symptom-relief
The rapid expansion of mindfulness research has generated both enthusiasm and controversy regarding its actual clinical value. While meditation is often regarded as the central mechanism of mindfulness-based interventions, other components such as psychoeducation and informal practice may play an equally significant role in improving mental health outcomes.
This critical review examined the relative contributions of these elements to the therapeutic impact of mindfulness and clarifies the extent to which its effects are comparable to established treatments, particularly Cognitive Behavioral Therapy (CBT).
Evidence from meta-analyses and high-quality trials indicated that mindfulness programs achieve moderate efficacy in reducing symptoms of anxiety, depression, and stress, but effect sizes are frequently inflated by the methodological limitations of the studies. Importantly, cognitive and emotional regulation skills, especially acceptance and non-judgment, appear to sustain long-term benefits more consistently than meditation alone.
The authors point out that high-quality studies tend to report smaller effect sizes for mindfulness meditation compared to studies with methodological limitations. This suggests that the benefits of it may have been overestimated in less robust research. However, even in well-controlled trials, meditation has shown moderate effects in reducing stress and anxiety, highlighting its potential therapeutic value while reinforcing the need for continued scrutiny of its long-term impact and mechanisms of action.
Mindfulness meditation is often regarded as the central component of mindfulness programs, yet its role should be critically examined in relation to other key elements. While some studies highlight meditation as a primary mechanism for short-term reductions in stress and anxiety, others suggest that cognitive and behavioral learning processes may play an equally or even more significant role in sustaining long-term benefits. This raises important questions about whether meditation alone is sufficient to drive mindfulness-related improvements or if its effects are dependent on complementary psychoeducational and cognitive strategies.
The authors concluded that the primary challenge in mindfulness-based interventions is determining which aspects are responsible for contributing to their effectiveness, and what mechanisms may be at work. While meditative practice, often associated with mindfulness training and stress reduction, has demonstrated benefits in alleviating symptoms of anxiety and depression, a critical question remains: is meditation alone sufficient to sustain these effects over time, or are additional cognitive, emotional, and behavioral factors necessary? Understanding whether the long-term benefits of mindfulness stem from mindfulness meditation alone, or also from additional contributions from complementary psychological processes, is essential for refining its clinical applications and preventing its overgeneralization as a universal remedy.
Recent high-quality evidence continues to support the moderate but consistent clinical efficacy of MBIs across populations and settings. However, these benefits appear to depend not only on meditation but also on psychoeducational and cognitive–behavioral elements that promote acceptance, non-judgment, and emotional regulation. Such skills have shown comparable or even greater contributions to long-term mental health outcomes than formal meditation practice alone.
Although mindfulness-based interventions have demonstrated effectiveness in reducing anxiety and depression, direct comparisons with Cognitive Behavioral Therapy (CBT) remain limited. Evidence from recent meta-analyses suggests that both approaches may yield comparable therapeutic outcomes, possibly through shared mechanisms involving cognitive restructuring and self-regulation. In contrast, findings on Transcendental Meditation (TM) are more heterogeneous and should be interpreted with caution, as TM differs conceptually and methodologically from mindfulness-based approaches. Nonetheless, further well-controlled, longitudinal research is required to clarify whether sustained meditation practice provides additional or distinct long-term advantages.
The psychoeducational components of mindfulness, which encourage present-moment awareness and a non-judgmental attitude, may play a significant role in reducing rumination—a core mechanism underlying anxiety and depression. This raises the question of whether long-term symptom improvement is primarily driven by the internalization of these cognitive and emotional strategies rather than by meditation itself.
Overall, mindfulness-based interventions show moderate clinical efficacy, with outcomes highly dependent on their specific components—meditation, psychoeducation, and informal practice. Cognitive and emotional regulation skills such as acceptance and non-judgment may be the most critical drivers of long-term well-being. Identifying how these elements interact to sustain psychological benefits is key for optimizing intervention design and ensuring mindfulness remains a scientifically grounded and contextually adaptable therapeutic tool.
I have often commented on what I see as the current hype around mindfulness. To me, the evidence suggests that it is not nearly as effective as its proponents are trying to make it out to be. Much of the observed outcomes are due to expectation and conditioning, in other words, they are caused by a placebo response. Yet, I think the authors of this review have a point, even though they seem not very good at making it concisely.
