducted and passed by an ethics committee. Any medic who has not slept through his/her cardiovascular physiology lectures could have predicted the results quite accurately. And running a trial where the result is well-known before the study has started can hardly be called ethical.

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.

_______________________________

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.

This article almost left me speechless:

The back-to-back waves of the COVID-19 pandemic have made a devastating impact globally. The conventional healthcare system is going through serious pressure as cases of the disease continue to spread and the numbers of hospitalizations are increasing every moment. It is becoming hard and challenging because the hospital resources are limited in number as compared with the rate of daily hospitalizations. There are significant shortages of patient care facilities and medical care providers, and on top of that, conventional healthcare systems do not have any proven treatments for COVID-19 patients. Experimental drugs like hydroxychloroquine, followed by remdesivir, ritonavir/lopinavir, and favipiravir are being administered under emergency use authorization (EUA). There is evidence that these experimental medications are causing adverse drug reactions, thus claiming the lives of the hospitalized COVID-19 patients. And those patients who survive the EUA medications and hospitalizations are left with iatrogenic immunosuppressive states leading to increased susceptibility towards secondary life-threatening infections like fungal diseases. In this scenario, complementary and alternative medical systems (CAMS) are providing commendable results with negligible adverse effects or iatrogenic issues in patients with COVID-19. There are several clinical cases recorded and published by various independent homoeopathic doctors and researchers worldwide. But unfortunately, because of a biased medical model and greed for monopolies, these effective treatment methods are not given equal opportunity as their conventional counterparts.

I think the best way to react to this nonsense might be to remind us what the only RCT of homeopathy for COVID showed.

This randomized, double-blind, two-armed, parallel, single-center, placebo-controlled study investigated the effectiveness and safety of the homeopathic medicine, Natrum muriaticum LM2, for mild cases of COVID-19.

Participants aged > 18 years, with influenza-like symptoms and a positive COVID test were recruited and randomized (1:1) into two groups that received different treatments during a period of at-home isolation. One group received the homeopathic medicine Natrum muriaticum, prepared with the second degree of the fifty-millesimal dynamization (LM2; Natrum muriaticum LM2), while the other group received a placebo.

The primary endpoint was time until recovery from COVID-19 influenza-like symptoms. Secondary measures included a survival analysis of the number and severity of COVID-19 symptoms (influenza-like symptoms plus anosmia and ageusia) from a symptom grading scale that was informed by the participant, hospital admissions, and adverse events. Kaplan-Meier curves were used to estimate time-to-event (survival) measures.

Data from 86 participants were analyzed (homeopathy, n = 42; placebo, n = 44). There was no difference in time to recovery between the two groups (homeopathy, n = 41; placebo, n = 41; P = 0.56), nor in a sub-group that had at least 5 moderate to severe influenza-like symptoms at the beginning of monitoring (homeopathy, n = 15; placebo, n = 17; P = 0.06). Secondary outcomes indicated that a 50% reduction in symptom score was achieved significantly earlier in the homeopathy group (homeopathy, n = 24; placebo, n = 25; P = 0.04), among the participants with a basal symptom score ≥ 5. Moreover, values of restricted mean survival time indicated that patients receiving homeopathy might have improved 0.9 days faster during the first five days of follow-up (P = 0.022). Hospitalization rates were 2.4% in the homeopathy group and 6.8% in the placebo group (P = 0.62). Participants reported 3 adverse events in the homeopathy group and 6 in the placebo group.

The authors concluded that the results showed that Natrum muriaticum LM2 was safe to use for COVID-19, but there was no statistically significant difference in the primary endpoints of Natrum muriaticum LM2 and placebo for mild COVID-19 cases. 

Another relevant study compared the antibody response of homeopathic and conventional vaccines and placebo in young adults. A placebo-controlled, double-blind RCT was conducted where 150 university students who had received childhood vaccinations were assigned to diphtheria, pertussis, tetanus, mumps, measles homeopathic vaccine, placebo, or conventional diphtheria, pertussis, tetanus (Tdap) and mumps, measles, rubella (MMR) vaccines. The primary outcome was a ≥ two-fold increase in antibodies from baseline following vaccination as measured by ELISA. Participants, investigators, study coordinators, data blood drawers, laboratory technicians, and data analysts were all blinded.

