Review
An epidemiological examination of the subluxation construct using Hill's criteria of causation
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* Corresponding author: Timothy A Mirtz timothy.mirtz@usd.edu
Chiropractic & Osteopathy 2009, 17:13 doi:10.1186/1746-1340-17-13
- Subluxation epidemiology: a response to Dr. Good
- A Criticism of an Epidemiological Examination of the Subluxation Construct using Hill’s Criteria of Causation: Limitations, Suspect Conclusions and an Opportunity Missed
- Subluxation, evidence-based medicine and epidemiology. Response to comments made by Drs. Demetrious and Hart
- Literature support for subluxation theory
- Subluxation, Hill's Criteria of Causation and EBM
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
(2010-05-06 02:38) University of Bridgeport College of Chiropractic 
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
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Competing interests
None
Subluxation, evidence-based medicine and epidemiology. Response to comments made by Drs. Demetrious and Hart
Timothy Mirtz
(2010-01-07 03:51) University of South Dakota
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.
Literature support for subluxation theory
John Hart
(2010-01-05 06:21) self
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, Hill's Criteria of Causation and EBM
James Demetrious
(2009-12-29 05:03) Private Practice
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.
Subluxation epidemiology: a response to Dr. Good
Timothy Mirtz (2010-05-10 08:25) University of South Dakota
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.
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