The objective of this study was to “critically assess the evidence presented in randomized controlled trials (RCTs) about the effectiveness of acupuncture on fatigue in cancer patients”. In April 2024 a systematic search was conducted searching five electronic databases to find studies concerning the use, effectiveness and potential harm of acupuncture therapy on cancer patients.
From all (1599) search results, 15 studies with 1346 patients were included. Acupuncture methods varied – e.g., traditional-, electro-, mind-regulating and ATAS-acupuncture – and were compared to sham acupuncture, usual care, or other controls.
- Studies comparing acupuncture to sham acupuncture reported mixed results: while some found significant effects on cancer-related fatigue, others found no advantages.
- Studies comparing acupuncture to usual care or waitlist controls often reported positive effects. However, the reliability of these findings is limited, as 14 of 15 studies were rated as “high risk of bias” by the RoB-2 tool due to issues like insufficient blinding and incomplete data analysis.
- Only one study, with low risk of bias, showed a significant reduction in fatigue with acupuncture compared to sham acupuncture (p < 0.001).
- GRADE evaluation showed very low certainty of evidence.
The authors concluded that the heterogenous results and methodological limitations of the existing studies prevent us from drawing definitive conclusions about the effectiveness of acupuncture in the treatment of cancer-related fatigue. Despite the inclusion of 15 studies, the overall evidence remains insufficient due to widespread problems in study design and inconsistent results. This analysis highlights the need to use more rigorous designs and more comprehensive assessment tools in future studies to better understand the role of acupuncture in the management of fatigue after cancer treatment.
So, only one study, with low risk of bias, showed a significant reduction in fatigue with acupuncture compared to sham acupuncture. Let’s have a look at it:
Background: Cancer-related fatigue (CRF) is a distressing symptom that is the most common unpleasant side effect experienced by lung cancer patients and is challenging for clinical care workers to manage.
Methods: We performed a randomized, double-blind, placebo-controlled pilot trial to evaluate the clinical effect of acupuncture on CRF in lung cancer patients. Twenty-eight patients presenting with CRF were randomly assigned to active acupuncture or placebo acupuncture groups to receive acupoint stimulation (LI-4, Ren-6, St-36, KI-3, and Sp-6) twice per week for 4 weeks, followed by 2 weeks of follow-up. The primary outcome was the change in intensity of CFR based on the Chinese version of the Brief Fatigue Inventory (BFI-C). As the secondary endpoint, the Functional Assessment of Cancer Therapy-Lung Cancer Subscale (FACT-LCS) was adopted to assess the influence of acupuncture on patients’ quality of life (QOL). Adverse events and safety of treatments were monitored throughout the trial.
Results: Our pilot study demonstrated feasibility among patients with appropriate inclusion criteria and good compliance with acupuncture treatment. A significant reduction in the BFI-C score was observed at 2 weeks in the 14 participants who received active acupuncture compared with those receiving the placebo (P < 0.01). At week 6, symptoms further improved according to the BFI-C (P < 0.001) and the FACT-LCS (P = 0.002). There were no significant differences in the incidence of adverse events in either group (P > 0.05).
Conclusion: Fatigue is a common symptom experienced by lung cancer patients. Acupuncture may be a safe and feasible optional method for adjunctive treatment in cancer palliative care, and appropriately powered trials are warranted to evaluate the effects of acupuncture.
Fancy that! The only study to produce some apparently sound evidence turns out to be a pilot study. Such studies are supposed to test feasibility, not effectiveness! In view of all this, it is far, I think, to draw a definitive conclusion, after all:
At present there is no compelling evidence that acupuncture works for cancer-related fatigue.
This study compared the analgesic efficacy of acupressure and magnetic therapy (AMT) versus diclofenac sodium (DFS) in acute renal colic. A total of 138 patients with acute renal colic (visual analog scale [VAS] score ≥ 7) were randomized to AMT or DFS treatment. Primary endpoints included changes in VAS scores at baseline, 1-, 10-, 30-, and 120-min post-intervention, along with analgesic duration. Multiple linear regression evaluated the influence of treatment modality, gender, white blood cell (WBC) count, and other covariates on VAS scores at 10 min. Interaction effect analysis was additionally used to assess how these factors modified treatment efficacy.
