*Based on the Martin Bass Lecture
Delivered at the Trillium Research Conference
University of Toronto, Toronto, Ontario
June 12, 1999

 Reproduced with Permission from Canadian Family Physician

In Part I I described clinical descriptive research as observing, recording, classifying, and analyzing, and expressed puzzlement at our neglect of it, given the notable contribution made by family physicians in the past. Clinical research seem s to have been replaced by survey research as the preferred method for studies in family practice.

A recent article in Family Medicine [1] showed that by far the commonest type of research done by family medicine residents at the University of British Colombia has been the cross-sectional population survey. In view of the time constraints, th is is not surprising. But I believe this is also the case in our discipline as a whole as noted by editors of the Canadian Family Physician [2]. Surveys have their place, but we cannot base a credible clinical discipline on surveys.

Besides the obvious disincentives to long-term projects, I can think of four reasons for our neglect of clinical research.

The common assumption about the generation of knowledge is that the interaction of basic and population sciences gives us knowledge of disease mechanisms, causes and therapeutic tools. These are then tested in clinical trials. Our knowledge of cardiovascular risk factors is a case in point. Laboratory science identified lipidemia as a possible risk factor, the population studies confirmed it as a risk factor and laboratory science developed cholesterol-reducing drugs, which were tested by rando mized clinical trials (RCT's). But we have missed out a crucial level of knowledge: taxonomic science. The discoveries of basic and population science have no practical value unless they have clinical significance. A clinical trial is of no value if the t arget disorder has no clinical significance. The identification and control of risk factors could not have got off the ground without a pre-existing body of knowledge of the natural history of ischemic heart disease (IHD). We are all dependent on this gre at foundation of taxonomic knowledge, most of it gathered over the last two centuries. And it is not a static foundation: it is constantly changing and evolving. The classification of IHD, for example, has evolved in our own time from one based on the ECG to one based on angiography. The laboratory and population sciences can never replace clinical descriptive science. Knowing the innervation of the heart does not tell us the distribution, duration and quality of anginal pain. Knowing the physiology of di gestion does not tell us the pattern of pain in peptic ulcer. We do not know that a biological deviation from normal is harmful unless we follow people who have the deviation over time. Medical history is full of spurious diseases shown by clinical resear ch to be harmless variants, from sinus arrhythmia and large tonsils, to mitral valve prolapse and tight perineum. The more sensitive our diagnostic technologies, more the risk of spurious "diseases", and the more need there will be for descriptive clinica l research.

There is a good example from the history of general practice of the fundamental importance of descriptive taxonomic research. Edward Jenner[3] was a country practitioner who was told by a milkmaid that she could not get smallpox because she had had co wpox. At that time epidemic smallpox had a very high mortality, but if smallpox was transmitted by inoculation to healthy children, the mortality risk was much less (10%). With parents facing this agonizing choice, Jenner saw the possibilities in the milk maid's story. He asked his colleagues to make observations on their own patients, but they did not confirm it. Instead of giving up, as a lesser scientist might have done, Jenner reasoned that what his colleagues were calling cowpox might be a heterogeneo us group of infections, only one of which provided immunity to smallpox. So he started to make detailed observations on the skin eruptions of dairy workers. He asked farmers to let him know when an outbreak occurred and would take an artist with him to dr aw the lesions. Eventually he was confident that he had an accurate description of cowpox and was ready to make his crucial experiment. Even after publication of his results, critics who were using vaccine from people wrongly identified as having cowpox, tried to discredit his research.

For logistic, economic, and ethical reasons the time span of RCT’s is limited. Ninety-nine percent of trials are for less than 3 years [4]. For chronic diseases this is too short to use significant outcome criteria or to identify the long-term effects of drugs. A by-product of short duration is the use of surrogate markers as outcomes. The early hypertension trials used heart and stroke events as outcomes, but since it is not feasible to do this for every new drug, blood pressure (BP) reduction has been used as a proxy. As recently reported, BP reduction has not proved to be a good surrogate (5). In his long term studies of patients with rheumatoid arthritis, Pincus⁴ found that the usual surrogates of joint swelling and tender ness were not good predictors of longer term outcomes.

Since trials are so short, they cannot provide much information about the long term harmful effects of drugs. The new and powerful drugs coming onto the market in increasing numbers will require long term descriptive studies. For example, between 1960 and 1980, many one-year drug trials were done on patients with rheumatoid arthritis. Several drugs were equally effective and textbooks began to give rheumatoid arthritis (Rh.A.). a good prognosis. Then, 10-year descriptive studies by Pincus (4) and colle agues told a different story (4). Most of the drugs effective over one-year, were ineffective over the longer term, or were discontinued because of adverse effects. The prognosis over 10 years was much worse than the one-year prognosis.

RCT's often use highly selected fractions of the population at risk. The elderly, those with co-morbidity and female patients are often excluded. The non-compliant, the poor, the uneducated and refusers of treatment tend not to enroll in RCT's. Even al l those who are enrolled may not be randomized. A letter in the Canadian Medical Association Journal [6] has drawn attention to the limitations of meta-analysis in this regard. In a descriptive study of one's own patients, all of them can be follow ed and there need be no dropouts.