None of the participants in either the homeopathic vaccine or the placebo group showed a ≥ two-fold response to any of the antigens. In contrast, of those vaccinated with Tdap, 68% (33/48) had a ≥ two-fold response to diphtheria, 83% (40/48) to pertussis toxoid, 88% (42/48) to tetanus, and 35% (17/48) of those vaccinated with MMR had a response to measles or mumps antigens (p < 0.001 for each comparison of conventional vaccine to homeopathic vaccine or to placebo). There was a significant increase in geometric mean titres of antibody from baseline for conventional vaccine antigens (p < 0.001 for each), but none for the response to homeopathic antigens or placebo.

The authors concluded that homeopathic vaccines do not evoke antibody responses and produce a response that is similar to placebo. In contrast, conventional vaccines provide a robust antibody response in the majority of those vaccinated.

To give ‘equal opportunity’ to implausible therapies would, in my view, not merely be wrong, it would be scandalously unethical. The role of homeopathy in the prophylaxis and symptomatic management of COVID-19 or other infections is very easily described; it is:

zero,

nil,

nothing,

null,

naught,

zilch.

Two million people in UK are estimated to be currently suffering from long COVID, says the Office for National Statistics. Fatigue continues to be the most common symptom – experienced by 55% of those with self-reported long COVID – followed by 32% with shortness of breath, 23% with a cough, and 23% with muscle ache. The problem is only going to increase in the near future. Thus, many people are frantically looking for an effective therapy. Practitioners of so-called alternative medicine (SCAM) are no exception.

This study aimed to evaluate the potential for inhalation of essential oils to improve energy levels among otherwise healthy female survivors of acute COVID-19 who experience a lack of energy more than five months after recovery.

This was a randomized double-blind, placebo-controlled trial to evaluate the potential for inhalation of Longevity™, a proprietary essential oil blend manufactured by Young Living Essential Oils (Lehi, Utah, USA), on energy levels among female survivors of COVID-19 who continue to experience fatigue more than 5 months recovery from the acute infection. Forty women were randomized to two groups: intervention and placebo. The placebo product contained an inert, odorless fractionated coconut oil. Both groups inhaled the assigned product twice daily for fourteen consecutive days. Fatigue scores were measured using the Multidimensional Fatigue Symptom Inventory (MFSI). Secondary outcomes included scores on each of the MFSI’s ten subscales.

Individuals who inhaled the essential oil blend for 2 weeks had significantly lower fatigue scores after controlling for baseline scores, employment status, BMI, olfactory function, and time since diagnosis, with a large effect size (F (1,39) = 6.15, p = .020, partial eta squared = 0.198). Subscale analysis identified subscales of vigor, as well as global, behavioral, general, and mental fatigue as benefiting from the intervention. This study provides evidence that a proprietary aromatherapy blend can significantly improve energy levels among women who are experiencing fatigue after recovering from COVID-19.

The authors concluded that the use of aromatherapy with Longevity™ essential oil blend to boost energy levels in women who have recovered from COVID-19 provides a novel, non-invasive approach to improving quality of life in this population. This intervention is particularly beneficial for global and mental fatigue, as well as vigor. Other subdomains may experience improvements to energy levels with a smaller effect size; future studies should be conducted to explore this potential.

This trial was funded by Young Living Essential Oils. Perhaps, this explains why there is no mention of the elephant in the room: the trial was not blind! Participants in the verum group knew that they received aromatherapy. Likewise, participants in the placebo group knew that they received the placebo.

Could this fact have influenced the outcome? Certainly!

Could the trial have been designed better? Certainly!

All the investigators needed to do is to use a nice-smelling oil that, according to aromatherapists, does not boost energy, as the placebo.

As it stands, we have no idea whether the authors’ assumption that the verum oil caused the effect is true.

Pity!

Or maybe not?

Perhaps Young Living Essential Oils, the sponsor of the study and producer of the oil never wanted to know the truth. Maybe they are happy to abuse science as a marketing tool?

Naprapathy is an odd variation of chiropractic. To be precise, it has been defined as a system of specific examination, diagnostics, manual treatment, and rehabilitation of pain and dysfunction in the neuromusculoskeletal system. It is aimed at restoring the function of the connective tissue, muscle- and neural tissues within or surrounding the spine and other joints. The evidence that it works is wafer-thin. Therefore rigorous studies are of interest.