The AMT group demonstrated rapid onset, achieving an 86 % VAS reduction at 1-min post-intervention (vs. baseline, P < 0.001), though pain rebound occurred after 30 min. The DFS group exhibited slower onset but significantly prolonged analgesic duration compared to AMT (23.6 ± 2.2 h vs. 2.4 ± 1.0 h, P < 0.001). Multiple linear regression revealed that AMT had the best analgesic effect (B = -6.22, P < 0.001). Male gender (B = 0.78, P = 0.026) and lower baseline WBC counts (B = -0.16, P = 0.026) were associated with higher VAS scores. Interaction analysis indicated enhanced AMT efficacy in male patients and those with lower WBC counts.
The authors concluded that AMT and DFS exhibit complementary “rapid-sustained” analgesic profiles in renal colic management, with gender and WBC levels significantly modulating treatment efficacy. A stratified analgesia protocol based on these factors may optimize patient outcomes.
Apart from the fact that, as an equivalence trial, the study is hopelessly underpowered and its results therefore less than reliable, I have a further reason for not trusting its findings.
A renal colic is an acute and severe loin pain caused by a urinary stone moving from the kidney downwards into the ureter. The pain is often resistant to DFS or other conventional pain-killers and might require opioids. The pain usually peaks sharply, lasts for 20 to 60 minutes, and then subsides into a dull ache before the next “wave” begins. These waves are caused by the ureter’s peristalsis—the tube’s rhythmic muscular contractions—as it tries to squeeze the stone toward the bladder.
So, all I need to do to fake the effectivenesss of a so-called alternative medicine (SCAM) like AMT is to start treating patients when a wave is subsiding. This can easily appear as though AMT had a remarkable effect of 86%. Subsequently, the pain will recur. And this is probably what happened in this study! What I am trying to convey is that I am not convinced that AMT did much at all.
Moreover, I find it daft to conduct a trial where two SCAMs are tested together in one single treatment arm. Even if one would be convinced of the value of AMT – which I am not! – one would need to ask: was it the acupressure or the magnetic therapy that did the trick?
My conclusion is therefore yet again: if you design a silly study, you get a silly result.
Many families explore so-called alternative medicine (SCAM) to manage autism spectrum disorder (ASD) and many SCAM practitioners claim to be able to treat ASD effectively. This review evaluated the efficacy and safety of SCAM therapies, including acupuncture, cupping, massage, dietary changes, herbal medicine, apitherapy, and Ayurveda medicine.
Systematic searches were carried out in PubMed, Scopus, and Web of Science to identify studies of SCAM interventions for ASD. The review adhered to Preferred Reporting Items for Systematic Reviews and Meta-Analyses guidelines, including various study types. Data extraction focused on design, population, intervention, outcomes, and bias risk.
The inclusion criteria were met by 45 studies, which encompassed six SCAM modalities. Acupuncture and massage consistently exhibited enhancements in sensory processing, communication, and social interaction levels. Dietary interventions, particularly probiotic supplementation and gluten-/casein-free regimens, had beneficial effects on behavioral and GI domains. While Ayurveda therapies such as Medhya Rasayanas (Bacopa monnieri), Swarnaprashana, and Panchakarma techniques improved cognition and reduced social deficits in small clinical series, herbal and apitherapy treatments primarily demonstrated neuroprotective and anti-inflammatory effects in preclinical studies. Control groups received no treatment, sham interventions, or standard care. The methodological limitations and heterogeneity of the study design limited the ability to draw definitive conclusions.
The authors conclused that the evidence indicates that SCAM approaches, including acupuncture, massage, and Ayurveda therapies, may be effective adjuncts in the management of ASD. The current body of research is constrained by the moderate-to-high risk of bias, variable protocols, and small sample sizes. Standardized, large-scale randomized trials are required to establish efficacy and safety. Clinicians should balance patient safety with innovation by adopting an integrative, evidence-informed approach.
This is almost complete nonsense:
- The authors claim to have followed the PRISMA guidelines. As one of the co-authors of these guidelines, I can affirm that this is untrue.
- The authors included 10 animal studies that provided mechanistic support for clinical findings, 18 RCTs, 12 pre-post controlled studies, and 5 case series or pilot studies comprised the designs. Several of these study types are unable to “evaluate the efficacy and safety of SCAM therapies” which is the stated aim of the review.
- Most of the included studies fail to control for placebo effects. Therefore, they cannot provide evidence regarding the “efficacy” of the treatments in question.
In view of these – and many other – flaws of the review, I fear that I might have to re-write the conclusions:
Many SCAMs have been studied as treatments for ASD. The results of these investigations fail to show that any of them is effective in alleviating the symptoms of ASD. Unless sound evidence emerges, SCAM cannot be recommended for ASD.
