I read with interest the paper written by Mirtz et al. I have reservations regarding the authors’ conclusions pertaining to the manner in which they have editorialized the subject matter and applied Hill’s Criteria of Causation.
First, I would direct the authors to the paper written by Phillips and Goodman [1] entitled, “The missed lessons of Sir Austin Bradford Hill." Phillips and Goodman report the following:
Making a good decision does not depend on having studies with confidence intervals that exclude the null. A best decision can be based on whatever information we have now, and indeed a decision will be made – after all, the decision to maintain the status quo is still a decision. Hill offered his clearest condemnation of over-emphasizing statistical significance testing, not when he discussed p-values, but when he concluded by saying: "All scientific work is incomplete – whether it be observational or experimental. All scientific work is liable to be upset or modified by advancing knowledge. That does not confer upon us a freedom to ignore the knowledge we already have, or to postpone the action that it appears to demand at a given time."
This would release us from the trap of letting ignorance trump knowledge. Regulators often fail to act because we have not yet statistically "proven" an association between an exposure and a disease, even when there is enough evidence to strongly suspect a causal relationship. There is a growing movement to escape this mistake by making a similar mistake in the other direction: adopting precautionary principles, which typically call for restrictions until we have "proven" lack of causal association – a decision based on ignorance that merely reverses the default. If we can escape from the false dichotomy of "proven vs. not proven," facilitated by the non-existant bright line implied by statistical hypothesis testing and by the notion that causality can be definitively inferred from a list of criteria, then we can make decisions based on what we do know rather than what we don't.
The uncritical repetition of Hill's "causal criteria" is probably counterproductive in promoting sophisticated understanding of causal inference. But a different list of considerations that can be found in his address is worthy of repeating:
• Statistical significance should not be mistaken for evidence of a substantial association. • Association does not prove causation (other evidence must be considered). • Precision should not be mistaken for validity (non-random errors exist). • Evidence (or belief) that there is a causal relationship is not sufficient to suggest action should be taken. • Uncertainty about whether there is a causal relationship (or even an association) is not sufficient to suggest action should not be taken.
These points may seem obvious when stated so bluntly, but causal inference and health policy decision making would benefit tremendously if they were considered more carefully and more often. The last point may be the most important unlearned lesson in health decision making.
In fairness to those who do not appreciate these points even today, it over-interprets Hill's short paper to claim that he clearly laid out these considerations, or that he was calling for modern decision analysis and uncertainty quantification. But the fundamental concepts were clearly there (and the over-interpretation is not as great as that required to derive a checklist of criteria for determining causation). Several generations of advancement in epidemiology and policy analysis provide much deeper exposition of his points. But Hill still offers timeless insightful analysis about how to interpret our observations. Strangely, these forgotten lessons, which are only slowly and grudgingly being appreciated in modern epidemiology, are hidden in plain sight, in what is possibly the best known paper in the field.
It is my impression that Mirtz et al. have exercised an uncritical repetition of Hill's, "causal criteria," that is counterproductive in promoting a sophisticated understanding of causal inference related to the term, “subluxation.”
I would also caution the authors to carefully apply the tenets of evidence based medicine. Sackett et al. [2] conveyed the following thoughts:
• Evidence based medicine is the conscientious, explicit, and judicious use of current best evidence in making decisions about the care of individual patients. • The practice of evidence based medicine means integrating individual clinical expertise with the best available external clinical evidence from systematic research. • Good doctors use both individual clinical expertise and the best available external evidence, and neither alone is enough. • Evidence based medicine is not restricted to randomised trials and meta-analyses. It involves tracking down the best external evidence with which to answer our clinical questions.
Finally, the opinion of Resnick [3] bears consideration: “Evidence-based medicine is a useful tool for summarizing and grading the evidence available in the literature for or against a particular treatment strategy. Its utility is limited by the quality of the primary literature, and the absence of proof cannot be equated with the proof of absence.”
When considering the term, “subluxation,” utilized by the chiropractic profession, it is my impression that stringent adherence to epidemiologic constructs and evidence based medical protocols must not over-shadow clinical experience. Authors must integrate clinical experience and the best available external evidence.
References
1. Phillips CV, Goodman KJ: The missed lessons of Sir Austin Bradford Hill.Epidemiologic Perspectives & Innovations 2004, 1:3.
2. Sackett DL, Rosenberg WMC, Gray JAM, Haynes RB, Richardson WS: Evidence based medicine: what it is and what it isn't: It's about integrating individual clinical expertise and the best external evidence.British Medical Journal 1996, 312(7023): 71-72.
3. Resnick DK: Evidence based spine surgery.Spine 2007, 32(11): S15-S19.
James Demetrious, DC, FACO Wilmington, NC
Competing interests
No competing interest exists with regard to my professional judgment about the referenced paper that could possibly be influenced by considerations other than the paper's validity or importance.
Literature support for subluxation theory
John Hart, self
5 January 2010
Editor:
The article by Mirtz et al regarding the application of Hill’s criteria to test whether or not subluxation is causal (1) is interesting but has a few problems, as follows.
1. Hill seems to apply his criteria to association first, rather than causation. (2) Indeed Hill himself warns that criteria alone do not establish cause-and-effect relationships. (2-3)
2. The authors seem to have overlooked literature that could qualify for at least some of Hill’s criteria for association. For example:
a) Given the large percentage of chiropractors (75%) who find that adjustment of subluxation results in improved health of the patient, (4) the criterion of consistency would seem to be satisfied.
b) Given the literature on patients who report improvement after, not before, adjustment of subluxation, i.e., references 5-14 below, the criterion of temporality would seem to be satisfied.
c) Given the literature that proffers plausible theories supporting subluxation theory, i.e., references 15-19 below, the criterion of plausibility would seem to be satisfied.
3. The authors missed an opportunity to point out what it would take to satisfy Hill’s criteria. For example, would they recommend clinical studies, or case reports, or literature reviews, or all of the above? Some of these approaches have already been accomplished regarding the subluxation model, though additional research should be ongoing and would certainly strengthen the model.
4. The authors conclude that the “subluxation construct has no valid clinical applicability” yet they fail to provide hard data to support such a conclusion, apparently basing their conclusion on their lack of findings in the literature. The authors seem to have ignored the axiom that absence of evidence is not necessarily evidence of absence. (20-21)
John Hart, DC, MHSc Assistant Director of Research Sherman College of Chiropractic P.O. Box 1452 Spartanburg, S.C. 29304 USA
References
1. Mirtz TA, Morgan L, Wyatt LH, Greene L. An epidemiological examination of the subluxation construct using Hill's criteria of causation. Chiropractic and Osteopathy 2009 Dec 2; 17:13.
2. Hill AB. The environment and disease: association or causation? Proceedings of the Royal Society of Medicine 1965; 58:295-300.
3. Doll R. Sir Austin Bradford Hill and the progress of medical science. British Medical Journal 1992; 305:1521-1526.
4. McDonald WP, Durkin KF, Pfefer M. How chiropractors think and practice. The survey of North American chiropractors. Seminars in Integrative Medicine 2004; 2(3):92-98.
5. Alcantara J, Plaugher G, Van Wyngarden DL. Chiropractic care of a patient with vertebral subluxation and Bell's palsy. Journal of Manipulative and Physiological Therapeutics 2003; 26(4):253.
6. Kessinger RC, Boneva DV. Vertigo, tinnitus, and hearing loss in the geriatric patient. Journal of Manipulative and Physiological Therapeutics 2000; 23(5):352-62.
7. Alcantara J, Heschong R, Plaugher G, Alcantara J. Chiropractic management of a patient with subluxations, low back pain and epileptic seizures. Journal of Manipulative and Physiological Therapeutics 1998; 21(6):410-8.
8. Elster E. Upper cervical chiropractic care for a patient with chronic migraine headaches with an appendix summarizing an additional 100 headache cases. Journal of Vertebral Subluxation Research 2003:1-10.
9. Alcantara J, Steiner DM, Plaugher G, Alcantara J. Chiropractic management of a patient with myasthenia gravis and vertebral subluxations. Journal of Manipulative and Physiological Therapeutics 1999; 22(5):333-40.
10. Pistolese RA. Epilepsy and seizure disorders: a review of literature relative to chiropractic care of children. Journal of Manipulative and Physiological Therapeutics 2001; 24(3):199-205.
11. Echeveste A. Chiropractic Care in a Nine Year Old Female with Vertebral Subluxations, Diabetes & Hypothyroidism. Journal of Vertebral Subluxation Research 2008 (Jun 9):1-5.
12. Di Duro JO. Improvement in hearing after chiropractic care: a case series. Chiropractic and Osteopathy 2006; 14:2.
13. Plaugher G, Long CR, Alcantra J, Silveus AD, Wood H, Lotun K, Menke JM, Meeker WC, Rowe SH. Practice-based randomized controlled-comparison clinical trial of chiropractic adjustments and brief massage treatment at sites of subluxation in subjects with essential hypertension: Pilot study. Journal of Manipulative and Physiological Therapeutics 2002; 25(4): 221-239.
14. Bedell L. Successful care of a young female with ADD/ADHD & vertebral subluxation: A Case Study. Journal of Vertebral Subluxation Research 2008 (Jun 23):1-7.
15. Dishman R. Review of the literature supporting a scientific basis for the chiropractic subluxation complex. Journal of Manipulative and Physiological Therapeutics 1985; 8(3):163-174).
16. Marino MJ, Langrell PM. A longitudinal assessment of chiropractic care using a survey of self-rated health wellness & quality of life: A preliminary study. Journal of Vertebral Subluxation Research 1999; 3(2):1-9.
17. Sato A, Swenson RS. Sympathetic nervous system response to mechanical stress of the spinal column in rats. Journal of Manipulative Physiological Therapeutics 1984; 7(3):141-7.
18. Bolton PS. Reflex effects of subluxation: the peripheral nervous system. Journal of Manipulative Physiological Therapeutics 2000; 23(2): 101-103.
19. Budgell BS. Reflex effects of subluxation: the autonomic nervous system. Journal of Manipulative Physiological Therapeutics 2000; 23(2): 104-106.
20. Hartung J, Cottrell JE, Giffin JP. Absence of evidence is not evidence of absence. Anesthesiology 1983; 58:298-300.
21. Altman DG, Bland JM. Absence of evidence is not evidence of absence. British Medical Journal 1995; 311:485.
Competing interests
None declared
Subluxation, evidence-based medicine and epidemiology. Response to comments made by Drs. Demetrious and Hart
Timothy Mirtz, University of South Dakota
7 January 2010
We wish to thank Drs. James Demetrious and John Hart for their thoughtful Letters to the Editor concerning our recent paper “An epidemiological examination of the subluxation construct using Hill’s criteria of causation”[1].
Dr. Demetrious referred us to the paper by Phillips and Goodman entitled, “The missed lessons of Sir Austin Bradford Hill" [2]. We wish to point out that we specifically used the Phillips reference in our paper under the subheading “Limitations to utilizing Hill's Criteria” (Ref #32). Notwithstanding, Phillips and Goodman’s [2] concerns about “statistical significance” and “precision” are irrelevant in the case of subluxation because we simply have no credible data upon which to perform measures of “statistical significance” or “precision”. In our paper we readily agreed with Phillips and Goodman [2] that belief in “. . . a causal relationship is not sufficient to suggest action should be taken.” Something more than mere belief is needed. Unfortunately, in the case of subluxation, chiropractic has not much more than belief to offer. Furthermore, Phillips and Goodman [2] also noted that “Association does not prove causation (other evidence must be considered)”. We also wish to point out that merely discussing subluxation from anecdotal experience and case studies does not mean that a subluxation was actually encountered.
In essence we believe Dr. Demetrious is pointing to Phillips and Goodman’s [2] specific statement: Regulators often fail to act because we have not yet statistically "proven" an association between an exposure and a disease, even when there is enough evidence to strongly suspect a causal relationship.
