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

causation

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Spinal epidural haematoma (SEH) is an uncommon but serious emergency condition. A team of emergency physicians reported the case of a SEH associated with traditional massage initially presenting with delayed lower paraplegia.

A 20-year-old man was seen with bilateral lower extremity weakness and numbness, symptoms that had started three hours prior to presentation. He had received a Thai massage by a friend three days before. Magnetic resonance imaging revealed a spinal epidural lesion suspicious for haematoma extending from C6 to T2 levels. Emergent surgical intervention for cord decompression was performed. An epidural haematoma with cord compression at C6-T2 levels was identified intra-operatively. No evidence of abnormal vascular flow or AV malformations was identified. The authors concluded that, similar to chiropractic manipulation, massage may be associated with spinal trauma. Emergency physicians must maintain a high index of suspicion for spinal epidural haematomas in patients with a history of massage or chiropractic manipulation with neurologic complaints, because delays in diagnosis may worsen clinical outcome.

Thai massage therapists typically use no lubricants. The patient remains clothed during a treatment. There is constant body contact between the therapist – who, in the above case, was a lay person – and the patient.

The authors of this case report rightly stress that such adverse events are rare – but they are by no means unknown. In 2003, I reviewed the risks and found 16 reports of adverse effects as well as 4 case series on the subject (like for all other manual therapies, there is no reporting system of adverse effects). The majority of adverse effects were – like the above case – associated with exotic types of manual massage or massage delivered by laymen. Professionally trained massage therapists were rarely implicated. The reported adverse events include cerebrovascular accidents, displacement of a ureteral stent, embolization of a kidney, haematoma, leg ulcers, nerve damage, posterior interosseous syndrome, pseudoaneurism, pulmonary embolism, ruptured uterus, strangulation of neck, thyrotoxicosis and various pain syndromes. In the majority of these instances, there was little doubt about a cause-effect relationship. Serious adverse effects were associated mostly with massage techniques other than ‘Swedish’ massage.

For patients, this means that massage is still amongst the safest form of manual therapy (best to employ qualified therapists and avoid the exotic versions of massage because they are not supported by evidence and carry the highest risks). For doctors, it means to be vigilant, if patients present with neurological problems after having enjoyed a massage.

Chiropractors believe that their spinal manipulations bring about a reduction in pain perception, and they often call this ‘manipulation-induced hypoalgesia’ (MIH). It is unknown, however, whether MIH following high-velocity low-amplitude spinal manipulative therapy is a specific and clinically relevant treatment effect.

This systematic review was an effort in finding out.

The authors investigated changes in quantitative sensory testing measures following high-velocity low-amplitude spinal manipulative therapy in musculoskeletal pain populations, in randomised controlled trials. Their objectives were to compare changes in quantitative sensory testing outcomes after spinal manipulative therapy vs. sham, control and active interventions, to estimate the magnitude of change over time, and to determine whether changes are systemic or not.

Fifteen studies were included. Thirteen measured pressure pain threshold, and 4 of these were sham-controlled. Change in pressure pain threshold after spinal manipulative therapy compared to sham revealed no significant difference. Pressure pain threshold increased significantly over time after spinal manipulative therapy (0.32 kg/cm2, CI 0.22–0.42), which occurred systemically. There were too few studies comparing to other interventions or for other types of quantitative sensory testing to make robust conclusions about these.

The authors concluded that they found that systemic MIH (for pressure pain threshold) does occur in musculoskeletal pain populations, though there was low quality evidence of no significant difference compared to sham manipulation. Future research should focus on the clinical relevance of MIH, and different types of quantitative sensory tests.

An odd conclusion, if there ever was one!

A more straight forward conclusion might be this:

MIH is yet another myth to add to the long list of bogus claims made by chiropractors.

The objective of this ‘real world’ study was to evaluate the effectiveness of integrative medicine (IM) on patients with coronary artery disease (CAD) and investigate the prognostic factors of CAD in a real-world setting.

A total of 1,087 hospitalized patients with CAD from 4 hospitals in Beijing, China were consecutively selected between August 2011 and February 2012. The patients were assigned to two groups:

  1. Chinese medicine (CM) plus conventional treatment, i.e., IM therapy (IM group). IM therapy meant that the patients accepted the conventional treatment of Western medicine and the treatment of Chinese herbal medicine including herbal-based injection and Chinese patent medicine as well as decoction for at least 7 days in the hospital or 3 months out of the hospital.
  2. Conventional treatment alone (CT group).