Non-specific low back pain is a common condition with substantial socioeconomic implications. Pulsed electromagnetic field (PEMF) therapy is said to generate benefits in pain reduction and improvement of physical function in patients with pain-associated disorders like osteoarthritis. However, studies had heterogeneous settings. The aim of this systematic review was to assess the effects of PEMF on pain and function on patients with non-specific low back pain.
A systematic literature search of randomized controlled trials in PubMed, MEDLINE, EMBASE, Cochrane Library, and PEDro was performed (from inception until 15/5/2023). Outcome measures assessed pain and function.
Nine randomized controlled trials with 420 participants (n = 420) were included. The studies compared PEMF vs. placebo-PEMF, PEMF and conventional physical therapy vs. conventional physical therapy alone, PEMF and conventional physical therapy vs. placebo-PEMF and conventional physical therapy, PEMF vs. high-intensity laser therapy (HILT) vs. conventional physical therapy, and osteopathic manipulative treatment (OMT) and PEMF vs. PEMF alone vs. placebo-PEMF vs. OMT alone. Five of the nine included studies showed statistically significant pain reduction and improvement in physical function in comparison to their control groups (p < 0.05). There was substantial heterogeneity among the groups of the study, with a wide range of duration (10-30 min), treatments per week (2-7/week), applied frequencies (3-50 Hz), and intensities (2mT-150mT). No serious adverse event had been reported in any study. The included studies showed solid methodological quality, with an overall score of 7.2 points according to the PEDro scale.
The authors concluded that the results of the present systematic review suggest that the use of PEMF for patients with non-specific low back pain is beneficial in terms of pain reduction and enhancement of physical function, particularly if used as an addition to conventional physical therapy modalities. It has also been shown that PEMF is a safe therapy for the treatment of non-specific low back pain. Further high-quality studies with larger sample sizes and standardized protocols are necessary. The studies should also focus on determining the optimal parameters of frequency and intensity to advance PEMF application for all pain disorders.
PEMF therapy is a non-invasive treatment widely used by physiotherapist and some practitioners of so-called alternative medicine (SCAM). It applies low-frequency electromagnetic waves to the body. PEMF therapy acts like a wireless charger for your body, sending pulses of energy that penetrate deep into your tissues to jumpstart cellular recovery. Because your body contains conductive fluids (like blood) and charged ions (like calcium and potassium), the PEMF device is said to induce very small electrical currents within your tissues. In turn, the induced current is claimed to stimulate the mitochondria. This, according to proponents, boosts the production of ATP. The pulses are also said to influence the movement of ions across cell membranes, particularly calcium which triggers a cascade of beneficial biochemical reactions, such as the release of nitric oxide, which dilates blood vessels to improve circulation. Lastly, PEMF are claimed to help “calm” the chemical signals that cause chronic inflammation, switching the cellular environment from a state of stress to a state of healing.
While these assumptions look like wild extrapolations, the more crucial question is whether PEMF is clinically effective. The present review seems to tell us that it works for back pain. Yet, I am not convinced.
Most of the RCTs are not of good quality. Many did not blind patients or therapists. Only 2 made a direct comparison against a placebo, and those did not blind patients or check the success of blinding them. As the authors noted, there is plenty of heterogeneity in the included RCTs. All this adds up to a high level of uncertainty about the effectiveness of PEMF.
In summary, I fear that the authors of this review are too optimistic and lack critical thinking in evaluating the existing evidence. My conclusion therefore differs from theirs:
Many RCTs suggest that PEMF is effective for non-specific low back pain. Yet, due to serious limitations of the primary studies, no firm conclusion can be drawn.
The authors found very low‐certainty evidence (downgraded for study limitations, inconsistency, and imprecision) that SMT may result in a medium reduction in pain compared to no treatment at one month (MD ‐13.99, 95% CI ‐27.33 to ‐0.66; I2 = 89%; 4 studies, 325 participants), but the evidence is very uncertain. They found low‐certainty evidence (downgraded for study limitations and imprecision) that SMT may result in a large improvement in functional status compared to no treatment at one month (SMD ‐0.84, 95% CI ‐1.32 to ‐0.35; I2 = 71%; 4 studies, 312 participants).