Granted, our paper does not delve into or consider health policy formulation. But the fact remains that non-chiropractic policy regulators will eventually make decisions about subluxation based upon the best available scientific evidence. After 114 years of chiropractors making claims about the significance of subluxation as a causal factor for sub-optimal health and disease formation there has not been produced sufficient evidence to substantiate such bold claims.
The extant evidence is insufficient to strongly suspect a causal relationship between subluxation and disease and consequently to even go further into the realm of statistical significance seems unnecessary. In other words, the latter portion of the Phillips and Goodman [2] statement has not been met by the chiropractic profession.
We predict that our review will produce fear and apprehension by chiropractors. We also believe that chiropractors who are disenchanted with our findings will be calling upon Phillips and Goodman’s [2] work as “evidence” that there is a subluxation cause and effect association.
Dr. Hart believes that we somehow overlooked literature that would qualify for some of Hill’s criteria. Dr. Hart would like us to believe that the results of a survey of chiropractors (who believe in the subluxation construct) is sufficient evidence to conclude that subluxation can meet the consistency criteria. We respectfully refer Dr. Hart to our paper [1] that stated: For the chiropractic subluxation to meet these criteria it (subluxation) would have to be found repeatedly in different persons, places, times, and circumstances. In the case of a clinical condition, the subluxation would have to be consistently found with the clinical condition. To date there has not been a study that has found the subluxation in any one population (gender, race, ethnicity, age).
The study that Dr. Hart refers to [3] does not satisfy that there is a positive health outcome consistent with any variable such as gender, race, ethnicity or age. Thus the study [3] that Dr. Hart alludes to does not qualify as meeting the consistency criteria.
Dr. Hart also believes that given the literature on patients who report improvement after, not before, adjustment of subluxation that the criterion of temporality would seem to be satisfied. Dr. Hart cites references he believes meet the temporality criterion. For temporality to be met the subluxation must always precede the clinical condition for a true cause and effect scenario to take place. For example, Dr. Hart lists studies that are suggestive that subluxation is found in Bell's palsy, myasthenia gravis vertigo and tinnitus, diabetes, epilepsy and ADHD along with others from his list of references. These studies did not find the subluxation as causal of these clinical conditions. There are other pathophysiological processes that can easily be explanatory. These conditions have other, more scientifically-derived, etiologies.
It is worth noting that most manual medicine practitioners could deliver spinal manipulation to such a case without having to acknowledge that a subluxation was present or not. We find it interesting that only some chiropractors can find a subluxation associated with such pathological states whereas other chiropractors and health professionals do not. Furthermore, what Dr. Hart has provided are merely case studies which in the evidence hierarchy sits low on the spectrum of evidence. Case studies are merely capable of generating an hypothesis and do not prove causation or cure.
Dr. Hart believes that the subluxation model adequately satisfies the biological plausibility criterion. The biological plausibility criterion asks the question “does a pathophysiologic model of how the exposure could cause the disease make sense?” [1] In other words, does the subluxation as a pathophysiologic model of having a subluxation being a causal factor of disease make sense? We suggest that it does not make sense. Nansel and Szlazak [4] noted: it is extremely important to keep in mind that all of the "somato-visceral disease" theories and models put forth over the years, regardless of their lack of biological tenability, have also suffered from a common central premise, that is, that the patients involved in these rather "miraculous" clinical situations were really suffering from true visceral disease in the first place!
Nansel and Szlazak [4] noted: we are aware of not a single appropriately controlled study that has convincingly established that spinal manipulation represents a valid curative strategy for the treatment of any true visceral disease, even though scientifically unsubstantiated claims of such therapeutic efficacy continue to be all too prevalent throughout the chiropractic profession.
After 14 years since this seminal paper was published, we do not know of any study that has established spinal manipulation as a valid curative strategy. We do know that unsubstantiated claims of therapeutic efficacy continue to plague the chiropractic profession. It is our opinion that the ACC Paradigm [5] still lends itself to such claims of therapeutic efficacy in their own definition of a subluxation.
Furthermore, we believe that the non-biological plausibility of the subluxation, seen in the ACC Paradigm, is further explained by Nansel and Slazek [4]. They suggested that: there is not the slightest suggestion that patients suffering from severe, primary, mechanical low back pain, for instance, are more prone to develop higher incidences of prostate or testicular carcinoma, colitis, ovarian cysts, endometriosis, pancreatitis, appendicitis, diabetes mellitus or any other category of regionally or segmentally related organ disease.
We believe that this explanation alone is suggestive of the folly of the subluxation as a biologically plausible explanation as described by the ACC Paradigm [5]. Thus, the biological plausibility is unfounded. What Dr. Hart has brought forward are individual aspects (the five components of the subluxation i.e. kinesiopathology, neuropathology, etc) and suggests that each of these are somehow biologically plausible. By themselves, we agree that they have a level of biological plausibility. However, for a subluxation to be a true entity it should consist of all five components. And this is where the model, in our opinion, falls apart. There simply is no evidence whatsoever suggestive of this subluxation construct. In addition, the mentioning of the five components of subluxation yet detailing only part of the components does not make a subluxation. In summary, the notional entity known as subluxation (for it to be a subluxation) should have all the five components available. Furthermore, such an entity would have to meet cause and effect criteria to be a putative clinical entity worthy of intervention. Our review found no evidence of this.
Dr. Hart laments that we missed an opportunity to point out what it would take to adequately satisfy the criteria of causation. The purpose of this examination was to review the current evidence on the epidemiology of the subluxation construct and to evaluate the subluxation by applying epidemiologic criteria for its significance as a causal factor [1]. Thus our purpose was not in research design or methodology of examining the subluxation. We leave it to the subluxation advocates to address this.
As well, we must point out that we did not intentionally avoid the EBM principles in our paper. The purpose of the paper was to examine the subluxation construct using criteria of causation i.e. Hill’s Criteria. Dr. Demetrious should know that the EBM paradigm was developed by epidemiologists. A thorough reading of Sackett’s work [6] specifically notes the value of epidemiological principles.
However, Dr. Demetrious correctly noted the thoughts by Sackett et al [6], namely: • Evidence based medicine is the conscientious, explicit, and judicious use of current best evidence. • The practice of evidence based medicine means integrating individual clinical expertise with the best available external clinical evidence. • Evidence based medicine is not restricted to randomised trials and meta-analyses. It involves tracking down the best external evidence.
We emphatically agree with these views and believe we are quite familiar with the EBM paradigm. Nonetheless, we specifically point out that every single one of these points involves the use of actual evidence. The whole focus of our paper was to examine the evidence and report the findings. These findings demonstrate an absence of any coherent, credible, objective evidence that will support the subluxation construct as it relates to the ACC Paradigm [5]. Simply put, the evidence is simply not there.
It is true that we concluded that the subluxation construct has no valid clinical applicability as Dr. Hart asserts. However, Dr. Hart suggests that we failed to provide hard data to support such a conclusion. We stand by our conclusion based on the lack of findings in the literature. If the subluxation was a valid clinical entity the literature would bear this out. Thus the only conclusion one can draw is that subluxation is a suspect clinical entity.
As well, Drs. Hart and Demetrious have suggested that we have ignored the axiom that absence of evidence is not necessarily evidence of absence. We believe that this comment has been over-utilized by chiropractors to the point of being cringe-worthy. We also believe it is a shield to cover the chiropractic profession and is used as a measure of our collective lack of evidence. Our paper, although preliminary, is illustrative of the “proof of absence.” The burden of proof rests with the chiropractic profession.
We wish to leave this argument with a quote from Charles Darwin that we feel is appropriate to the subluxation debate: “Ignorance more frequently begets confidence than does knowledge.”
Again, we wish to thank Drs. Hart and Demetrious for taking the time to critique of our work and we look forward to seeing new credible research that explores the theoretical construct that is subluxation.
Timothy Mirtz DC, PhD, CHES, CAPE Lon Morgan DC, DABCO Larry Wyatt DC, DACBR Leon Greene PhD
References
[1] Mirtz TA, Morgan L, Wyatt LH, Greene L. An epidemiological examination of the subluxation construct using Hill's criteria of causation. Chiropractic and Osteopathy 2009; 17:13.
[2] Phillips CV, Goodman KJ. The mixed lessons of Sir Austin Bradford Hill. Epidemiol Perspect Innov 2004;1:1-5.
[3] McDonald WP, Durkin KF, Pfefer M. How chiropractors think and practice. The survey of North American chiropractors. Seminars in Integrative Medicine 2004; 2(3):92-98.
[4] Nansel D, Szlazak M. Somatic dysfunction and the phenomenon of visceral disease simulation: a probable explanation for the apparent effectiveness of somatic therapy in patients presumed to be suffering from true visceral disease. J Manipulative Physiol Ther. 1995;18(6):379-97.
[5] Association of Chiropractic Colleges. A position paper on chiropractic. J Manipulative Physiol Ther 1996;19:634-637.
[6] Sackett, DL. Straus SD, Richardson WS, Rosenberg W, Haynes RB. Evidence-based Medicine: How to Practice and Teach EBM. 2nd Edition. 2000. Churchill-Livingstone. Edinburgh.
Competing interests
The authors declare no competing interests.
A Criticism of an Epidemiological Examination of the Subluxation Construct using Hill’s Criteria of Causation: Limitations, Suspect Conclusions and an Opportunity Missed
Christopher Good, University of Bridgeport College of Chiropractic
6 May 2010
As a chiropractic practitioner and educator over the past three decades I have been privileged to share the science, art and philosophy of the profession with thousands of patients, students and field doctors in both the United States and Europe. So it was with great interest that I read the work of Mirtz et al concerning the subluxation construct (SC) [1]. Indeed, their epidemiological examination of the SC utilizing Hill’s criteria was an opportunity to consider an important perspective regarding some of the evidence pertaining to it. It was also an opportunity to positively affect the evolution of the profession by buttressing the calls some academics have made to improve the SC, especially as it pertains to clinical practice [2,3]. Upon reflection however, it became apparent there were a number of critical shortcomings made by Mirtz and co-authors that rendered their final conclusions suspect, if not invalid. Specifically, the conclusions that the SC is “in the realm of unsupported speculation” and has “no valid clinical applicability” are not simply flawed, but in my view reckless and harmful. This may have moved the profession further away from coming to a valid, respected and unified position in regards to these matters; in essence a golden opportunity was missed. The purpose of this comment is to address the most important shortcomings of their article, identify information worthy of further consideration and make suggestions that would advance the understanding of the SC as reflected in contemporary chiropractic education and practice.
The first and most serious shortcoming involves a fundamental misuse of the work of Sir Austin Bradford Hill and the criteria he proposed to examine claims of causation between some agent or event and subsequent disease. Bradford Hill’s work has been chronicled by Yoshioka [4] and is illuminating to read. It begins in 1937 with a series of articles in The Lancet regarding the design of clinical trials (with a focus on randomization) and these eventually became the basis for his textbook on medical statistics. The story continues in the aftermath of WW II when tuberculosis was common and deadly and pharmacological interventions were being sought. The antibiotic streptomycin had recently been developed (1943) and because of its success in guinea pigs human trials followed. In 1946 a successful clinical study in England was performed using the new drug and this trial had the unique feature of including a randomly allocated control group as Bradford Hill had advocated. Over the next 20 years Sir Austin organized his thoughts regarding claims of causation primarily as they related to environmental exposures to toxins in the workplace. This culminated in his highly informative and entertaining address to the newly founded Section of Occupational Medicine of the Royal Society of Medicine [5] and gives a powerful depiction of the knowledge and attitudes of the man. His concern was focused on interpreting the observational evidence of the day, especially in the absence of more in-depth clinical research. But as important were the warnings he gave to those who would misuse his work, which is particularly relevant here:
"What I do not believe – and this has been suggested – is that we can usefully lay down some hard-and-fast rules of evidence that must be obeyed before we accept cause and effect. None of my nine viewpoints can bring indisputable evidence for or against the cause-and-effect hypothesis and none can be required as a sine qua non [5]."