The endpoint was a major cardiac event [MCE; including cardiac death, myocardial infarction (MI), and the need for revascularization].

A total of 1,040 patients finished the 2-year follow-up. Of them, 49.4% received IM therapy. During the 2-year follow-up, the total incidence of MCE was 11.3%. Most of the events involved revascularization (9.3%). Cardiac death/MI occurred in 3.0% of cases. For revascularization, logistic stepwise regression analysis revealed that age ⩾ 65 years [odds ratio (OR), 2.224], MI (OR, 2.561), diabetes mellitus (OR, 1.650), multi-vessel lesions (OR, 2.554), baseline high sensitivity C-reactive protein level ⩾ 3 mg/L (OR, 1.678), and moderate or severe anxiety/depression (OR, 1.849) were negative predictors (P<0.05); while anti-platelet agents (OR, 0.422), β-blockers (OR, 0.626), statins (OR, 0.318), and IM therapy (OR, 0.583) were protective predictors (P<0.05). For cardiac death/MI, age ⩾ 65 years (OR, 6.389) and heart failure (OR, 7.969) were negative predictors (P<0.05), while statin use (OR, 0.323) was a protective predictor (P<0.05) and IM therapy showed a beneficial tendency (OR, 0.587), although the difference was not statistically significant (P=0.218).

The authors concluded that in a real-world setting, for patients with CAD, IM therapy was associated with a decreased incidence of revascularization and showed a potential benefit in reducing the incidence of cardiac death or MI.

What the authors call ‘real world setting’ seems to be a synonym of ‘lousy science’, I fear. I am not aware of good evidence to show that herbal injections and concoctions are effective treatments for CAD, and this study can unfortunately not change this. In the methods section of the paper, we read that the treatment decisions were made by the responsible physicians without restriction. That means the two groups were far from comparable. In their discussion section, the authors state; we found that IM therapy was efficacious in clinical practice. I think that this statement is incorrect. All they have shown is that two groups of patients with similar diagnoses can differ in numerous ways, including clinical outcomes.

The lessons here are simple:

  1. In clinical trials, lack of randomisation (the only method to create reliably comparable groups) often leads to false results.
  2. Flawed research is currently being used by many proponents of  SCAM (so-called alternative medicine) to mislead us about the value of SCAM.
  3. The integration of dubious treatments into routine care does not lead to better outcomes.
  4. Integrative medicine, as currently advocated by SCAM-proponents, is a nonsense.

Patients with rheumatoid arthritis (RA) have a higher risk of coronary heart disease (CHD). Despite good evidence for effectiveness, acupuncture is often advocated for RA, and it has not been reported to prevent CHD in patients with RA.

The authors of this analysis aimed to assess the risk of developing CHD in acupuncture-users and non-users of patients with RA. They identified 29,741 patients with newly diagnosed RA from January 1997 to December 2010 from the Registry of Catastrophic Illness Patients Database from the Taiwanese National Health Insurance Research Database. Among them, 10,199 patients received acupuncture (acupuncture users), and 19,542 patients did not receive acupuncture (no-acupuncture users). After performing 1:1 propensity score matching by sex, age, baseline comorbidity, conventional treatment, initial diagnostic year, and index year, there were 9932 patients in both the acupuncture and no-acupuncture cohorts. The main outcome was the diagnosis of CHD in patients with RA in the acupuncture and no-acupuncture cohorts.

Acupuncture users had a lower incidence of CHD than non-users (adjusted HR = 0.60, 95% CI = 0.55-0.65). The estimated cumulative incidence of CHD was significantly lower in the acupuncture cohort (log-rank test, p < .001). Subgroup analysis showed that patients receiving manual acupuncture of traditional Chinese medicine style, electroacupuncture, or combination of both all had a lower incidence of CHD than patients never receiving acupuncture treatment. The beneficial effect of acupuncture on preventing CHD was independent of age, sex, diabetes mellitus, hypertension, hyperlipidemia, and statins use.

The authors concluded that this is the first large-scale study to reveal that acupuncture might have beneficial effect on reducing the risk of CHD in patients with RA. This study may provide useful information for clinical utilization and future studies.