The aim of this study was to evaluate the cost-effectiveness of manual therapy compared with advice to stay active for working-age persons with nonspecific back and/or neck pain.

The two interventions were:

  • a maximum of 6 manual therapy sessions within 6 weeks, including spinal manipulation/mobilization, massage, and stretching, performed by a naprapath (index group),
  • information from a physician on the importance to stay active and on how to cope with pain, according to evidence-based advice, on 2 occasions within 3 weeks (control group).

A cost-effectiveness analysis with a societal perspective was performed alongside a randomized controlled trial including 409 persons followed for one year, in 2005. The outcomes were health-related Quality of Life (QoL) encoded from the SF-36 and pain intensity. Direct and indirect costs were calculated based on intervention and medication costs and sickness absence data. An incremental cost per health-related QoL was calculated, and sensitivity analyses were performed.

The difference in QoL gains was 0.007 (95% CI – 0.010 to 0.023) and the mean improvement in pain intensity was 0.6 (95% CI 0.068-1.065) in favor of manual therapy after one year. Concerning the QoL outcome, the differences in mean cost per person were estimated at – 437 EUR (95% CI – 1302 to 371) and for the pain outcome the difference was – 635 EUR (95% CI – 1587 to 246) in favor of manual therapy. The results indicate that manual therapy achieves better outcomes at lower costs compared with advice to stay active. The sensitivity analyses were consistent with the main results.

Cost-effectiveness plane using bootstrapped incremental cost-effectiveness ratios for QoL and pain intensity outcomes

The authors concluded that these results indicate that manual therapy for nonspecific back and/or neck pain is slightly less costly and more beneficial than advice to stay active for this sample of working age persons. Since manual therapy treatment is at least as cost-effective as evidence-based advice from a physician, it may be recommended for neck and low back pain. Further health economic studies that may confirm those findings are warranted.

This is an interesting and well-conducted study. The differences between the groups seem small and of doubtful relevance. The authors acknowledge this fact by stating: “together with the clinical results from previously published studies on the same population the results suggest that manual therapy may be as cost-effective a treatment as evidence-based advice from a physician, for back and neck pain”. Moreover, the data do not convince me that the treatment per se was effective; it might have been the non-specific effects of touch and attention.

I have said it before: there is currently no optimal treatment for neck and back pain. Therefore, the findings even of rigorous cost-effectiveness studies will only generate lukewarm results.

Osteopathic visceral manipulation (VM) is a bizarre so-called alternative medicine (SCAM) that has been featured on this blog with some regularity, e.g.:

Rigorous trials fail to show that it works for anything. So, the obvious solution to this dilemma is to conduct dodgy trials!

This study tested the effects of VM on dysmenorrhea, irregular, delayed, and/or absent menses, and premenstrual symptoms in PCOS patients.

Thirty Egyptian women with polycystic ovary syndrome (PCOS), with menstruation-related complaints and free from systematic diseases and/or adrenal gland abnormalities, participated in a single-blinded, randomized controlled trial. They were recruited from the women’s health outpatient clinic in the faculty of physical therapy at Cairo University, with an age of 20-34 years, and a body mass index (BMI) ≥25, <30 kg/m2. Patients were randomly allocated into two equal groups (15 patients); the control group received a low-calorie diet for 3 months, and the study group that received the same hypocaloric diet added to VM to the pelvic organs and their related structures for eight sessions over 3 months. Evaluations for body weight, BMI, and menstrual problems were done by weight-height scale, and menstruation-domain of Polycystic Ovary Syndrome Health-Related Quality of Life Questionnaire (PCOSQ), respectively, at baseline and after 3 months from interventions. Data were described as mean, standard deviation, range, and percentage whenever applicable.