SMT versus other conservative interventions
Low‐certainty evidence (downgraded for inconsistency) indicated that SMT may result in little to no difference in pain (MD ‐4.72, 95% CI ‐8.26 to ‐1.17; I2 = 89%; 31 studies, 4109 participants) and may result in a small improvement in functional status (SMD ‐0.25, 95% CI ‐0.38 to ‐0.11; I2 = 73%; 28 studies, 3940 participants) compared to other conservative interventions at one month.
These effects, however, should be interpreted with caution due to the substantial statistical heterogeneity for which there is no clear explanation.
Less than half of the studies (47%) reported on adverse events, of which 12 studies reported these systematically. Adverse events in the SMT group were limited to muscle soreness, stiffness, and/or transient increase in pain. None of the studies registered any serious complications related to either the experimental or control group treatment. The evidence is very uncertain about the adverse effects of SMT.
Authors’ conclusions: When SMT is compared to sham SMT/placebo, it may result in a small improvement in pain and medium improvement in functional status in adults with chronic low back pain. When compared to no treatment, SMT may result in a medium improvement in pain and a large improvement in functional status. When compared to other conservative interventions, SMT may result in little to no difference in pain and a small improvement in functional status. The evidence is of low to very low certainty, largely due to the fact that the effects of SMT were examined in trials conducted in different settings and populations, with different types of SMT technique, dosage, and frequency of treatment. Continuing to conduct RCTs in the same manner will neither strengthen the evidence nor our confidence in it.
Once again, it has been confirmed that most trials of SMT are, because of their failure to report adverse effects, in violation of ethical standards. But the importance of this excellent review lies elsewhere. Despite 76 published RCTs, there is huge uncertainty about the benefits of SAM. What should we make of this fact?
In my view, it highlights that:
- the studies are often of poor quality;
- the effect of SMT are so small that they are negligibel;
- patients with back pain should look for treatments that are safe and effective;
- the choice can therefore not be SMT.
Opioid withdrawal involves sympathetic hyperactivity and reduced parasympathetic tone, which standard pharmacological treatments may not adequately address, contributing to relapse vulnerability. This study evaluated yoga as adjuvant therapy to accelerate opioid withdrawal recovery and assess its impact on heart rate variability, anxiety, sleep, and pain.
This 2-arm, early-stage randomized clinical trial was conducted at an addiction medicine inpatient ward in India from April 30, 2023 to March 31, 2024. The outcome assessors and data analyst were blinded to group allocation. Participants included adults aged 18 to 50 years with opioid use disorder experiencing mild to moderate withdrawal symptoms (Clinical Opiate Withdrawal Scale [COWS] scores 4-24). Exclusion criteria included severe withdrawal, neurological conditions affecting autonomic function, severe psychiatric conditions, and recent yoga training. Of 68 individuals screened, 59 were randomized (30 yoga and 29 control participants).
Participants in the yoga group received (A) 10 supervised 45-minute sessions during 14 days alongside (B) standard buprenorphine treatment, including relaxation practices, postures, breathing techniques, and guided relaxation. Participants in the control group received (B) standard buprenorphine treatment only. Co-primary outcomes included time to withdrawal stabilization (COWS score <4) and heart rate variability parameters. Secondary outcomes included anxiety (Hamilton Anxiety Rating Scale), sleep latency, and pain scores. Assessments were conducted at baseline (day 1) and day 15.
Fifty-nine participants (59 male [100%]; mean [SD] age, 25.6 [3.9] years) completed intent-to-treat analysis. Participants in the yoga group recovered faster than those in the control group (hazard ratio [HR], 4.40; 95% CI, 2.40-8.07; P < .001), with a median stabilization time of 5 days (95% CI, 4-6 days) for those in the yoga group vs 9 days (95% CI, 7-13 days) for the control group. Participants in the yoga group showed superior heart rate variability improvements with large effects on low frequency (LF) power (ω2 = 0.16), high frequency (HF) power (ω2 = 0.14), and LF/HF ratio (ω2 = 0.12); all effects were statistically significant (P < .001). Mediation analysis showed that increases in parasympathetic activity accounted for 23% of the treatment effect (indirect HR, 1.38; 95% CI, 1.10-2.03). Anxiety reduction was significantly greater among those in the yoga group (ω2 = 0.28; P < .001), with moderate improvements in sleep latency (a 61-minute reduction; P = .008) and pain (P = .004).