Pigs might fly, but – call me a sceptic – I somehow doubt it almost as much as I doubt that acupuncture might have beneficial effect on reducing the risk of CHD.

Why?

Because of two reasons mainly:

  1. For the life of me, I cannot see a mechanism by which acupuncture achieves this extraordinary feast (the authors allege an anti-inflammatory effect of acupuncture which I find wholly unconvincing).
  2. There is a much simpler explanation for the observed outcomes.

The propensity score used here did, of course, only match the groups for a hand-full of factors. Yet there are many more that could play a part which the authors could not consider because they did not have the data to do so. The one that foremost comes to my mind is a generally healthier life-style of the patients using acupuncture. I think it stands to reason that people who bother to have and pay for an additional treatment are higher motivated to adhere to a life-style (e. g. smoking-cessation, exercise, nutrition, stress) that reduces the CHD-risk. And the influence of this factor could be very significant indeed. As the devil’s advocate, I could therefore even postulate that acupuncture itself had a slightly detrimental effect which, however, was over-ridden by the massive effect of the healthier life-style.

And the lesson to learn from all this?

Before we conclude about ‘beneficial effects’ of acupuncture or any other therapy, we need RCTs that effectively eliminate these rather obvious confounders.

 

Belgian homeopaths, together with the ‘European Committee for Homeopathy’, have published a statement which I find too remarkable to withhold it from you:

START OF QUOTE

Users of homeopathic medicines can no longer remain silent about the untruths circulating in the media. These lies raise doubts which naïve and gullible people take on board all too easily and then see homeopathy as quackery. None of this is accurate!

Because they fear seeing some of their ‘certainties’ questioned, the SKEPP movement is firing off at anything that current science cannot yet explain with both barrels.

The contents of homeopathic medicines
SKEPP states that a homeopathic medicine is nothing more than a drop of water in a swimming pool and therefore has nothing in it. This is  wrong. Tests performed on a high homeopathic potency (30CH) of Gelsemium sempervirens (Yellow Jasmine, a very common homeopathic medicine) have detected 36 micrograms of a specific substance per gram of solution [1]. Opponents denounce homeopathic medicines as being nothing but water. This is  wrong. This water, the solvent itself, contains a specific signature of the active ingredient. Basic research has demonstrated this [2].

Clinical efficacy.
By asserting at every opportunity that there is no evidence of the clinical effectiveness of homeopathy, opponents sow doubt. Correction:  such proof [3] does exist.  The fact that critics refuse to look at or accept these data speaks volumes about their attitude to science.
What is true, however, is that there is  not enough  scientific evidence of effectiveness. Science demands a lot of such evidence – and rightly so. There would be more if the universities applied the rules correctly!  For example: The Professional Union of Homeopathic Physicians had accepted a double-blind research protocol for fibromyalgia which took account of homeopathy’s individualized approach. This research was to be carried out at the Rheumatology Department of a hospital in Brussels with the agreement of the Rector of the Faculty of Medicine. But the hospital’s ethics committee decided that it would be unethical to test a ‘placebo’ (the homeopathic medicine) versus another placebo! Making an a priori assumption that homeopathic medicine is just a placebo, even before beginning the study, flies in the face of scientific objectivity.

Patients are not stupid!
In the meantime, Pro Homeopathia, the Belgian association of homeopathy patients, is no longer able to contain its members’ exasperation. It has published an article [4]  which denounces in direct terms the accusations of credulity, or even stupidity levelled at patients, in blatant disregard of their therapeutic freedom of choice and their capacity for critical thought.

Dare to ask questions! 
Why all this misinformation in the press? Why do these ‘experts’, whose opinions on homeopathy above all betray their profound misunderstanding of this discipline, flood the media with fake news? What is the hidden agenda behind this campaign of systematic denigration? Homeopathy and many other complementary medicines only want to collaborate, both in medical practice and in scientific research … fair play! It’s called integrative medicine!