It is clear from the preceding that Sir Austin did not believe that examination of any evidence by his criteria was the only means of determining the validity of claims of causation in a disease process. In fact that role is played by a well constructed randomized clinical trial (RCT) [6]. Currently it is suggested that Hill’s criteria are actually best utilized as an educated guess when observational studies or other data have been collected and are assessed. This is because Hill’s criteria have come under intense debate given the flaws inherent in their utilization, which begins with problems encountered in even defining the criteria themselves. For example, all of the criteria have been observed to be ambiguous, vague and/or have the potential to create any number of logical fallacies [7,8]. Instead, as Ward proposes, Hill’s criteria are best utilized as inferences of best explanation. Under this model the practitioner is warned of the flaws inherent in strictly applying Hill’s criteria and instead utilizes them as the basis for insight and further scientific investigation [6]. I would suggest that this is essentially where Mirtz and co-authors have gone astray. Their strict application of Hill’s criteria in regards to reviewing the literature is directly contrary to what Sir Austin advised, and given the shortcomings inherent in the criteria, it is also contrary to the current best use of his criteria.
The next major shortcoming involves the primary assumption the authors make when they state that the purpose of their paper involved “how the concept of subluxation is currently embraced by the chiropractic profession.” I submit that to truly understand the depth and breadth of the subluxation construct as currently embraced by the profession one must begin with a thorough reading of the current editions of the most evidence-based textbooks used in contemporary chiropractic education. The following is a short list of the texts that I believe best represent the subluxation construct as it currently exists in the profession (author or editor and year of publication included): Principles and Practice of Chiropractic (Haldeman, 2005) [9], The Chiropractic Theories: A Textbook of Scientific Research (Leach, 2004) [10], Chiropractic Technique: Principles and Procedures (Peterson and Bergmann, 2002) [11], Foundations of Chiropractic: Subluxation (Gatterman, 2005) [12], and Technique Systems in Chiropractic (Cooperstein and Gleberzon, 2004) [13].
If one were to read these texts it would become very clear that the current state of the chiropractic profession in regards to the SC is not accurately depicted in the paper by Mirtz et al. In essence the authors focused on a very narrow element of the construct, namely the subluxation as a cause of a visceral disease. In reality the current model of the SC has as its focus the concept often described to patients as the “painful sticky joint.” This is identified in Peterson and Bergmann’s Chiropractic Technique as “joint subluxation/dysfunction syndrome” and is associated with local pain, tissue hypersensitivity, decreased joint movement and other local findings [11]. This definition of subluxation is the foundation of their book, a text that has been adopted by no less than 10 of the current chiropractic colleges in the US and many of the programs outside of the States (personal communication, K White, Senior Editor, Elsevier Publishing). Similarly, Leach defines the contemporary version of the SC as spinal “segmental dysfunction” and describes the lesion as having a loss of motion, local tenderness and increased tension in paraspinal muscle [10]. Curiously enough, a permutation of the SC is also identified as “spinal joint dysfunction” by one of Mirtz’s co-authors in the text Handbook of Clinical Chiropractic Care. In his book Wyatt states that “this lesion can cause focal or diffuse spine pain, radiating pain not below the elbow or knee, and/or referred pain simulating visceral disease [14].” Furthermore, more complex musculoskeletal conditions based on regional spinal joint dysfunctions have been described by Gatterman and her co-contributors [12]. Their text provides a well evidenced clinical approach to patient care based on the SC and includes a categorization and description of various subluxation syndromes. The focus of these syndromes is clearly within the musculoskeletal system and includes cevicogenic headache, thoracic outlet syndrome associated with first rib subluxation, thoracic and costovertebral subluxation syndromes, lumbar facet subluxation syndrome, intervertebral disc syndrome, sacroiliac subluxation syndrome, coccygeal subluxation syndrome, and cevicogenic sympathetic syndrome, among others. Therefore, as noted above, segmental dysfunction and musculoskeletal oriented subluxation syndromes are the common and well recognized modern permutations of the SC. It is also clear that this musculoskeletal focus is the basis for contemporary clinical practice, as observed by Smith and Carber [15]:
"Most chiropractors typically reported that over 75% of their clinical approach to addressing musculoskeletal or biomechanical disorders such as back pain was “subluxation-based.” Conversely, most chiropractors also reported that less than 20% of their clinical approach was “subluxation-based” for patient complaints deemed to be principally problems with circulation, digestion, or similarly “visceral” in nature."
To return to the paper by Mirtz and colleagues, even if one accepts their findings that to date there was no published epidemiological evidence for a specific subluxation-induced disease, it is obvious their conclusion that the SC “has no clinical applicability” must be rejected as a flawed over generalization given the current musculoskeletal focus of subluxation in regards to patient care. This oversight is particularly puzzling since Mirtz et al cited Smith and Carber’s paper in their article. Unfortunately the advice of Smith and Carber to move beyond the polarized polemics of the past seems to have been missed as well.
The third significant shortcoming by Mirtz et al involved the use of the ACC presidents’ definition of subluxation [16], which itself has serious limitations. In the first case this definition is outdated; in the second it is far too ambiguous to be useful as the basis for such work because it is prone to selective interpretation. Probably the observation that the definition is “beautifully vague and vaguely beautiful” is one of the best things that can be said about it [17]. This is understandable however because it was the result of consensus building and was not intended as a basis for research endeavors. To elucidate, when the position paper on chiropractic was produced by the North American college presidents in the mid 1990s this was seen by many as a remarkable outcome in a land of significant political divide. The subluxation definition was an attempt to bring unity to the profession at a time when this was (and is) sorely needed, and in doing so a definition was created that was as broad and inclusive as possible. As Leach noted, the definition was most appropriately seen as a significant step in the maturation of the profession and a move away from vitalism [10]. Keating et al [3] have identified additional problems with the presidents’ definition, but suffice it to say that as written the definition could encompass virtually all forms of clinical conditions involving a spinal motion segment. However, in the realm of contemporary chiropractic education and practice the presidents’ definition is best interpreted as follows: the spine and pelvis are considered in regards to functional, structural and/or pathoanatomical changes to the intervertebral disc, zygapophyseal, uncovertebral, atlantooccipital, atlantoaxial, atlantoodontal, sacroiliac, sacrococcygial and symphysis pubis articulations and the neurological reactions associated with those changes, the most common of which is nociception. However the representation of the presidents’ definition of subluxation by Mirtz and colleagues is far from this. By choosing to focus on the most tenuous element of the definition (i.e. subluxation as a cause of visceral disease) they have developed a straw man argument in the guise of a questionable narrative literature review. In actuality what the authors have shown is that the presidents’ definition has shortcomings that are easily exposed under academic scrutiny. But in no way can one extend their conclusions to all elements of the SC because these were not thoroughly defined, investigated or reported on, which leads to the next major shortcoming.
A fatal shortcoming of Mirtz et al involved the methods utilized in the literature review itself. Before conclusions can be made regarding whether the SC has clinical applicability a properly performed systematic review would have to be done [18,19]. At the very least this would require actually evaluating the quality of the studies pertaining to Hill’s criteria, which would begin with studies in which both aspects of interest were measured (i.e. the subluxation and some type of disease). Additionally, it would also involve obtaining and assessing the quality of any study in which an association was evaluated between any one of the aspects included in the definition of the SC and any health condition, including those studies which had not addressed Hill’s criteria specifically. The review offered by Mirtz et al clearly does not rise to these standards, and if fact, even minimally accepted standards regarding published literature reviews were not met. Nowhere in their paper is there a description of the total number of “hits” the search terms returned (either in isolation or combination), the effect the inclusion and exclusion criteria had on these hits, or the final tallies of the papers that were included or rejected in the application of these criteria. Reporting this information is common procedure when publishing the results of a literature review [19]. Without it the reader is not able to reproduce the work, consider the quality of the search or assess any biases. Additionally, it is also reasonable to assume that given the contentious nature of the word subluxation contemporary authors (including those outside of chiropractic) are using different terms such as “segmental dysfunction” or “spinal joint dysfunction” to describe the subluxation, which were terms not included in the Mirtz et al literature search. Ultimately it is not possible to accept at face value the result that only four peer-reviewed journal articles exist and were able to be examined per Hill’s criteria. But even if it was accepted (as other authors have noted) that there is a paucity of epidemiological investigations regarding the SC [20,21], then the observation that the subluxation fared poorly in regards to Hill’s criteria is best explained by the fact that the investigations simply have not been done and/or the research investigations haven’t been published. Ultimately the conclusion by Mirtz et al that the subluxation construct is “in the realm of unsupported speculation” cannot be made until it is supported by the findings of a comprehensive and properly performed systematic review and even then any conclusion would have to placed into context relative to the number of high quality studies that have actually been performed; without it their assertion is meaningless if not misleading. This leaves the last major shortcoming of the work, which is tied directly to the highly evocative nature of the debate involving the subluxation. As stated above, I am of the opinion that the conclusions of the authors are not just flawed, but are harmful. This is because inflammatory conclusions only serve to strengthen the resolve of those who embrace the most speculative aspects of the SC and/or those who view subluxation as their raison d'être and practice within a narrow scope as described by McDonald [22]. Such conclusions make the article prone to being discarded as just another “subluxation bashing” paper designed to humiliate and eliminate narrow scope practitioners. But isn’t this the group that many of us are hoping to influence the most? Is this the best way to encourage a cultural change, especially when considering the number of chiropractors with more moderate views (i.e. the “middle scope practitioners” [15, 22]) who hold a contemporary understanding of the SC and would reject the Mirtz paper on similar grounds?
What makes the conclusions of Mirtz and colleagues particularly reckless however is the reality that journal articles (and their shortcomings) are so quickly and broadly disseminated. Articles in the Journal of Chiropractic and Osteopathy become included in the most important science and health care data bases that exist, such as MEDLINE as accessed through PubMed. It is very clear that perceptions of the chiropractic profession by the public (including current and potential patients, litigants, healthcare policy makers and other healthcare providers) can be directly impacted by our publications. Once published, these papers provide ammunition to chiropractic adversaries at a time when the profession can least enjoy it. I believe there are important lessons to be learned by all parties involved in chiropractic journal publications, and this includes not only authors but also peer-reviewers and journal editors. We are the stewards of this important source of information and we all need to act in a responsible fashion.
The debate regarding the various elements of the SC is obviously important for our patients and our profession. As noted above the majority of patients enter chiropractic offices with musculoskeletal complaints and often this is thought to be associated with some type of painful joint dysfunction. Some patients have also reported success with non-musculoskeletal conditions [23,24] and new patients come to our offices with the hope that they will experience those same benefits. It is clear that there is a lack of published research in this domain and this has been thoughtfully presented by Hass et al as an outcome of the most recent Chiropractic Research Agenda initiative [21]. A contemporary perspective in regards to visceral conditions and the subluxation has also been described by Budgell in which he differentiates between subluxation as a cause of a specific disease (not very likely) and subluxation as a component of functional visceral disorders by virtue of somatoautonomic or other neurophysiological mechanisms (more likely) [12]. Comprehensive reviews of the evidence concerning chiropractic care for non-musculoskeletal conditions by Leach [10] and chapters by Vernon and Sarnat and Budgell [9] provide an excellent contemporary education in this area. Vernon in particular offers an important algorithm for care when patients present with visceral signs and symptoms. Additionally, the work of Hawk et al has shifted the paradigm of chiropractic care for non-musculoskeletal conditions into one focusing on whole system research, which might be more appropriate in some cases [25]. Her work as well as those of others regarding all aspects of chiropractic care has been the focus of the Council on Chiropractic Guidelines and Practice Parameters (CCGPP) and their literature syntheses are important, must read publications [26]. Interestingly, one task yet to be completed by the CCGPP involves a chapter on subluxation, which if written with the same due diligence as the other chapters, should become an excellent resource for the profession.