The authors concluded that in this randomized clinical trial, yoga significantly accelerated opioid withdrawal recovery and improved autonomic regulation, anxiety, sleep, and pain. These findings support integrating yoga into withdrawal protocols as a neurobiologically informed intervention addressing core regulatory processes beyond symptom management.
This conclusion is demonstrably wrong, and I am dismayed that a reputable journal published it.
The study followed the infamous ‘A+B versus B’ design. It is infamous because it is seemingly rigorous (“A RANDOMIZED CLINICAL TRIAL”!!!), while invariably generating a positive result for the tested intervention – even if it happens to be nothing more than a placebo tretment. And because of this, it is, in my view, unethical to use it for concluding about the specific effects of the tested intervention. I have explained this so often that I hesitate to do it again:
- Imagine the treatments as two amounts of money.
- Amount (treatmet) A equals £1.
- Amount (treatment) B equals £2.
- If one (the verum) group gets A+B, it will have £3.
- If the other (control) group gets just £2, it will have £2.
- A+B is always more that B.
- If A is a placebo, the A+B > B still applies, due to the existance of placebo effects
- QED!
The crux is obviously that the A+B vs B design only appears to be rigorous but, in fact, does NOT control for placebo effects. Since placebo effects exist, the A+B vs B design must produce a positive result, even if the verum is ineffective and merely generates a placebo response.
As the type of yoga employed in this study is bound to generate a sizable placebo effect, it would easily be enought to cause the observed outcomes. Let me put it even more bluntly: this study design is unable to tell us whether the yoga therapy or a placebo response was responsible for the observed result*.
In view of this, I will re-formuate the first sentence of the conclusion as follows:
In this randomized clinical trial, a placebo effect accelerated opioid withdrawal recovery and improved autonomic regulation, anxiety, sleep, and pain.
But what about the 2nd sentence of the conclusion?
Arguably, it is even worse!
To claim that the findings of one single study sufiice for calling for the integration of the tested treatment into routine healthcare ignores the need for independent replications and is therefore dangerous nonsense.
*(Btw: this is also the reason why it is so popular with pseudoscientists trying to show that their pet therapy works.]
This study aimed to evaluate the comparative effectiveness of “fire cupping therapy” (FC) versus electroacupuncture for reducing pain and improving cervical spine range of motion in patients with neck pain due to cervical spondylosis. FC is essentially nothing else than the TCM version of cupping.
Eighty-two participants with neck pain caused by cervical spondylosis were randomly allocated in 1:1 ratio to either the fire cupping (FC) or the electroacupuncture (EA) group. Both groups received treatment at the EX-B2, A-shi, and GB21 acupuncture points. The two-week study assessed pain levels using the Visual Analog Scale (VAS) at 2 points in time post-intervention and evaluated adverse effects weekly.
After 2 weeks of intervention, VAS scores significantly decreased in both the FC group (from 6 (6–7) to 3 (2–3)) and the EA group (from 6 (6–7) to 2 (1–3)) (p<0.001). However, inter-group pain relief was not statistically significant (p = 0.5794, Cohen’s d = 21 0.12; 95% CI [-0.31–0.6]). Both groups showed statistically significant ROM improvement (p<0.001), though the EA group demonstrated better improvement in flexion, extension, and left/right lateral flexion (p<0.05). No adverse effects of FC were reported.
The authors concluded that FC appears to be an effective and safe therapy for neck pain due to cervical spondylosis, showing similar pain relief efficacy with no statistically significant difference compared to electroacupuncture despite a lower treatment dosage. However, due to methodological limitations, these findings should be interpreted with caution and warrant further validation in rigorously designed studies.
I do agree with the authors’ call for caution – but with little else of what they state. Here are some of my concerns:
- A trial comparing two supposedly active treatments is an ‘equivalence study’; and such investigations require much larger sample sizes that 80.
- Equivalence studies only make sense, if one of the two treatments has been shown beyond doubt to be effective; this is not the case for electroacupuncture nor for FC.
- As it stands, the study does not control for placebo effects; thus the findings are in accordance with both treatments being pure placebos.
- A study with 80 patients tells us as good as nothing about the safety of the iterventions; to draw conclusions about safety is thus unwarranted
My conclusion (yet again) is this:
If you design a nonsense study, you are asking for a nonsense result.
Reliable reporting and publication practices are essential for trustworthy evidence synthesis and clinical decision-making. This analysis aimed to identify latent classes of randomized controlled trials (RCTs) evaluating spinal manipulative therapy (SMT) based on trial reporting and publication practices, and to examine whether these classes influenced treatment effects.