References
[1]Nanoparticle Characterization of Traditional Homeopathically-Manufactured Cuprum metallicum and Gelsemium Sempervirens Medicines and Controls. Novembre 2018: https://www.thieme-connect.de/DOI/DOI?10.1055/s-0038-1666864)
[2]Nuclear Magnetic Resonance characterization of traditional homeopathically-manufactured copper (Cuprum metallicum) and a plant (Gelsemium sempervirens) medicines and controls. Août 2017: https://doi.org/10.1016/j.homp.2017.08.001
[3]Model validity and risk of bias in randomized placebo-controlled trials of individualised homeopathic treatment. 2016: http://dx.doi.org/10.1016/j.ctim.2016.01.005 //Clinical verification in homeopathy and allergic conditions. 2012 http://dx.doi.org/10.1016/j.homp.2012.06.002 //Scientific framework of homeopathy 2017. www.lmhi.org/Article/Detail/42)
[4]http://www.homeopathie-unio.be/uploads/files/unprotected/Presse/Attaques%20Hom%C3%A9o-FR2.pdf

END OF QUOTE

For regular readers of this blog, any comment on this little article might well be superfluous. For newcomers, I nevertheless provide a few thoughts. In doing so, I simply follow the three headings used above.

The contents of homeopathic medicines

A homeopathic C30 potency (the one that is used most frequently) is a dilution of 1 part homeopathic stock to 1000000000000000000000000000000000000000000000000000000000000 parts of diluent. This amounts to little more than one molecule of stock per universe. This is an undeniable fact, and the reference provided (incidentally, the link to it is dead) does not change it in any way. The theory of ‘the memory of water’ is an implausible hypothesis that has no basis in reality. It is believed only by homeopaths, and ‘studies’ that seemingly support it are flimsy, false or biased, and usually only get published in journals such as ‘Homeopathy’ (where also the reference provided appeared).

Clinical efficacy

This is a subject that we have already discussed ad nauseam. Highly diluted homeopathic remedies are pure placebos. If someone does not believe this nor all the evidence provided on this blog, they perhaps trust the many independent international bodies that have looked at the totality of the reliable evidence for or against homeopathy. Their verdicts are unanimously negative. (The above-cited decision of the ethics committee is therefore the only one that is ethically possible.)

Patients are not stupid!

That is absolutely correct; patients are certainly not stupid. And their experiences are certainly real. What is often wrong, however, is the interpretation of their experiences. When a patient’s symptoms improve after taking a highly diluted remedy, the perceived improvement is due to a long list of factors that are unrelated to the remedy: placebo, natural history, regression towards the mean, etc.

Patients are not stupid, but the misinformation homeopaths incessantly publish might render them stupid – one more reason why such irresponsible nonsense ought to stop.

 

In 1995, Dabbs and Lauretti reviewed the risks of cervical manipulation and compared them to those of non-steroidal, anti-inflammatory drugs (NSAIDs). They concluded that the best evidence indicates that cervical manipulation for neck pain is much safer than the use of NSAIDs, by as much as a factor of several hundred times. This article must be amongst the most-quoted paper by chiropractors, and its conclusion has become somewhat of a chiropractic mantra which is being repeated ad nauseam. For instance, the American Chiropractic Association states that the risks associated with some of the most common treatments for musculoskeletal pain—over-the-counter or prescription nonsteroidal anti-inflammatory drugs (NSAIDS) and prescription painkillers—are significantly greater than those of chiropractic manipulation.

As far as I can see, no further comparative safety-analyses between cervical manipulation and NSAIDs have become available since this 1995 article. It would therefore be time, I think, to conduct new comparative safety and risk/benefit analyses aimed at updating our knowledge in this important area.

Meanwhile, I will attempt a quick assessment of the much-quoted paper by Dabbs and Lauretti with a view of checking how reliable its conclusions truly are.

The most obvious criticism of this article has already been mentioned: it is now 23 years old, and today we know much more about the risks and benefits of these two therapeutic approaches. This point alone should make responsible healthcare professionals think twice before promoting its conclusions.

Equally important is the fact that we still have no surveillance system to monitor the adverse events of spinal manipulation. Consequently, our data on this issue are woefully incomplete, and we have to rely mostly on case reports. Yet, most adverse events remain unpublished and under-reporting is therefore huge. We have shown that, in our UK survey, it amounted to exactly 100%.

To make matters worse, case reports were excluded from the analysis of Dabbs and Lauretti. In fact, they included only articles providing numerical estimates of risk (even reports that reported no adverse effects at all), the opinion of exerts, and a 1993 statistic from a malpractice insurer. None of these sources would lead to reliable incidence figures; they are thus no adequate basis for a comparative analysis.