Finally, I would also submit that segmental dysfunction as a cause of non-musculoskeletal disorders due to reactions within the nervous system are far from having no evidence, much less no clinical applicability. For example, the contemporary version of the subluxation construct includes the well established cauda equina syndrome as a result of severe intervertebral disc disruption, among other things [12]. Additionally, numerous non-musculoskeletal case studies exist as noted by Leach [10] and Sarnat and Budgell [9], and while case studies are one of the weakest forms of clinical evidence, they are evidence nonetheless. Of course causality cannot be determined by case studies, but descriptions of patients who obtained a significant benefit (or harm, as the case may be) are worthy of clinical consideration and further research, and should not be ignored. Also, by maintaining a continually evolving SC as a core component of clinical education and practice the chiropractic profession retains its unique perspective, meanwhile establishing a profession which offers high quality patient care based on the best available evidence. The SC provides an environment of inquiry so that researchers are able to pursue alternative hypotheses in regards to non-musculoskeletal clinical presentations, such as the effect adjusting upper cervical subluxation has on blood pressure [27] or on neck-tongue syndrome [28]. It also creates a model from which to understand mimicry conditions such as pseudo-angina associated with thoracic region segmental dysfunction [29,30].
In my opinion though, what is particularly ripe for investigation are the hypothesized somatoautonomic reflex phenomena associated with the SC. Just as the profession initially focused its research efforts on our most commonly observed musculoskeletal successes (low back pain, neck pain and headache), it now seems prudent to focus some of our resources on the most common non-musculoskeletal presentations. I would offer my clinical observations (and unfortunate experiences as a patient) regarding severe lumbar spinal pain and dysfunction and associated transient constipation as an ideal place to start. It would seem that of all the likely candidates from which to establish a painful joint dysfunction as a cause of visceral dysfunction, this presumed sympathetic nervous system reaction sits at the top the list given its frequency and temporality. But of course, in order for this research to proceed the criteria often identified on television police dramas must first be grappled with: means, motivation and opportunity. I believe we have researchers with enough motivation, but is the profession ready to provide the means and opportunity…or is it going to continue to live in the world of poorly evidenced hypotheses and let the vocal minorities at the extremes of our profession run (or ruin) the debate?
Despite the shortcomings of Mirtz et al’s paper, the examination of the SC in regards to Hill’s criteria is still important because it provides a framework for understanding the most important issues regarding claims of causation and it identifies areas in need of epidemiological research. It also highlights the shortcomings of the ACC presidents’ definition of subluxation and a carefully crafted revision of it appears to be warranted. Lastly, given the continued improvement in chiropractic education and the profession’s textbooks, a chasm has emerged between a contemporary understanding of the subluxation construct and historical notions held by some. Instead of denigrating those beliefs in our journal publications, a concerted effort must be made to continually update our colleagues so that we are able to offer the best casting of our valued profession to our patients and society at large.
Christopher Good DC, MA(Ed) Professor of Clinical Sciences University of Bridgeport College of Chiropractic
References [1] Mirtz TA, Morgan L, Wyatt LH, Greene, L: An Epidemiological Examination of the Subluxation Construct using Hill’s Criteria of Causation. Chiro & Osteo 2009, 17(13). [2] Good, C: Subluxation Syndromes: A Condition Whose Time Has Come? J of Chiropr Hum, 2004; 11:38-43. [3] Keating JC, Carlton KH, Grod JP, Perle SM, Sikorski S, Winterstein JF. Subluxation: dogma or science? Chiro & Osteo 2005, 13: 17. [4] Yoshioka, A. Use of randomization in the Medical Research Council’s clinical trial of streptomycin in pulomonay tuberculosis in the 1940s. BMJ 1998, 317: 1220-3. [5] Hill AB. The environment and disease: association or causation? Proc R Soc Med 1965, 58: 295-300. [6] Ward AC. The role of causal criteria in causal inferences: Bradford Hill’s “aspects of association.” Epidemiologic Perspectives & Innovations 2009, 6: 2. [7] Rothman KJ, Greenland S: Causation and causal inference in epidemiology. Am J Public Health. 2005, 95: S144-S150. [8] Rothman KJ, Greenland S, Poole C, Lash TL: Casuation and casual inference. In: Modern Epidemiology 3rd edition. Edited by: Rothman KJ, Geenland S, Lash TL. Philadelphia, PA: Lippincott, Williams and Wilkins; 2008:6-31. [9] Haldeman S (ed): Principles and Practice of Chiropractic. McGraw-Hill; 2005. [10] Leach RA: The Chiropractic Theories: A Textbook of Scientific Research. Lippincott, Williams and lkins; 2004: 48, 138, 563-566. [11] Peterson D, Bergmann T: Chiropractic Technique. Mosby: 2002:104. [12] Gatterman MI: Foundations of Chiropractic: Subluxation. Elsevier-Mosby: 2005:373-556, 563-566, 530-31. [13] Cooperstein R, Gleberzon BJ: Technique Systems in Chiropractic. Churchill Livingstone: 2004. [14] Wyatt LH: Handbook of Clinical Chiropractic Care. Jones and Bartlett: 2005:290. [15] Smith M and Carber LA. Survey of US chiropractor attitudes and behaviors about subluxation. J of Chiropr Hum, 2008, 19-26. [16] Association of Chiropractic College. A position paper on chiropractic. J Manipulative and Physiol Ther 1996,19: 634-637. [17] Good C. Creating a common sense of identity during post-graduate and continuing education courses. In: Proceeding from the World Federation of Chiropractic/Association of Chiropractic Colleges’ Education Conference on Professional Identity and Curriculum, World Federation of Chiropractic: 2006:149. [18] Moher D, Tetzlaff J, Tricco AC, Sampson M, Altman DG. Epidemiology and reporting characteristics of systematic review.. PLoS Med 2007, 4 (3): e78. [19] Green, B.N., Johnson, C.D. and Adams, A. Writing narrative literature reviews for peer-reviewed journals: secrets of the trade. Journal of Chiropractic Medicine. 2006, 5(6):101-14. [20] Mootz RD, Shekelle PG, Hansen DT. The politics of policy and research. Topics Clin Chiro. 1995, 2(2):56-70. [21] Haas M, Bronfort G and Evans RL. Chiropractic clinical research: progress and recommendations. J Manipulative and Physiol Ther. 2006, 29(9):695-706. [22] McDonald WP (ed). How Chiropractors Think and Practice. Institute for Social Research, Ohio Northern University; 2003. [23] Hawk C, Long CR and Boulanger KT. Prevalence of non-musculoskeletal complaints in chiropractic practice: report from a practice-based research program. J Manipulative and Physiol Ther. 2001, 24(3):157-69. [24] Leboeuf-Yde C, Pedersen EN, Bryner P, Cosman D, Hayek R, Meeker WC, Shaik J, Terrazas O, Tucker J, Walsh M. Self-reported non-musculoskeletal responses to chiropractic intervention: a multination survey. J Manipulative Physiol Ther. 2005 Jun, 28(5):294-302. [25] Hawk C, Khorsan R, Lisi AJ, Ferrance RJ, Evans MW. Chiropractic care for non-musculoskeletal conditions: a systematic review with implications for whole systems research. J Altern Complement Med. 2007, Jun, 13(5):491-512. [26] The Council on Chiropractic Guidelines and Practice Parameters [http://www.ccgpp.org]. [27] Bakris G, Dickholtz M, Meyer PM, Kravitz G, Avery E, Miller M, Brown J, Woodfield C, Bell B. Atlas Vertebra Realignment and Achievement of Arterial Pressure Goal in Hypertensive Patients: A Pilot Study J Hum Hypertens. 2007 (May), 21(5):347–352. [28] Borody C. Neck-tongue syndrome. J Manipulative Physiol Ther. 2004 Jun, 27(5):367e6. [29] Wax CM, Abend DS, Pearson RH. Chest pain and the role of somatic dysfunction. JAOA 1997, 97(6):347-355. [30] Smith M, Lawrence DJ, and Rowell RM. Management of chest pain: exploring the views and experiences of chiropractors and medical practitioners in a focus group interview. Chiro & Osteo. 2005, 13:18
Competing interests
None
Subluxation epidemiology: a response to Dr. Good
Timothy Mirtz, University of South Dakota
10 May 2010
We wish to thank Dr. Good for his response to our recent work that was published in the December issue of Chiropractic & Osteopathy. In attempting to sift through the lengthy comment provided by Dr. Good we have chosen to only address the key points he makes.
We do not believe that the conclusion of the subluxation construct (SC) having “no valid clinical applicability” is flawed. Nor is it reckless and/or harmful. Simply put, if there is little or no data providing evidence of the SC combined with and the claim chiropractors make to treat this putative entity as a causal agent then its validity should be considered unproven. Until data comes forth that can adequately demonstrate the existence of the SC and provide the necessary data that demonstrates that it is a causative agent in disease or ill health then the SC should be regarded as having no such valid utility. One cannot say that some thing is causative for disease in the hope that someday science will somehow and some way catch up with it. We find this wholly unacceptable of any group of health practitioners to make such statements. It is not enough to accept the SC because a profession has historically “hitched its wagon” to a suspect entity.
Our intent, in writing the paper, was not in hope of unifying the profession or tearing it asunder. It was, however, an exercise in attempting to search the literature and apply the criteria of causation generally accepted by the epidemiological community. We are perplexed by Dr. Good’s assertion that our paper may have moved the profession further away from coming to a valid and respected unified position. In fact, the definition that we utilized was the ACC Paradigm which has been accepted by most, if not all, of the leading chiropractic organizations. It appears that the ACC Paradigm on subluxation is the unifying definition. For this reason we believe that using various definitions from various authors of chiropractic textbooks would have been problematic. It is worthy of note that none of the definitions in the works cited by Dr. Good provide any data that can attest to the SC being a causative agent in disease.
Dr. Good claims that the ACC Paradigm is outdated and ambiguous. We wholeheartedly agree with this assessment. We nonetheless disagree with the assessment that the ACC Paradigm is somehow “beautifully ambiguous.” We also suggest that the textbook authors various opinions on a SC definition are just as vague and ambiguous and lack the rigor of any substantive supportive scientific data.
It is not surprising to see Dr. Good (and possibly others) go directly to Sir Austin and examine his feelings on his very own work. It is true that Sir Austin did not intend for his criteria to be hard and fast rules. However, epidemiologists still refer to them and hold these criteria as foundational to the workings of epidemiology. In our work, we believed it was important to use his tenets to begin the investigation of the epidemiology of the SC. The use of the criteria provides a starting point for this investigation. In our investigation, we found no evidence to support the SC or an epidemiology for causation. Unless Dr. Good or any other person has solid evidence to support that the SC is causative we remain firm in our findings and our conclusions.
We do take issue with Dr. Good in his suggestion that we focused on a narrow element of the construct. As explained previously we utilized the ACC Paradigm which has been accepted by many leading organizations in the chiropractic profession. As well, Dr. Good alludes to the fact that there is a “joint subluxation/dysfunction syndrome.” This syndrome has never been documented to actually exist as a functional diagnosis nor does it have any evidence supporting it in relation to any known disease process. As per the consideration that the SC is somehow a “permutation” is nothing more than an attempt to offer some sort of validation to a construct that has not been scientifically validated. As well, the reference that 75% of chiropractors consider their clinical approach to be “subluxation-based” does not make the SC a reality or that there is sufficient research evidence suggestive that the SC is a causative agent. This is a common logical fallacy called the fallacy of consensus gentium (i.e. arguing that an idea is true on the basis that the majority of the people believe it.) Definitions that are commonly accepted for the subluxation have often been political in nature and cannot be used as testable models. Thus, a political definition such as put forward for the SC offers a difficult investigation using an epidemiological protocol.
Dr. Good noted our methodology. It is true that a systematic review would have included the number of “hits” in the search results and document inclusion and exclusion criteria. Nevertheless, using a very broad search strategy we were hard pressed to find any literature to support the SC that matched the definitions of the causation criteria. Furthermore, Dr. Good believes that other researchers are using terms such as “segmental dysfunction” and/or “spinal joint dysfunction” to describe the SC. To date, we are unaware of any serious research that describes “segmental dysfunction” and/or “spinal joint dysfunction” as causative of disease.