Lack of Confidence in Our Own Ability to Add to Knowledge.

We tend to underestimate our own practice as a source of knowledge or to feel that all diseases have now been described and that our taxonomic vocabulary is a given, rather than an ever changing and evolving process: a map that is always being made and remade.

That was certainly my own feeling when I started practice. I wanted to do research towards my doctorate, but could not think of a single question arising from my practice. In the end I did a project that had nothing to do with the practice. What made m e realize the potential of my own practice as a source of new knowledge was an elderly patient who complained of disabling pain and stiffness in shoulder and hip girdles. The joints were normal except for stiffness in hips and shoulders; all investigation s were negative except for a very high ESR. The picture did not fit with anything I had seen before. I consulted an experienced internist who was puzzled too. He said "Let’s try prednisone", which had just become available. The result was an immediate and striking restoration of function. Seeking more information about this unfamiliar condition, I presented her case at the local medical society, but nobody could help me, nor did the literature. A few months later, reading an issue of The Practit ioner on rheumatology, I saw a paragraph headed "Bagratuni's Syndrome". This Italian physician had described several cases just like my patient. He called it anarthritic rheumatoid arthritis. A few months later came Barber’s [7] definitive desc ription and the suggested name "polymyalgia rheumatica". Six years later Bagratuni published a ten year follow-up of his cases, confirming the relatively benign course of the illness [8]. So I had witnessed the birth of a new disease. Of course it was not new: it was newly described and – as not unusually happens – its description coincided with the introduction of an effective remedy. A new remedy can give us a better taxonomic map. The history of Canadian medicine provides a striking example. The introd uction of insulin immediately divided diabetes into its two big categories, IDDM and NIDDM, which served us very well for almost a century. The introduction of sumatriptan for migraine could do the same for headache.

My experience with polymyalgia rheumatica showed me that original observation could be made in general practice. I started keeping notes on conditions that interested me: early symptoms of cancer, depression, brucellosis in the farming community, coron ary heart disease, infectious mononucleosis, thyroiditis. I found things that were not in the books or that were in the books, but were wrong. None of this was ground breaking: there were no "breakthroughs"; just a few small contributions to knowledge. Wa s it worth the effort? I enjoyed doing it. I didn't have to drive myself, there was the occasional joy of discovery and I learned a lot as a clinician, especially about the early stages of illness [9].

A fourth reason is the devaluation of descriptive, taxonomic research in the medical schools and in biology as a whole. It is as if a clinician cannot be a scientist unless he or she is working in a laboratory. A descriptive study may be dismis sed with that hackneyed label "anecdotal", however meticulous the observations. No wonder we have a crisis in clinical research [10].

General practice has four advantages as an environment for clinical research. First, for any disease, we see the whole range – from the mildest cases to the most severe - so we are in a position to give a fuller description than a referral clinic. Some diseases with low referral rates can only be studied in general practice. Second, because of our long term relationships with patients we can follow them for long periods and can, by using tracing strategies, obtain very complete follow-up. Third, we are in a position to add important contextual detail.

Fourth, because we see the earliest stages of illness, we can describe its whole natural history, including all the circumstances surrounding its onset. Even in such a common condition as chronic daily headache, there are no descriptions of its natural history, from its onset onwards. As John Ryle [11] wrote, "There is no disease of which a fuller or additional description does not remain to be written; there is no symptom as yet adequately explored."

Godwin has predicted dire consequences for our poor record in research [12]. Among the suggested remedies are more protected time for faculty, so that they can gain respite from the relentless demands of teaching and patient care. Although necessary fo r any physician who makes a career in grant-funded research, it is not likely to be possible for the majority of faculty members, unless residency training is transferred entirely to community practices. There is also an implicit suggestion that to do res earch one needs to withdraw from practice. Yet our great exemplars of research in family practice were clinicians who immersed themselves in practice. Clinical studies of the kind I have described are within the reach of any family physician, whether in a cademic family medicine or full-time practice. This is one kind of research which can only be done by clinicians. And it can be fun!

I thank Bette Cunningham for preparing the manuscript.

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2. Reid T. Family medicine research: Let’s play in the major leagues. CFP 1995;41:1277-1279.

3. Fisk D. Doctor Jenner of Berkeley. William Heinemann:London. 1959.

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6. Mittmann N, Liu BA, Knowles S, Shear N. Meta-analysis and adverse drug reactions. CMAJ 1999;160(7):987.

7. Barber HS. Myalgic syndrome with constitutional effects: polymyalgia rheumatica. Ann Rheum Dis 1957;16:230-237.

8. Bagratuni L. Prognosis in the anarthritic rheumatoid syndrome. BMJ. 1963;1:513-18.

9. McWhinney IR. The Early Signs of Illness. Pitman Medical Publishing Company, London, 1965.

10. Schechter AN. The Crisis in Clinical Research: Endangering the half-century National Institutes of Health Consensus. Commentaries in JAMA 1998;280(16):1440-1442.

11. Ryle J. The Physician as Naturalist. in: The Natural History of Disease. Oxford University Press:London. 1936.

12. Godwin M. Dumbing down of academic family medicine: A manifesto for change. Editorial. CFP 2000;46:1948-1950.