In contrast, NSAIDs have long been subject to proper post-marketing surveillance systems generating realistic incidence figures of adverse effects which Dabbs and Lauretti were able to use. It is, however, important to note that the figures they did employ were not from patients using NSAIDs for neck pain. Instead they were from patients using NSAIDs for arthritis. Equally important is the fact that they refer to long-term use of NSAIDs, while cervical manipulation is rarely applied long-term. Therefore, the comparison of risks of these two approaches seems not valid.

Moreover, when comparing the risks between cervical manipulation and NSAIDs, Dabbs and Lauretti seemed to have used incidence per manipulation, while for NSAIDs the incidence figures were bases on events per patient using these drugs (the paper is not well-constructed and does not have a methods section; thus, it is often unclear what exactly the authors did investigate and how). Similarly, it remains unclear whether the NSAID-risk refers only to patients who had used the prescribed dose, or whether over-dosing (a phenomenon that surely is not uncommon with patients suffering from chronic arthritis pain) was included in the incidence figures.

It is worth mentioning that the article by Dabbs and Lauretti refers to neck pain only. Many chiropractors have in the past broadened its conclusions to mean that spinal manipulations or chiropractic care are safer than drugs. This is clearly not permissible without sound data to support such claims. As far as I can see, such data do not exist (if anyone knows of such evidence, I would be most thankful to let me see it).

To obtain a fair picture of the risks in a real life situation, one should perhaps also mention that chiropractors often fail to warn patients of the possibility of adverse effects. With NSAIDs, by contrast, patients have, at the very minimum, the drug information leaflets that do warn them of potential harm in full detail.

Finally, one could argue that the effectiveness and costs of the two therapies need careful consideration. The costs for most NSAIDs per day are certainly much lower than those for repeated sessions of manipulations. As to the effectiveness of the treatments, it is clear that NSAIDs do effectively alleviate pain, while the evidence seems far from being conclusively positive in the case of cervical manipulation.

In conclusion, the much-cited paper by Dabbs and Lauretti is out-dated, poor quality, and heavily biased. It provides no sound basis for an evidence-based judgement on the relative risks of cervical manipulation and NSAIDs. The notion that cervical manipulations are safer than NSAIDs is therefore not based on reliable data. Thus, it is misleading and irresponsible to repeat this claim.

 

One would be hard-pressed to find a form of so-called alternative medicine (SCAM) that is not being promoted for back pain: chiropractic, osteopathy, reflexology, naturopathy, homeopathy … you name it. Intriguingly, they all seem to generate similarly good – a realist would say bad – results. Faced with this large but largely ineffective options, one can hardly be surprised that enterprising innovators look for their own solutions. And few are more enterprising then this patient from Ireland who decided to devise his very own and highly unusual back pain therapy.

The 33 year old male with a history of back problems was seen complaining of severe, sudden onset lower back pain. He reported lifting a heavy steel object 3 days prior and his symptoms had progressed ever since. A physical exam of revealed an erythematous papule with a central focus on the medial aspect of his right upper limb.

The patient disclosed that he had – independent of any medical advice – intravenously injected his own semen as an innovative method to alleviate his back pain (a truly naturopathic approach, if there ever was one!). He also revealed that he had previously injected one monthly “dose” of semen for 18 consecutive months using a hypodermic needle purchased online.

On this occasion, the patient had tried to inject three “doses” of semen intra-vascularly and intra-muscularly. The erythema extended medially along his upper limb over the course of the following 24 hours.

It became indurated around the injection site where he had failed multiple attempts at injecting the semen thus causing an extravasation of his sperm into the soft tissues. Blood tests demonstrated a C-reactive protein of 150mg/L and white cell count of 13×109/L. The patient was immediately commenced on intravenous antimicrobial treatment after seeking advice regarding appropriate cover. A radiograph of the limb was obtained to exclude retained foreign body and it demonstrated a subcutaneous emphysema.

This patient’s back pain improved over the course of his inpatient stay. He opted to discharge himself without availing of an incision and drainage of the local collection.

Remarkable!

For me, the most fascinating aspect of this story is the fact that the patient had previously treated himself 18 (!) times before this little mishap occurred.

Why?, one may well ask. The answer has, I think, been provided by legions of proponents of diverse forms of SCAM: BECAUSE IT WORKED! PEOPLE ARE NOT STUPID; THEY DON’T CONTINUE TREATMENTS, IF THEY DON’T WORK.