We take issue with Dr. Good when he stated that: “Ultimately the conclusion by Mirtz et al that the subluxation construct is in the realm of unsupported speculation cannot be made until it is supported by the findings of a comprehensive and properly performed systematic review and even then any conclusion would have to placed into context relative to the number of high quality studies that have actually been performed; without it their assertion is meaningless if not misleading.” We believe that the conclusion that the SC is in the realm of unsupported speculation due to the fact that there are no high quality studies that have validated the SC as causative. If Dr. Good has a number of high quality studies that leaves no doubt to the existence of the SC and these high quality studies scientifically verify that the SC is causative of disease then our opinion can be amended.
As stated previously, our intent, in writing the paper, was not in hope of unifying the profession or tearing it asunder. Nor was it intended to “bash” the profession or alienate or humiliate certain practitioners. Also, our intent in writing this paper was not to influence the general public or provide ammunition to chiropractic adversaries. We disagree vehemently with Dr. Good that researchers are somehow obligated to make sure that their research does not have political implications that could be construed as “costly.” We find the comments by Dr. Good in this regard to be very troubling.
In closing, we appreciate Dr. Good’s comments of our work. While there is little doubt that we are in disagreement with many of his responses, we suggest to Dr. Good that he provide the necessary data to support the existence of the SC that is testable, reproducible, and that there are screening measures that are valid to assess the SC. And when this is accomplished we suggest the next step would be to provide the necessary data, using the criteria of causation, in making the determination that this SC is a causative agent in disease. If this is achieved it falls to well supported chiropractic researchers to assess whether the act of spinal manipulation is a curative strategy. To date, none of these steps have been adequately fulfilled. This leaves us with no other conclusion than to suggest that the SC is a theoretical construct and at this time has only speculative clinical applicability.
Timothy A. Mirtz DC, PhD Lon Morgan DC, DACBR Lawrence Wyatt DC, DACBR Leon Greene PhD
Chiropractic & Manual Therapies
Subluxation, Hill's Criteria of Causation and EBM
29 December 2009
I read with interest the paper written by Mirtz et al. I have reservations regarding the authors’ conclusions pertaining to the manner in which they have editorialized the subject matter and applied Hill’s Criteria of Causation.
First, I would direct the authors to the paper written by Phillips and Goodman [1] entitled, “The missed lessons of Sir Austin Bradford Hill." Phillips and Goodman report the following:
Making a good decision does not depend on having studies with confidence intervals that exclude the null. A best decision can be based on whatever information we have now, and indeed a decision will be made – after all, the decision to maintain the status quo is still a decision. Hill offered his clearest condemnation of over-emphasizing statistical significance testing, not when he discussed p-values, but when he concluded by saying: "All scientific work is incomplete – whether it be observational or experimental. All scientific work is liable to be upset or modified by advancing knowledge. That does not confer upon us a freedom to ignore the knowledge we already have, or to postpone the action that it appears to demand at a given time."
This would release us from the trap of letting ignorance trump knowledge. Regulators often fail to act because we have not yet statistically "proven" an association between an exposure and a disease, even when there is enough evidence to strongly suspect a causal relationship. There is a growing movement to escape this mistake by making a similar mistake in the other direction: adopting precautionary principles, which typically call for restrictions until we have "proven" lack of causal association – a decision based on ignorance that merely reverses the default. If we can escape from the false dichotomy of "proven vs. not proven," facilitated by the non-existant bright line implied by statistical hypothesis testing and by the notion that causality can be definitively inferred from a list of criteria, then we can make decisions based on what we do know rather than what we don't.
The uncritical repetition of Hill's "causal criteria" is probably counterproductive in promoting sophisticated understanding of causal inference. But a different list of considerations that can be found in his address is worthy of repeating:
• Statistical significance should not be mistaken for evidence of a substantial association.
• Association does not prove causation (other evidence must be considered).
• Precision should not be mistaken for validity (non-random errors exist).
• Evidence (or belief) that there is a causal relationship is not sufficient to suggest action should be taken.
• Uncertainty about whether there is a causal relationship (or even an association) is not sufficient to suggest action should not be taken.
These points may seem obvious when stated so bluntly, but causal inference and health policy decision making would benefit tremendously if they were considered more carefully and more often. The last point may be the most important unlearned lesson in health decision making.
In fairness to those who do not appreciate these points even today, it over-interprets Hill's short paper to claim that he clearly laid out these considerations, or that he was calling for modern decision analysis and uncertainty quantification. But the fundamental concepts were clearly there (and the over-interpretation is not as great as that required to derive a checklist of criteria for determining causation). Several generations of advancement in epidemiology and policy analysis provide much deeper exposition of his points. But Hill still offers timeless insightful analysis about how to interpret our observations. Strangely, these forgotten lessons, which are only slowly and grudgingly being appreciated in modern epidemiology, are hidden in plain sight, in what is possibly the best known paper in the field.
It is my impression that Mirtz et al. have exercised an uncritical repetition of Hill's, "causal criteria," that is counterproductive in promoting a sophisticated understanding of causal inference related to the term, “subluxation.”
I would also caution the authors to carefully apply the tenets of evidence based medicine. Sackett et al. [2] conveyed the following thoughts:
• Evidence based medicine is the conscientious, explicit, and judicious use of current best evidence in making decisions about the care of individual patients.
• The practice of evidence based medicine means integrating individual clinical expertise with the best available external clinical evidence from systematic research.
• Good doctors use both individual clinical expertise and the best available external evidence, and neither alone is enough.
• Evidence based medicine is not restricted to randomised trials and meta-analyses. It involves tracking down the best external evidence with which to answer our clinical questions.
Finally, the opinion of Resnick [3] bears consideration: “Evidence-based medicine is a useful tool for summarizing and grading the evidence available in the literature for or against a particular treatment strategy. Its utility is limited by the quality of the primary literature, and the absence of proof cannot be equated with the proof of absence.”
When considering the term, “subluxation,” utilized by the chiropractic profession, it is my impression that stringent adherence to epidemiologic constructs and evidence based medical protocols must not over-shadow clinical experience. Authors must integrate clinical experience and the best available external evidence.
References
1. Phillips CV, Goodman KJ: The missed lessons of Sir Austin Bradford Hill. Epidemiologic Perspectives & Innovations 2004, 1:3.
2. Sackett DL, Rosenberg WMC, Gray JAM, Haynes RB, Richardson WS: Evidence based medicine: what it is and what it isn't: It's about integrating individual clinical expertise and the best external evidence. British Medical Journal 1996, 312(7023): 71-72.
3. Resnick DK: Evidence based spine surgery. Spine 2007, 32(11): S15-S19.
James Demetrious, DC, FACO
Wilmington, NC
Competing interests
No competing interest exists with regard to my professional judgment about the referenced paper that could possibly be influenced by considerations other than the paper's validity or importance.
Literature support for subluxation theory
5 January 2010
Editor:
The article by Mirtz et al regarding the application of Hill’s criteria to test whether or not subluxation is causal (1) is interesting but has a few problems, as follows.
1. Hill seems to apply his criteria to association first, rather than causation. (2) Indeed Hill himself warns that criteria alone do not establish cause-and-effect relationships. (2-3)
2. The authors seem to have overlooked literature that could qualify for at least some of Hill’s criteria for association. For example:
a) Given the large percentage of chiropractors (75%) who find that adjustment of subluxation results in improved health of the patient, (4) the criterion of consistency would seem to be satisfied.
b) Given the literature on patients who report improvement after, not before, adjustment of subluxation, i.e., references 5-14 below, the criterion of temporality would seem to be satisfied.
c) Given the literature that proffers plausible theories supporting subluxation theory, i.e., references 15-19 below, the criterion of plausibility would seem to be satisfied.
3. The authors missed an opportunity to point out what it would take to satisfy Hill’s criteria. For example, would they recommend clinical studies, or case reports, or literature reviews, or all of the above? Some of these approaches have already been accomplished regarding the subluxation model, though additional research should be ongoing and would certainly strengthen the model.
4. The authors conclude that the “subluxation construct has no valid clinical applicability” yet they fail to provide hard data to support such a conclusion, apparently basing their conclusion on their lack of findings in the literature. The authors seem to have ignored the axiom that absence of evidence is not necessarily evidence of absence. (20-21)
John Hart, DC, MHSc
Assistant Director of Research
Sherman College of Chiropractic
P.O. Box 1452
Spartanburg, S.C. 29304
USA
References
1. Mirtz TA, Morgan L, Wyatt LH, Greene L. An epidemiological examination of the subluxation construct using Hill's criteria of causation. Chiropractic and Osteopathy 2009 Dec 2; 17:13.
2. Hill AB. The environment and disease: association or causation? Proceedings of the Royal Society of Medicine 1965; 58:295-300.
3. Doll R. Sir Austin Bradford Hill and the progress of medical science. British Medical Journal 1992; 305:1521-1526.
4. McDonald WP, Durkin KF, Pfefer M. How chiropractors think and practice. The survey of North American chiropractors. Seminars in Integrative Medicine 2004; 2(3):92-98.
5. Alcantara J, Plaugher G, Van Wyngarden DL. Chiropractic care of a patient with vertebral subluxation and Bell's palsy. Journal of Manipulative and Physiological Therapeutics 2003; 26(4):253.
6. Kessinger RC, Boneva DV. Vertigo, tinnitus, and hearing loss in the geriatric patient. Journal of Manipulative and Physiological Therapeutics 2000; 23(5):352-62.
7. Alcantara J, Heschong R, Plaugher G, Alcantara J. Chiropractic management of a patient with subluxations, low back pain and epileptic seizures. Journal of Manipulative and Physiological Therapeutics 1998; 21(6):410-8.
8. Elster E. Upper cervical chiropractic care for a patient with chronic migraine headaches with an appendix summarizing an additional 100 headache cases. Journal of Vertebral Subluxation Research 2003:1-10.
9. Alcantara J, Steiner DM, Plaugher G, Alcantara J. Chiropractic management of a patient with myasthenia gravis and vertebral subluxations. Journal of Manipulative and Physiological Therapeutics 1999; 22(5):333-40.
10. Pistolese RA. Epilepsy and seizure disorders: a review of literature relative to chiropractic care of children. Journal of Manipulative and Physiological Therapeutics 2001; 24(3):199-205.
11. Echeveste A. Chiropractic Care in a Nine Year Old Female with Vertebral Subluxations, Diabetes & Hypothyroidism. Journal of Vertebral Subluxation Research 2008 (Jun 9):1-5.
12. Di Duro JO. Improvement in hearing after chiropractic care: a case series. Chiropractic and Osteopathy 2006; 14:2.
13. Plaugher G, Long CR, Alcantra J, Silveus AD, Wood H, Lotun K, Menke JM, Meeker WC, Rowe SH. Practice-based randomized controlled-comparison clinical trial of chiropractic adjustments and brief massage treatment at sites of subluxation in subjects with essential hypertension: Pilot study. Journal of Manipulative and Physiological Therapeutics 2002; 25(4): 221-239.
14. Bedell L. Successful care of a young female with ADD/ADHD & vertebral subluxation: A Case Study. Journal of Vertebral Subluxation Research 2008 (Jun 23):1-7.
15. Dishman R. Review of the literature supporting a scientific basis for the chiropractic subluxation complex. Journal of Manipulative and Physiological Therapeutics 1985; 8(3):163-174).
16. Marino MJ, Langrell PM. A longitudinal assessment of chiropractic care using a survey of self-rated health wellness & quality of life: A preliminary study. Journal of Vertebral Subluxation Research 1999; 3(2):1-9.
17. Sato A, Swenson RS. Sympathetic nervous system response to mechanical stress of the spinal column in rats. Journal of Manipulative Physiological Therapeutics 1984; 7(3):141-7.