Of 60 Egyptian women with PCOS, 30 patients were included, with baseline mean age, weight, BMI, and a menstruation domain score of 27.5 ± 2.2 years, 77.7 ± 4.3 kg, 28.6 ± 0.7 kg/m2, and 3.4 ± 1.0, respectively, for the control group, and 26.2 ± 4.7 years, 74.6 ± 3.5 kg, 28.2 ± 1.1 kg/m2, and 2.9 ± 1.0, respectively, for the study group. Out of the 15 patients in the study group, uterine adhesions were found in 14 patients (93.3%), followed by restricted uterine mobility in 13 patients (86.7%), restricted ovarian/broad ligament mobility (9, 60%), and restricted motility (6, 40%). At baseline, there was no significant difference (p>0.05) in any of the demographics (age, height), or dependent variables (weight, BMI, menstruation domain score) among both groups. Post-study, there was a statistically significant reduction (p=0.000) in weight, and BMI mean values for the diet group (71.2 ± 4.2 kg, and 26.4 ± 0.8 kg/m2, respectively) and the diet + VM group (69.2 ± 3.7 kg; 26.1 ± 0.9 kg/m2, respectively). For the improvement in the menstrual complaints, a significant increase (p<0.05) in the menstruation domain mean score was shown in the diet group (3.9 ± 1.0), and the diet + VM group (4.6 ± 0.5). On comparing both groups post-study, there was a statistically significant improvement (p=0.024) in the severity of menstruation-related problems in favor of the diet + VM group.

The authors concluded that VM yielded greater improvement in menstrual pain, irregularities, and premenstrual symptoms in PCOS patients when added to caloric restriction than utilizing the low-calorie diet alone in treating that condition.

WHERE TO START?

  • Tiny sample size.
  • A trail design (A+B vs B) which will inevitably generate a positive result.
  • Questionable ethics.

VM is a relatively invasive and potentially embarrassing intervention for any woman; I imagine that this is all the more true in Egypt. In such circumstances, it is mandatory to ask whether a planned study is ethically justifiable. I would answer this question related to an implausible treatment like VM with a straight NO!

I realize that there may be people who disagree with me. But even those guys should accept that, at the very minimum, such a study must be designed such that it leads to a clear answer – is VM effective or not? The present trial merely suggests that the placebo effect associated with VM is powerful (which is hardly surprising for a therapy like VM).

Acupuncture is often promoted as a therapeutic option for obesity and weight control. The aim of this study was to investigate the effects of electroacupuncture (EA) on body weight, body mass index (BMI), skin fold thickness, waist circumference and skin temperature of the abdominal region in non-obese women with excessive abdominal subcutaneous fat.

A total of 50 women with excessive abdominal subcutaneous fat (and average BMI of 22) were randomly assigned to one of two groups:

  1. an EA group (n = 25) receiving 10 EA sessions (insertion of needles connected to an electrical stimulator at a frequency of 40 Hz for 40 min),
  2. a control group (n = 25) that received no treatment.

Outcome measures evaluated included waist circumference, supra-iliac and abdominal skinfolds, body composition and superficial skin temperature (measured by cutaneous thermography) before and after treatment.

Compared with the untreated group, women in the EA group exhibited decreased supra-iliac and abdominal skin folds (p < 0.001), waist circumference (p < 0.001), percentage body fat (p = 0.001) and percentage abdominal fat (p < 0.001). In addition, the EA group showed an elevated skin temperature at the site of the treatment. However, EA did not significantly impact body weight (p = 0.01) or BMI (p = 0.2).

The authors concluded that EA promoted a reduction in abdominal waist circumference, supra-iliac and abdominal skin folds, and percentage body and abdominal fat in women of normal BMI with excessive abdominal subcutaneous fat, as well as an increase in the superficial skin temperature of the abdominal region.

If we did not know that acupuncture researchers were all honest investigators testing hypotheses the best they can, we could almost assume that some are trying to fool us. The set-up of this study is ideally suited to introduce a proper placebo treatment. All one has to do is to not switch on the electrical stimulator in the control group. Why did the researchers not do that? Surely not because they wanted to increase the chances of generating a positive result; that would have been dishonest!!!

So, as it stands, what does the study tell us? I think it shows that, compared to patients who receive no treatment, patients who do receive the ritual of EA are better motivated to adhere to calorie restrictions and dietary advice. Thus, I suggest to re-phrase the conclusions of this trial as follows:

The extra attention of the EA treatment motivated obese patients to eat less which caused a reduction in abdominal waist circumference, supra-iliac and abdominal skin folds, and percentage body and abdominal fat in women of normal BMI with excessive abdominal subcutaneous fat.

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