So, either intravenous semen injections are an effective way to control back pain – in which case, I recommend that NICE look into it – or…

THERE IS SOMETHING BADLY WRONG WITH THE FAVOURITE ARGUMENT OF SCAM-ENTHUSIASTS, IT WORKED FOR ME AND THEREFORE IT IS EFFECTIVE AND SAFE.

(I know which explanation I favour)

The notion that ‘chiropractic adds years to your life’ is often touted, particularly of course by chiropractors (in case you doubt it, please do a quick google search). It is logical to assume that chiropractors themselves are the best informed about what they perceive as the health benefits of chiropractic care. Chiropractors would therefore be most likely to receive some level of this ‘life-prolonging’ chiropractic care on a long-term basis. If that is so, then chiropractors themselves should demonstrate longer life spans than the general population.

Sounds logical?

Perhaps, but is the theory supported by evidence?

Back in 2004, a chiropractor, Lon Morgan,  courageously tried to test the theory and published an interesting paper about it.

He used two separate data sources to examine the mortality rates of chiropractors. One source used obituary notices from past issues of Dynamic Chiropractic from 1990 to mid-2003. The second source used biographies from Who Was Who in Chiropractic – A Necrology covering a ten year period from 1969-1979. The two sources yielded a mean age at death for chiropractors of 73.4 and 74.2 years respectively. The mean ages at death of chiropractors is below the national average of 76.9 years; it also is below the average age at death of their medical doctor counterparts which, at the time, was 81.5.

So, one might be tempted to conclude that ‘chiropractic substracts years from your life’. I know, this would be not very scientific – but it would probably be more evidence-based than the marketing gimmick of so many chiropractors trying to promote their trade by saying: ‘chiropractic adds years to your life’!

In any case, Morgan, the author of the paper, concluded that this paper assumes chiropractors should, more than any other group, be able to demonstrate the health and longevity benefits of chiropractic care. The chiropractic mortality data presented in this study, while limited, do not support the notion that chiropractic care “Adds Years to Life …”, and it fact shows male chiropractors have shorter life spans than their medical doctor counterparts and even the general male population. Further study is recommended to discover what factors might contribute to lowered chiropractic longevity.

Another beautiful theory killed by an ugly fact!

I would warn every parent who thinks that taking their child to a chiropractor is a good idea. For this, I have three main reasons:

  1. Chiropractic has not been shown to be effective for any paediatric condition.
  2. Chiropractors often advise parents against vaccinating their children.
  3. Chiropractic spinal manipulations can cause harm to kids.

The latter point seems to be confirmed by a recent PhD thesis of which so far only one short report is available. Here are the relevant bits of information from it:

Katie Pohlman has successfully defended her PhD thesis, which focused on the assessment of safety in pediatric manual therapy. As a clinical research scientist at Parker University, Dallas, Texas, she identified a lack of prospective patient safety research within the chiropractic population in general and investigated this deficit in the paediatric population in particular.

Pohlman used a cross-sectional survey to assess the barriers and facilitators for participation in a patient safety reporting system. At the same time, she also conducted a randomized controlled trial comparing the quantity and quality of adverse event reports in children under 14 years receiving chiropractic care.

The RCT recruited 69 chiropractors and found adverse events reported in 8.8% and 0.1% of active and passive surveillance groups respectively. Of the adverse events reported, 56% were considered mild, 26% were moderate and 18% were severe. The frequency of adverse events was more common than previously thought.

This last sentence from the report is somewhat puzzling. Our systematic review of the risks of spinal manipulation showed that data from prospective studies suggest that minor, transient adverse events occur in approximately half of all patients receiving spinal manipulation. The most common serious adverse events are vertebrobasilar accidents, disk herniation, and cauda equina syndrome. Estimates of the incidence of serious complications range from 1 per 2 million manipulations to 1 per 400,000. Given the popularity of spinal manipulation, its safety requires rigorous investigation.

The 8.8% reported by Pohlman are therefore not even one fifth of the average incidence figure reported previously in all age groups.

What could be the explanation for this discrepancy?