18. Bolton PS. Reflex effects of subluxation: the peripheral nervous system. Journal of Manipulative Physiological Therapeutics 2000; 23(2): 101-103.
19. Budgell BS. Reflex effects of subluxation: the autonomic nervous system. Journal of Manipulative Physiological Therapeutics 2000; 23(2): 104-106.
20. Hartung J, Cottrell JE, Giffin JP. Absence of evidence is not evidence of absence. Anesthesiology 1983; 58:298-300.
21. Altman DG, Bland JM. Absence of evidence is not evidence of absence. British Medical Journal 1995; 311:485.
Competing interests
None declared
Subluxation, evidence-based medicine and epidemiology. Response to comments made by Drs. Demetrious and Hart
7 January 2010
We wish to thank Drs. James Demetrious and John Hart for their thoughtful Letters to the Editor concerning our recent paper “An epidemiological examination of the subluxation construct using Hill’s criteria of causation”[1].
Dr. Demetrious referred us to the paper by Phillips and Goodman entitled, “The missed lessons of Sir Austin Bradford Hill" [2]. We wish to point out that we specifically used the Phillips reference in our paper under the subheading “Limitations to utilizing Hill's Criteria” (Ref #32). Notwithstanding, Phillips and Goodman’s [2] concerns about “statistical significance” and “precision” are irrelevant in the case of subluxation because we simply have no credible data upon which to perform measures of “statistical significance” or “precision”. In our paper we readily agreed with Phillips and Goodman [2] that belief in “. . . a causal relationship is not sufficient to suggest action should be taken.” Something more than mere belief is needed. Unfortunately, in the case of subluxation, chiropractic has not much more than belief to offer. Furthermore, Phillips and Goodman [2] also noted that “Association does not prove causation (other evidence must be considered)”. We also wish to point out that merely discussing subluxation from anecdotal experience and case studies does not mean that a subluxation was actually encountered.
In essence we believe Dr. Demetrious is pointing to Phillips and Goodman’s [2] specific statement: Regulators often fail to act because we have not yet statistically "proven" an association between an exposure and a disease, even when there is enough evidence to strongly suspect a causal relationship.
Granted, our paper does not delve into or consider health policy formulation. But the fact remains that non-chiropractic policy regulators will eventually make decisions about subluxation based upon the best available scientific evidence. After 114 years of chiropractors making claims about the significance of subluxation as a causal factor for sub-optimal health and disease formation there has not been produced sufficient evidence to substantiate such bold claims.
The extant evidence is insufficient to strongly suspect a causal relationship between subluxation and disease and consequently to even go further into the realm of statistical significance seems unnecessary. In other words, the latter portion of the Phillips and Goodman [2] statement has not been met by the chiropractic profession.
We predict that our review will produce fear and apprehension by chiropractors. We also believe that chiropractors who are disenchanted with our findings will be calling upon Phillips and Goodman’s [2] work as “evidence” that there is a subluxation cause and effect association.
Dr. Hart believes that we somehow overlooked literature that would qualify for some of Hill’s criteria. Dr. Hart would like us to believe that the results of a survey of chiropractors (who believe in the subluxation construct) is sufficient evidence to conclude that subluxation can meet the consistency criteria. We respectfully refer Dr. Hart to our paper [1] that stated: For the chiropractic subluxation to meet these criteria it (subluxation) would have to be found repeatedly in different persons, places, times, and circumstances. In the case of a clinical condition, the subluxation would have to be consistently found with the clinical condition. To date there has not been a study that has found the subluxation in any one population (gender, race, ethnicity, age).
The study that Dr. Hart refers to [3] does not satisfy that there is a positive health outcome consistent with any variable such as gender, race, ethnicity or age. Thus the study [3] that Dr. Hart alludes to does not qualify as meeting the consistency criteria.
Dr. Hart also believes that given the literature on patients who report improvement after, not before, adjustment of subluxation that the criterion of temporality would seem to be satisfied. Dr. Hart cites references he believes meet the temporality criterion. For temporality to be met the subluxation must always precede the clinical condition for a true cause and effect scenario to take place. For example, Dr. Hart lists studies that are suggestive that subluxation is found in Bell's palsy, myasthenia gravis vertigo and tinnitus, diabetes, epilepsy and ADHD along with others from his list of references. These studies did not find the subluxation as causal of these clinical conditions. There are other pathophysiological processes that can easily be explanatory. These conditions have other, more scientifically-derived, etiologies.
It is worth noting that most manual medicine practitioners could deliver spinal manipulation to such a case without having to acknowledge that a subluxation was present or not. We find it interesting that only some chiropractors can find a subluxation associated with such pathological states whereas other chiropractors and health professionals do not. Furthermore, what Dr. Hart has provided are merely case studies which in the evidence hierarchy sits low on the spectrum of evidence. Case studies are merely capable of generating an hypothesis and do not prove causation or cure.
Dr. Hart believes that the subluxation model adequately satisfies the biological plausibility criterion. The biological plausibility criterion asks the question “does a pathophysiologic model of how the exposure could cause the disease make sense?” [1] In other words, does the subluxation as a pathophysiologic model of having a subluxation being a causal factor of disease make sense? We suggest that it does not make sense. Nansel and Szlazak [4] noted: it is extremely important to keep in mind that all of the "somato-visceral disease" theories and models put forth over the years, regardless of their lack of biological tenability, have also suffered from a common central premise, that is, that the patients involved in these rather "miraculous" clinical situations were really suffering from true visceral disease in the first place!
Nansel and Szlazak [4] noted: we are aware of not a single appropriately controlled study that has convincingly established that spinal manipulation represents a valid curative strategy for the treatment of any true visceral disease, even though scientifically unsubstantiated claims of such therapeutic efficacy continue to be all too prevalent throughout the chiropractic profession.
After 14 years since this seminal paper was published, we do not know of any study that has established spinal manipulation as a valid curative strategy. We do know that unsubstantiated claims of therapeutic efficacy continue to plague the chiropractic profession. It is our opinion that the ACC Paradigm [5] still lends itself to such claims of therapeutic efficacy in their own definition of a subluxation.
Furthermore, we believe that the non-biological plausibility of the subluxation, seen in the ACC Paradigm, is further explained by Nansel and Slazek [4]. They suggested that: there is not the slightest suggestion that patients suffering from severe, primary, mechanical low back pain, for instance, are more prone to develop higher incidences of prostate or testicular carcinoma, colitis, ovarian cysts, endometriosis, pancreatitis, appendicitis, diabetes mellitus or any other category of regionally or segmentally related organ disease.
We believe that this explanation alone is suggestive of the folly of the subluxation as a biologically plausible explanation as described by the ACC Paradigm [5]. Thus, the biological plausibility is unfounded. What Dr. Hart has brought forward are individual aspects (the five components of the subluxation i.e. kinesiopathology, neuropathology, etc) and suggests that each of these are somehow biologically plausible. By themselves, we agree that they have a level of biological plausibility. However, for a subluxation to be a true entity it should consist of all five components. And this is where the model, in our opinion, falls apart. There simply is no evidence whatsoever suggestive of this subluxation construct. In addition, the mentioning of the five components of subluxation yet detailing only part of the components does not make a subluxation. In summary, the notional entity known as subluxation (for it to be a subluxation) should have all the five components available. Furthermore, such an entity would have to meet cause and effect criteria to be a putative clinical entity worthy of intervention. Our review found no evidence of this.
Dr. Hart laments that we missed an opportunity to point out what it would take to adequately satisfy the criteria of causation. The purpose of this examination was to review the current evidence on the epidemiology of the subluxation construct and to evaluate the subluxation by applying epidemiologic criteria for its significance as a causal factor [1]. Thus our purpose was not in research design or methodology of examining the subluxation. We leave it to the subluxation advocates to address this.
As well, we must point out that we did not intentionally avoid the EBM principles in our paper. The purpose of the paper was to examine the subluxation construct using criteria of causation i.e. Hill’s Criteria. Dr. Demetrious should know that the EBM paradigm was developed by epidemiologists. A thorough reading of Sackett’s work [6] specifically notes the value of epidemiological principles.
However, Dr. Demetrious correctly noted the thoughts by Sackett et al [6], namely:
• Evidence based medicine is the conscientious, explicit, and judicious use of current best evidence.
• The practice of evidence based medicine means integrating individual clinical expertise with the best available external clinical evidence.
• Evidence based medicine is not restricted to randomised trials and meta-analyses. It involves tracking down the best external evidence.
We emphatically agree with these views and believe we are quite familiar with the EBM paradigm. Nonetheless, we specifically point out that every single one of these points involves the use of actual evidence. The whole focus of our paper was to examine the evidence and report the findings. These findings demonstrate an absence of any coherent, credible, objective evidence that will support the subluxation construct as it relates to the ACC Paradigm [5]. Simply put, the evidence is simply not there.
It is true that we concluded that the subluxation construct has no valid clinical applicability as Dr. Hart asserts. However, Dr. Hart suggests that we failed to provide hard data to support such a conclusion. We stand by our conclusion based on the lack of findings in the literature. If the subluxation was a valid clinical entity the literature would bear this out. Thus the only conclusion one can draw is that subluxation is a suspect clinical entity.
As well, Drs. Hart and Demetrious have suggested that we have ignored the axiom that absence of evidence is not necessarily evidence of absence. We believe that this comment has been over-utilized by chiropractors to the point of being cringe-worthy. We also believe it is a shield to cover the chiropractic profession and is used as a measure of our collective lack of evidence. Our paper, although preliminary, is illustrative of the “proof of absence.” The burden of proof rests with the chiropractic profession.
We wish to leave this argument with a quote from Charles Darwin that we feel is appropriate to the subluxation debate: “Ignorance more frequently begets confidence than does knowledge.”
Again, we wish to thank Drs. Hart and Demetrious for taking the time to critique of our work and we look forward to seeing new credible research that explores the theoretical construct that is subluxation.
Timothy Mirtz DC, PhD, CHES, CAPE
Lon Morgan DC, DABCO
Larry Wyatt DC, DACBR
Leon Greene PhD
References
[1] Mirtz TA, Morgan L, Wyatt LH, Greene L. An epidemiological examination of the subluxation construct using Hill's criteria of causation. Chiropractic and Osteopathy 2009; 17:13.
[2] Phillips CV, Goodman KJ. The mixed lessons of Sir Austin Bradford Hill. Epidemiol Perspect Innov 2004;1:1-5.
[3] McDonald WP, Durkin KF, Pfefer M. How chiropractors think and practice. The survey of North American chiropractors. Seminars in Integrative Medicine 2004; 2(3):92-98.
[4] Nansel D, Szlazak M. Somatic dysfunction and the phenomenon of visceral disease simulation: a probable explanation for the apparent effectiveness of somatic therapy in patients presumed to be suffering from true visceral disease. J Manipulative Physiol Ther. 1995;18(6):379-97.
[5] Association of Chiropractic Colleges. A position paper on chiropractic. J Manipulative Physiol Ther 1996;19:634-637.
[6] Sackett, DL. Straus SD, Richardson WS, Rosenberg W, Haynes RB. Evidence-based Medicine: How to Practice and Teach EBM. 2nd Edition. 2000. Churchill-Livingstone. Edinburgh.
Competing interests
The authors declare no competing interests.
A Criticism of an Epidemiological Examination of the Subluxation Construct using Hill’s Criteria of Causation: Limitations, Suspect Conclusions and an Opportunity Missed
6 May 2010
As a chiropractic practitioner and educator over the past three decades I have been privileged to share the science, art and philosophy of the profession with thousands of patients, students and field doctors in both the United States and Europe. So it was with great interest that I read the work of Mirtz et al concerning the subluxation construct (SC) [1]. Indeed, their epidemiological examination of the SC utilizing Hill’s criteria was an opportunity to consider an important perspective regarding some of the evidence pertaining to it. It was also an opportunity to positively affect the evolution of the profession by buttressing the calls some academics have made to improve the SC, especially as it pertains to clinical practice [2,3]. Upon reflection however, it became apparent there were a number of critical shortcomings made by Mirtz and co-authors that rendered their final conclusions suspect, if not invalid. Specifically, the conclusions that the SC is “in the realm of unsupported speculation” and has “no valid clinical applicability” are not simply flawed, but in my view reckless and harmful. This may have moved the profession further away from coming to a valid, respected and unified position in regards to these matters; in essence a golden opportunity was missed. The purpose of this comment is to address the most important shortcomings of their article, identify information worthy of further consideration and make suggestions that would advance the understanding of the SC as reflected in contemporary chiropractic education and practice.