Trials were evaluated on whether they met criteria for trial reporting and publication practices across six domains. Latent class analysis was used to identify trial subgroups. Random-effects meta-regression models assessed whether class membership predicted pooled estimates of treatment effects for pain and disability.
The international team included 239 RCTs and identified four classes: Dated (23 %), older trials (mostly pre-2010) with consistently low proportions of criteria met; Non-contributing (30 %), newer trials that inconsistently met the criteria, had small samples, and short follow-ups; SMT-focused (15 %), which reported SMT details and fidelity more consistently but otherwise resembled the Non-contributing class; and Pragmatic (33 %), consisting of larger trials, meeting most criteria, but often underreported SMT-specific and fidelity details. Reporting practices had larger impact on class membership than publication practices. Despite differences class membership was not associated with treatment effect estimates and explained minimal outcome variability (R2 ∼1 %).
The authors concluded that, although trial reporting and publication practices varied substantially across SMT trials, these differences were not associated with differences in treatment effects. The widespread failure to meet key criteria raises concerns about the interpretability and credibility of the SMT evidence base. To strengthen transparency and scientific value, future trials should adhere more rigorously to reporting guidelines.
What does this mean?
The authors state that editors and peer reviewers should more rigorously enforce established reporting standards, including CONSORT (with its Harms extension), TIDieR, and the CIRCLe SMT checklist.
Undoubtedly, this is true.
But what does it mean for patients?
In my view, it is a reminder for all of us to be skeptical about the claims made by chiropractors, osteopaths and other providers of SMT – even if they claim to be based on evidence.
Homeopathy is among the most popular kinds of so-called alternative medicine (SCAM). Patients have different opinions about homeopathy because there is still debate about its efficacy and scientific foundation, despite its popularity. The purpose of this cross-sectional study was to compare homeopathic therapies to conventional medicine in terms of patient satisfaction for a range of health issues.
Secifically, the Indian researchers aimed to compare levels of patient satisfaction with homeopathic vs conventional treatments in terms of:
- treatment results,
- side effects,
- cost,
- and overall experience.
A varied group of patients undergoing therapy for long-term diseases like anxiety, asthma, and arthritis provided the data. Patients’ levels of satisfaction with their therapy, its duration, their perceptions of safety, and the quality of their interactions with their providers were measured using a standardized survey that contained Likert-scale items.
Patients who had homeopathic treatment were more likely to be satisfied with their tailored care and the low frequency of adverse effects, according to the results. On the other hand, patients receiving conventional treatments were more satisfied with the rapid alleviation of their symptoms and the fact that their treatments were based on solid evidence. But many patients in both categories were worried about how much their treatments would cost and whether or not they would be beneficial in the long run. Perceivable treatment efficacy, safety, and the total healthcare experience are three of the many aspects that impact patients’ levels of satisfaction.
The authors concluded that the significance of patient-centered care and the necessity for additional research to comprehend the elements contributing to contentment in various treatment modalities highlight the value of both conventional and homeopathic treatments.
This amazingly incompetent paper was published in the ‘Indian Journal of Ayurvedic & Alternative Medicine’ by Dr. Anil Kumar Sharma. He is the dean of the Faculty of Homoeopathy, Govt. Ayush University, Kurukshetra Professor, JRK Homoeopathic Medical College, Rohtak Teacher Code Registered with National Homoeopathic Commission, Govt. of India.
Amazingly incompetent?
I better justify this verdict!
But where to begin? I cannot possibly discuss all the fatal flaws of this paper. Let me just mention a few obvious ones:
- A “standardized survey” was used to measure the outcomes. But was it validated to ensure that it quantified what the researcher thought to measure? No!
- Were the two patient groups comparable? No!
- Were they objective? No, the homeopathy group has chosen to consult homeopaths. Thus the results are as meaningful as asking people who choose to buy a hamburger whether they like eating beef.
- The conclusions are pure fantasy and do not follow from the data.
You may feel that all this is irrelevant nonsense – and you would be entirely correct. Yet, I think that this paper might still be important for one reason: it was published by the dean of the Faculty of Homoeopathy, Govt. Ayush University, Kurukshetra Professor. Imagine the dean of the faculty of cosmology of a reputable university wrote a paper claiming without any eveidence that the earth was flat. That, in my view, would be the equivalent of the above article.