There are, of course, several possibilities, including the fact that infants cannot tell the clinician when their pain has increased. However, the most likely one, in my view, lies in the fact that RCTs are wholly inadequate for investigating risks because they typically include far too few patients to generate reliable incidence figures about adverse events. More importantly, clinicians included in such studies are self-selected (and thus particularly responsible/cautious) and are bound to behave most carefully while being part of a clinical trial. Therefore it seems possible – I would speculate even likely – that the 8.8% reported by Pohlman is unrealistically low.

Having said that, I do feel that the research by Kathie Pohlman is a step in the right direction and I do applaud her initiative.

Lumbar spinal stenosis (LSS) is a common reason for spine surgery. Several non-surgical LSS treatment options are also available, but their effectiveness remains unproven. The objective of this study was to explore the comparative clinical effectiveness of three non-surgical interventions for patients with LSS:

  • medical care,
  • group exercise,
  • individualised exercise plus manual therapy.

All interventions were delivered during 6 weeks with follow-up at 2 months and 6 months at an outpatient research clinic. Patients older than 60 years with LSS were recruited from the general public. Eligibility required anatomical evidence of central canal and/or lateral recess stenosis (magnetic resonance imaging/computed tomography) and clinical symptoms associated with LSS (neurogenic claudication; less symptoms with flexion). Analysis was intention to treat.

Medical care consisted of medications and/or epidural injections provided by a physiatrist. Group exercise classes were supervised by fitness instructors. Manual therapy/individualized exercise consisted of spinal mobilization, stretches, and strength training provided by chiropractors and physical therapists. The primary outcomes were between-group differences at 2 months in self-reported symptoms and physical function measured by the Swiss Spinal Stenosis questionnaire (score range, 12-55) and a measure of walking capacity using the self-paced walking test (meters walked for 0 to 30 minutes).

A total of 259 participants were allocated to medical care (n = 88), group exercise (n = 84), or manual therapy/individualized exercise (n = 87). Adjusted between-group analyses at 2 months showed manual therapy/individualized exercise had greater improvement of symptoms and physical function compared with medical care or group exercise. Manual therapy/individualized exercise had a greater proportion of responders (≥30% improvement) in symptoms and physical function (20%) and walking capacity (65.3%) at 2 months compared with medical care (7.6% and 48.7%, respectively) or group exercise (3.0% and 46.2%, respectively). At 6 months, there were no between-group differences in mean outcome scores or responder rates.

The authors concluded that a combination of manual therapy/individualized exercise provides greater short-term improvement in symptoms and physical function and walking capacity than medical care or group exercises, although all 3 interventions were associated with improvements in long-term walking capacity.

In many ways, this is a fairly rigorous study; in one important way, however, it is odd. One can easily see why one group received the usual standard care (except perhaps for the fact that standard medical care should also include exercise). I also understand why one group attended group exercise. Yet, I fail to see the logic in the third intervention, individualised exercise plus manual therapy.

Individualised exercise is likely to be superior to group exercise. If the researchers wanted to test this hypothesis, they should not have added the manual therapy. If they wanted to find out whether manual therapy is better that the other two treatments, they should not have added individualised exercise. As it stands, they cannot claim that either manual therapy or individualised exercise are effective (yet, I am sure that the chiropractic fraternity will claim that this study shows their treatment to be indicated for LSS [three of the authors are chiropractors and the 1st author seems to have a commercial interest in the matter!]).

Manual therapy procedures used in this trial included:

  • lumbar distraction mobilization,
  • hip joint mobilization,
  • side posture lumbar/sacroiliac joint mobilization,
  • and neural mobilization.

Is there any good reason to assume that these interventions work for LSS? I doubt it!

And this is what makes the new study odd, in my view. Assuming I am correct in speculating that individualised exercise is better than group exercise, the trial would have yielded a similarly positive result, if the researchers had offered, instead of the manual therapy, a packet of cigarettes, a cup of tea, a chocolate bar, or swinging a dead cat. In other words, if someone had wanted to make a useless therapy appear to be effective, they could not have chosen a better trial design.

And why do I find such studies objectionable?

Mainly because they deliberately mislead many of us. In the present case, many non-critical observers might conclude that manual therapy is effective for LSS. Yet, the truth could well be that it is useless or even harmful (assuming that the effect size of individualised exercise is large, adding a harmful therapy would still render the combination effective). To put it bluntly, such trials

  • could harm patients,
  • might waste money,
  • and hinder progress.

 

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