The first and most serious shortcoming involves a fundamental misuse of the work of Sir Austin Bradford Hill and the criteria he proposed to examine claims of causation between some agent or event and subsequent disease. Bradford Hill’s work has been chronicled by Yoshioka [4] and is illuminating to read. It begins in 1937 with a series of articles in The Lancet regarding the design of clinical trials (with a focus on randomization) and these eventually became the basis for his textbook on medical statistics. The story continues in the aftermath of WW II when tuberculosis was common and deadly and pharmacological interventions were being sought. The antibiotic streptomycin had recently been developed (1943) and because of its success in guinea pigs human trials followed. In 1946 a successful clinical study in England was performed using the new drug and this trial had the unique feature of including a randomly allocated control group as Bradford Hill had advocated. Over the next 20 years Sir Austin organized his thoughts regarding claims of causation primarily as they related to environmental exposures to toxins in the workplace. This culminated in his highly informative and entertaining address to the newly founded Section of Occupational Medicine of the Royal Society of Medicine [5] and gives a powerful depiction of the knowledge and attitudes of the man. His concern was focused on interpreting the observational evidence of the day, especially in the absence of more in-depth clinical research. But as important were the warnings he gave to those who would misuse his work, which is particularly relevant here:
"What I do not believe – and this has been suggested – is that we can usefully lay down some hard-and-fast rules of evidence that must be obeyed before we accept cause and effect. None of my nine viewpoints can bring indisputable evidence for or against the cause-and-effect hypothesis and none can be required as a sine qua non [5]."
It is clear from the preceding that Sir Austin did not believe that examination of any evidence by his criteria was the only means of determining the validity of claims of causation in a disease process. In fact that role is played by a well constructed randomized clinical trial (RCT) [6]. Currently it is suggested that Hill’s criteria are actually best utilized as an educated guess when observational studies or other data have been collected and are assessed. This is because Hill’s criteria have come under intense debate given the flaws inherent in their utilization, which begins with problems encountered in even defining the criteria themselves. For example, all of the criteria have been observed to be ambiguous, vague and/or have the potential to create any number of logical fallacies [7,8]. Instead, as Ward proposes, Hill’s criteria are best utilized as inferences of best explanation. Under this model the practitioner is warned of the flaws inherent in strictly applying Hill’s criteria and instead utilizes them as the basis for insight and further scientific investigation [6]. I would suggest that this is essentially where Mirtz and co-authors have gone astray. Their strict application of Hill’s criteria in regards to reviewing the literature is directly contrary to what Sir Austin advised, and given the shortcomings inherent in the criteria, it is also contrary to the current best use of his criteria.
The next major shortcoming involves the primary assumption the authors make when they state that the purpose of their paper involved “how the concept of subluxation is currently embraced by the chiropractic profession.” I submit that to truly understand the depth and breadth of the subluxation construct as currently embraced by the profession one must begin with a thorough reading of the current editions of the most evidence-based textbooks used in contemporary chiropractic education. The following is a short list of the texts that I believe best represent the subluxation construct as it currently exists in the profession (author or editor and year of publication included): Principles and Practice of Chiropractic (Haldeman, 2005) [9], The Chiropractic Theories: A Textbook of Scientific Research (Leach, 2004) [10], Chiropractic Technique: Principles and Procedures (Peterson and Bergmann, 2002) [11], Foundations of Chiropractic: Subluxation (Gatterman, 2005) [12], and Technique Systems in Chiropractic (Cooperstein and Gleberzon, 2004) [13].
If one were to read these texts it would become very clear that the current state of the chiropractic profession in regards to the SC is not accurately depicted in the paper by Mirtz et al. In essence the authors focused on a very narrow element of the construct, namely the subluxation as a cause of a visceral disease. In reality the current model of the SC has as its focus the concept often described to patients as the “painful sticky joint.” This is identified in Peterson and Bergmann’s Chiropractic Technique as “joint subluxation/dysfunction syndrome” and is associated with local pain, tissue hypersensitivity, decreased joint movement and other local findings [11]. This definition of subluxation is the foundation of their book, a text that has been adopted by no less than 10 of the current chiropractic colleges in the US and many of the programs outside of the States (personal communication, K White, Senior Editor, Elsevier Publishing). Similarly, Leach defines the contemporary version of the SC as spinal “segmental dysfunction” and describes the lesion as having a loss of motion, local tenderness and increased tension in paraspinal muscle [10]. Curiously enough, a permutation of the SC is also identified as “spinal joint dysfunction” by one of Mirtz’s co-authors in the text Handbook of Clinical Chiropractic Care. In his book Wyatt states that “this lesion can cause focal or diffuse spine pain, radiating pain not below the elbow or knee, and/or referred pain simulating visceral disease [14].”
Furthermore, more complex musculoskeletal conditions based on regional spinal joint dysfunctions have been described by Gatterman and her co-contributors [12]. Their text provides a well evidenced clinical approach to patient care based on the SC and includes a categorization and description of various subluxation syndromes. The focus of these syndromes is clearly within the musculoskeletal system and includes cevicogenic headache, thoracic outlet syndrome associated with first rib subluxation, thoracic and costovertebral subluxation syndromes, lumbar facet subluxation syndrome, intervertebral disc syndrome, sacroiliac subluxation syndrome, coccygeal subluxation syndrome, and cevicogenic sympathetic syndrome, among others.
Therefore, as noted above, segmental dysfunction and musculoskeletal oriented subluxation syndromes are the common and well recognized modern permutations of the SC. It is also clear that this musculoskeletal focus is the basis for contemporary clinical practice, as observed by Smith and Carber [15]:
"Most chiropractors typically reported that over 75% of their clinical approach to addressing musculoskeletal or biomechanical disorders such as back pain was “subluxation-based.” Conversely, most chiropractors also reported that less than 20% of their clinical approach was “subluxation-based” for patient complaints deemed to be principally problems with circulation, digestion, or similarly “visceral” in nature."
To return to the paper by Mirtz and colleagues, even if one accepts their findings that to date there was no published epidemiological evidence for a specific subluxation-induced disease, it is obvious their conclusion that the SC “has no clinical applicability” must be rejected as a flawed over generalization given the current musculoskeletal focus of subluxation in regards to patient care. This oversight is particularly puzzling since Mirtz et al cited Smith and Carber’s paper in their article. Unfortunately the advice of Smith and Carber to move beyond the polarized polemics of the past seems to have been missed as well.
The third significant shortcoming by Mirtz et al involved the use of the ACC presidents’ definition of subluxation [16], which itself has serious limitations. In the first case this definition is outdated; in the second it is far too ambiguous to be useful as the basis for such work because it is prone to selective interpretation. Probably the observation that the definition is “beautifully vague and vaguely beautiful” is one of the best things that can be said about it [17]. This is understandable however because it was the result of consensus building and was not intended as a basis for research endeavors. To elucidate, when the position paper on chiropractic was produced by the North American college presidents in the mid 1990s this was seen by many as a remarkable outcome in a land of significant political divide. The subluxation definition was an attempt to bring unity to the profession at a time when this was (and is) sorely needed, and in doing so a definition was created that was as broad and inclusive as possible. As Leach noted, the definition was most appropriately seen as a significant step in the maturation of the profession and a move away from vitalism [10]. Keating et al [3] have identified additional problems with the presidents’ definition, but suffice it to say that as written the definition could encompass virtually all forms of clinical conditions involving a spinal motion segment. However, in the realm of contemporary chiropractic education and practice the presidents’ definition is best interpreted as follows: the spine and pelvis are considered in regards to functional, structural and/or pathoanatomical changes to the intervertebral disc, zygapophyseal, uncovertebral, atlantooccipital, atlantoaxial, atlantoodontal, sacroiliac, sacrococcygial and symphysis pubis articulations and the neurological reactions associated with those changes, the most common of which is nociception. However the representation of the presidents’ definition of subluxation by Mirtz and colleagues is far from this. By choosing to focus on the most tenuous element of the definition (i.e. subluxation as a cause of visceral disease) they have developed a straw man argument in the guise of a questionable narrative literature review. In actuality what the authors have shown is that the presidents’ definition has shortcomings that are easily exposed under academic scrutiny. But in no way can one extend their conclusions to all elements of the SC because these were not thoroughly defined, investigated or reported on, which leads to the next major shortcoming.
A fatal shortcoming of Mirtz et al involved the methods utilized in the literature review itself. Before conclusions can be made regarding whether the SC has clinical applicability a properly performed systematic review would have to be done [18,19]. At the very least this would require actually evaluating the quality of the studies pertaining to Hill’s criteria, which would begin with studies in which both aspects of interest were measured (i.e. the subluxation and some type of disease). Additionally, it would also involve obtaining and assessing the quality of any study in which an association was evaluated between any one of the aspects included in the definition of the SC and any health condition, including those studies which had not addressed Hill’s criteria specifically. The review offered by Mirtz et al clearly does not rise to these standards, and if fact, even minimally accepted standards regarding published literature reviews were not met. Nowhere in their paper is there a description of the total number of “hits” the search terms returned (either in isolation or combination), the effect the inclusion and exclusion criteria had on these hits, or the final tallies of the papers that were included or rejected in the application of these criteria. Reporting this information is common procedure when publishing the results of a literature review [19]. Without it the reader is not able to reproduce the work, consider the quality of the search or assess any biases. Additionally, it is also reasonable to assume that given the contentious nature of the word subluxation contemporary authors (including those outside of chiropractic) are using different terms such as “segmental dysfunction” or “spinal joint dysfunction” to describe the subluxation, which were terms not included in the Mirtz et al literature search. Ultimately it is not possible to accept at face value the result that only four peer-reviewed journal articles exist and were able to be examined per Hill’s criteria. But even if it was accepted (as other authors have noted) that there is a paucity of epidemiological investigations regarding the SC [20,21], then the observation that the subluxation fared poorly in regards to Hill’s criteria is best explained by the fact that the investigations simply have not been done and/or the research investigations haven’t been published. Ultimately the conclusion by Mirtz et al that the subluxation construct is “in the realm of unsupported speculation” cannot be made until it is supported by the findings of a comprehensive and properly performed systematic review and even then any conclusion would have to placed into context relative to the number of high quality studies that have actually been performed; without it their assertion is meaningless if not misleading.
This leaves the last major shortcoming of the work, which is tied directly to the highly evocative nature of the debate involving the subluxation. As stated above, I am of the opinion that the conclusions of the authors are not just flawed, but are harmful. This is because inflammatory conclusions only serve to strengthen the resolve of those who embrace the most speculative aspects of the SC and/or those who view subluxation as their raison d'être and practice within a narrow scope as described by McDonald [22]. Such conclusions make the article prone to being discarded as just another “subluxation bashing” paper designed to humiliate and eliminate narrow scope practitioners. But isn’t this the group that many of us are hoping to influence the most? Is this the best way to encourage a cultural change, especially when considering the number of chiropractors with more moderate views (i.e. the “middle scope practitioners” [15, 22]) who hold a contemporary understanding of the SC and would reject the Mirtz paper on similar grounds?
What makes the conclusions of Mirtz and colleagues particularly reckless however is the reality that journal articles (and their shortcomings) are so quickly and broadly disseminated. Articles in the Journal of Chiropractic and Osteopathy become included in the most important science and health care data bases that exist, such as MEDLINE as accessed through PubMed. It is very clear that perceptions of the chiropractic profession by the public (including current and potential patients, litigants, healthcare policy makers and other healthcare providers) can be directly impacted by our publications. Once published, these papers provide ammunition to chiropractic adversaries at a time when the profession can least enjoy it. I believe there are important lessons to be learned by all parties involved in chiropractic journal publications, and this includes not only authors but also peer-reviewers and journal editors. We are the stewards of this important source of information and we all need to act in a responsible fashion.
The debate regarding the various elements of the SC is obviously important for our patients and our profession. As noted above the majority of patients enter chiropractic offices with musculoskeletal complaints and often this is thought to be associated with some type of painful joint dysfunction. Some patients have also reported success with non-musculoskeletal conditions [23,24] and new patients come to our offices with the hope that they will experience those same benefits. It is clear that there is a lack of published research in this domain and this has been thoughtfully presented by Hass et al as an outcome of the most recent Chiropractic Research Agenda initiative [21]. A contemporary perspective in regards to visceral conditions and the subluxation has also been described by Budgell in which he differentiates between subluxation as a cause of a specific disease (not very likely) and subluxation as a component of functional visceral disorders by virtue of somatoautonomic or other neurophysiological mechanisms (more likely) [12]. Comprehensive reviews of the evidence concerning chiropractic care for non-musculoskeletal conditions by Leach [10] and chapters by Vernon and Sarnat and Budgell [9] provide an excellent contemporary education in this area. Vernon in particular offers an important algorithm for care when patients present with visceral signs and symptoms. Additionally, the work of Hawk et al has shifted the paradigm of chiropractic care for non-musculoskeletal conditions into one focusing on whole system research, which might be more appropriate in some cases [25]. Her work as well as those of others regarding all aspects of chiropractic care has been the focus of the Council on Chiropractic Guidelines and Practice Parameters (CCGPP) and their literature syntheses are important, must read publications [26]. Interestingly, one task yet to be completed by the CCGPP involves a chapter on subluxation, which if written with the same due diligence as the other chapters, should become an excellent resource for the profession.
Finally, I would also submit that segmental dysfunction as a cause of non-musculoskeletal disorders due to reactions within the nervous system are far from having no evidence, much less no clinical applicability. For example, the contemporary version of the subluxation construct includes the well established cauda equina syndrome as a result of severe intervertebral disc disruption, among other things [12]. Additionally, numerous non-musculoskeletal case studies exist as noted by Leach [10] and Sarnat and Budgell [9], and while case studies are one of the weakest forms of clinical evidence, they are evidence nonetheless. Of course causality cannot be determined by case studies, but descriptions of patients who obtained a significant benefit (or harm, as the case may be) are worthy of clinical consideration and further research, and should not be ignored. Also, by maintaining a continually evolving SC as a core component of clinical education and practice the chiropractic profession retains its unique perspective, meanwhile establishing a profession which offers high quality patient care based on the best available evidence. The SC provides an environment of inquiry so that researchers are able to pursue alternative hypotheses in regards to non-musculoskeletal clinical presentations, such as the effect adjusting upper cervical subluxation has on blood pressure [27] or on neck-tongue syndrome [28]. It also creates a model from which to understand mimicry conditions such as pseudo-angina associated with thoracic region segmental dysfunction [29,30].
In my opinion though, what is particularly ripe for investigation are the hypothesized somatoautonomic reflex phenomena associated with the SC. Just as the profession initially focused its research efforts on our most commonly observed musculoskeletal successes (low back pain, neck pain and headache), it now seems prudent to focus some of our resources on the most common non-musculoskeletal presentations. I would offer my clinical observations (and unfortunate experiences as a patient) regarding severe lumbar spinal pain and dysfunction and associated transient constipation as an ideal place to start. It would seem that of all the likely candidates from which to establish a painful joint dysfunction as a cause of visceral dysfunction, this presumed sympathetic nervous system reaction sits at the top the list given its frequency and temporality. But of course, in order for this research to proceed the criteria often identified on television police dramas must first be grappled with: means, motivation and opportunity. I believe we have researchers with enough motivation, but is the profession ready to provide the means and opportunity…or is it going to continue to live in the world of poorly evidenced hypotheses and let the vocal minorities at the extremes of our profession run (or ruin) the debate?
Despite the shortcomings of Mirtz et al’s paper, the examination of the SC in regards to Hill’s criteria is still important because it provides a framework for understanding the most important issues regarding claims of causation and it identifies areas in need of epidemiological research. It also highlights the shortcomings of the ACC presidents’ definition of subluxation and a carefully crafted revision of it appears to be warranted. Lastly, given the continued improvement in chiropractic education and the profession’s textbooks, a chasm has emerged between a contemporary understanding of the subluxation construct and historical notions held by some. Instead of denigrating those beliefs in our journal publications, a concerted effort must be made to continually update our colleagues so that we are able to offer the best casting of our valued profession to our patients and society at large.
Christopher Good DC, MA(Ed)
Professor of Clinical Sciences
University of Bridgeport College of Chiropractic
References
[1] Mirtz TA, Morgan L, Wyatt LH, Greene, L: An Epidemiological Examination of the Subluxation Construct using Hill’s Criteria of Causation. Chiro & Osteo 2009, 17(13).
[2] Good, C: Subluxation Syndromes: A Condition Whose Time Has Come? J of Chiropr Hum, 2004; 11:38-43.
[3] Keating JC, Carlton KH, Grod JP, Perle SM, Sikorski S, Winterstein JF. Subluxation: dogma or science? Chiro & Osteo 2005, 13: 17.
[4] Yoshioka, A. Use of randomization in the Medical Research Council’s clinical trial of streptomycin in pulomonay tuberculosis in the 1940s. BMJ 1998, 317: 1220-3.
[5] Hill AB. The environment and disease: association or causation? Proc R Soc Med 1965, 58: 295-300.
[6] Ward AC. The role of causal criteria in causal inferences: Bradford Hill’s “aspects of association.” Epidemiologic Perspectives & Innovations 2009, 6: 2.
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Competing interests
None
Subluxation epidemiology: a response to Dr. Good
10 May 2010
We wish to thank Dr. Good for his response to our recent work that was published in the December issue of Chiropractic & Osteopathy. In attempting to sift through the lengthy comment provided by Dr. Good we have chosen to only address the key points he makes.
We do not believe that the conclusion of the subluxation construct (SC) having “no valid clinical applicability” is flawed. Nor is it reckless and/or harmful. Simply put, if there is little or no data providing evidence of the SC combined with and the claim chiropractors make to treat this putative entity as a causal agent then its validity should be considered unproven. Until data comes forth that can adequately demonstrate the existence of the SC and provide the necessary data that demonstrates that it is a causative agent in disease or ill health then the SC should be regarded as having no such valid utility. One cannot say that some thing is causative for disease in the hope that someday science will somehow and some way catch up with it. We find this wholly unacceptable of any group of health practitioners to make such statements. It is not enough to accept the SC because a profession has historically “hitched its wagon” to a suspect entity.
Our intent, in writing the paper, was not in hope of unifying the profession or tearing it asunder. It was, however, an exercise in attempting to search the literature and apply the criteria of causation generally accepted by the epidemiological community. We are perplexed by Dr. Good’s assertion that our paper may have moved the profession further away from coming to a valid and respected unified position. In fact, the definition that we utilized was the ACC Paradigm which has been accepted by most, if not all, of the leading chiropractic organizations. It appears that the ACC Paradigm on subluxation is the unifying definition. For this reason we believe that using various definitions from various authors of chiropractic textbooks would have been problematic. It is worthy of note that none of the definitions in the works cited by Dr. Good provide any data that can attest to the SC being a causative agent in disease.
Dr. Good claims that the ACC Paradigm is outdated and ambiguous. We wholeheartedly agree with this assessment. We nonetheless disagree with the assessment that the ACC Paradigm is somehow “beautifully ambiguous.” We also suggest that the textbook authors various opinions on a SC definition are just as vague and ambiguous and lack the rigor of any substantive supportive scientific data.
It is not surprising to see Dr. Good (and possibly others) go directly to Sir Austin and examine his feelings on his very own work. It is true that Sir Austin did not intend for his criteria to be hard and fast rules. However, epidemiologists still refer to them and hold these criteria as foundational to the workings of epidemiology. In our work, we believed it was important to use his tenets to begin the investigation of the epidemiology of the SC. The use of the criteria provides a starting point for this investigation. In our investigation, we found no evidence to support the SC or an epidemiology for causation. Unless Dr. Good or any other person has solid evidence to support that the SC is causative we remain firm in our findings and our conclusions.
We do take issue with Dr. Good in his suggestion that we focused on a narrow element of the construct. As explained previously we utilized the ACC Paradigm which has been accepted by many leading organizations in the chiropractic profession. As well, Dr. Good alludes to the fact that there is a “joint subluxation/dysfunction syndrome.” This syndrome has never been documented to actually exist as a functional diagnosis nor does it have any evidence supporting it in relation to any known disease process. As per the consideration that the SC is somehow a “permutation” is nothing more than an attempt to offer some sort of validation to a construct that has not been scientifically validated. As well, the reference that 75% of chiropractors consider their clinical approach to be “subluxation-based” does not make the SC a reality or that there is sufficient research evidence suggestive that the SC is a causative agent. This is a common logical fallacy called the fallacy of consensus gentium (i.e. arguing that an idea is true on the basis that the majority of the people believe it.) Definitions that are commonly accepted for the subluxation have often been political in nature and cannot be used as testable models. Thus, a political definition such as put forward for the SC offers a difficult investigation using an epidemiological protocol.
Dr. Good noted our methodology. It is true that a systematic review would have included the number of “hits” in the search results and document inclusion and exclusion criteria. Nevertheless, using a very broad search strategy we were hard pressed to find any literature to support the SC that matched the definitions of the causation criteria. Furthermore, Dr. Good believes that other researchers are using terms such as “segmental dysfunction” and/or “spinal joint dysfunction” to describe the SC. To date, we are unaware of any serious research that describes “segmental dysfunction” and/or “spinal joint dysfunction” as causative of disease.
We take issue with Dr. Good when he stated that: “Ultimately the conclusion by Mirtz et al that the subluxation construct is in the realm of unsupported speculation cannot be made until it is supported by the findings of a comprehensive and properly performed systematic review and even then any conclusion would have to placed into context relative to the number of high quality studies that have actually been performed; without it their assertion is meaningless if not misleading.” We believe that the conclusion that the SC is in the realm of unsupported speculation due to the fact that there are no high quality studies that have validated the SC as causative. If Dr. Good has a number of high quality studies that leaves no doubt to the existence of the SC and these high quality studies scientifically verify that the SC is causative of disease then our opinion can be amended.
As stated previously, our intent, in writing the paper, was not in hope of unifying the profession or tearing it asunder. Nor was it intended to “bash” the profession or alienate or humiliate certain practitioners. Also, our intent in writing this paper was not to influence the general public or provide ammunition to chiropractic adversaries. We disagree vehemently with Dr. Good that researchers are somehow obligated to make sure that their research does not have political implications that could be construed as “costly.” We find the comments by Dr. Good in this regard to be very troubling.
In closing, we appreciate Dr. Good’s comments of our work. While there is little doubt that we are in disagreement with many of his responses, we suggest to Dr. Good that he provide the necessary data to support the existence of the SC that is testable, reproducible, and that there are screening measures that are valid to assess the SC. And when this is accomplished we suggest the next step would be to provide the necessary data, using the criteria of causation, in making the determination that this SC is a causative agent in disease. If this is achieved it falls to well supported chiropractic researchers to assess whether the act of spinal manipulation is a curative strategy. To date, none of these steps have been adequately fulfilled. This leaves us with no other conclusion than to suggest that the SC is a theoretical construct and at this time has only speculative clinical applicability.
Timothy A. Mirtz DC, PhD
Lon Morgan DC, DACBR
Lawrence Wyatt DC, DACBR
Leon Greene PhD
Competing interests
No competing interests claimed.