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Perspective |
1 Department of Radiology, State University of New York, Stony Brook, NY.
Received November 21, 2007; accepted after revision November 21, 2007.
Address correspondence to M. A. Meyers, 14 Wainscott Ln., East Setauket, NY
11733
(jimenez1234{at}optonline.net).
Keywords: medical research • peer review • scientific investigation
In the medical literature of the past century or so, there are two outstanding guides offering time less advice as to the nature of scientific investigation. The first by the ground-breaking neurobiologist Santiago Ramón y Cajal, still relevant since its original publication in 1897, covers topics from valuable personality traits to factors conducive to scientific work [1]. The second in 1979 by another Nobel laureate, Peter Medawar, is a thoughtful insight into the pitfalls and rewards of the scientific process [2].
At international meetings it's somewhat of a tradition to offer an inspirational vision about the future of radiology, emphasizing that the future is bright. We're all aware of exciting developments and applications.
Yet, in the modern field of diagnostic imaging and interventional procedures, a novice may become easily intimidated not only by an increasing technologic complexity but also by a perception that reports in the literature need to be based on multiple authorships and meta-analyses.
Both the European Society of Gastrointestinal and Abdominal Radiology (ESGAR) and the Society of Gastrointestinal Radiologists (SGR), of course, are fiercely committed to teaching and research and clinical service. The future in radiology lies in our residents and young radiologists. I believe we can profit by looking backward, not forward, for lessons learned, to understand not what but how—for any advice we might offer to a young academically inclined radiologist.
The truth is we can't predict the future, not only regarding fundamental concepts and theories, but also techniques. Not too long ago, digital subtraction angiography was considered state-of-the-art imaging and now has been supplanted by an unanticipated development called MRI. Essentially, Medawar [3] points out elsewhere:
...it is impossible to predict new ideas—the ideas people are going to have in ten years' or ten minutes' time—and we're caught in a logical paradox the moment we try to do so. For to predict an idea is to have an idea, and if we have an idea it can no longer be the subject of a prediction.
Nothing illustrates this more dramatically than the utterances of false prophets.
Hear the prediction of Yale Professor Irving Fisher just before the 1929 stock-market crash: Fisher declared that stocks had reached "what looks like a permanently high plateau." As we all know, the plateau abruptly turned into an abyss.
Economics is accepted for its dubious accuracy, but science is regarded as, well, scientific. But despite stunning breakthroughs in medicine over the past century and a half, false prophets have long trumpeted the end of scientific advances. Consider these:
The abdomen, the chest, and the brain will be forever shut from the intrusions of the wise and humane surgeon.
—Sir John Erichsen, British surgeon, later appointed Surgeon Extraordinary to Queen Victoria, 1873
X-rays will prove to be a hoax.
—Lord Kelvin, English physicist and President of the Royal Society, 1896
Everything that can be invented has been invented.
—Charles H. Duell, commissioner of the U.S. Patent Office, in a letter to President William McKinley urging him to close the office, 1899
We can surely never hope to see the craft of surgery made much more perfect than it is today. We are at the end of a chapter.
—Berkeley George Moynihan, Leeds University Medical School, 1930
The energy produced by the breaking down of the atom is a very poor kind of thing. Anyone who looks for a source of power in the transformation of the atom is talking moonshine.
—Lord Ernest Rutherford, 1933
...the great era of scientific discovery is over.... Further research may yield no more great revelations or revolutions, but only incremental, diminishing returns.
—John Horgan, science journalist [4]
Reality shows that such statements border on farce. Carl Sagan [5] has eloquently put the issue into a human dimension:
For myself, I like a universe that includes much that is unknown and, at the same time, much that is knowable. A universe in which everything is known would be static and dull.... A universe that is unknowable is no fit place for a thinking being. The ideal universe for us is one very much like the universe we inhabit. And I would guess that this is not really much of a coincidence.
Clearly, the rate of scientific advances is accelerating at a furious pace.
But how is it best to balance a mindset that's open and unbiased with a sense of what's gone before us—our historic precedents? Here, there's a sharp difference in attitude.
On the one hand, for example, Richard Feynman, Nobel laureate in physics, disdained reading journal articles or anything regarding previous achievements, so that he could approach problems with a fresh, unbiased mind. Feynman was considered the leading intuitionist of his age. But theoretic physics may not be the best standard for us to use in radiology. In contrast, there is Judah Folkman, the physician investigator at Harvard Medical School who introduced and developed the concept of angiogenesis over the past four decades. In his formative years, Folkman read all of the Nobel Prize lectures and acceptance speeches, hoping to uncover the patterns of creative thinking.
And this points out a fundamental characteristic of radiology: Not only is it a field essentially dependent on technology, but it rarely has generated the technology. Rather, the technology we are all dependent on originally arose outside of medicine:
If we review the most frequently cited articles from the radiologic literature, we'd confirm that far and away they are based more on techniques than concepts.
In radiology there is an overwhelming tendency to cite our own literature rather than more inclusively that from other disciplines—for example, gastroenterology. Nor do we often publish in or are cited by the journals of other specialties—except for a review article or, uncommonly, an interventional article. We are, sadly, too inbred.
Among widely cited radiology articles, only a small handful have dealt with concepts—that is, have used imaging to introduce or further understanding of mechanisms of human disease. Such articles are cited not only in the radiologic literature but also by a broad audience in medical and surgical journals for their clinical importance. The small number may be taken by some as a dearth of original thinking, but this is a grave mistake. Rather, it should be looked at in another way. While only a few articles dealing with conceptual perspectives are submitted and published, they can pack a wallop. Our challenge is to increase this.
Over time, the idea has taken hold that advances can come about only through what's called "Big Science": highly funded, resource-rich, supported by modern technology, in an ivory tower or an industrial complex.
Yet, what drives science is ideas, not money. Money does not buy ideas, only applications of existing ideas. Subsidized research provides developments rather than discoveries. J. J. Thomson, the British Nobel laureate in physics who built the Cavendish Laboratory at Cambridge University into the greatest research institution in the world, used to say that if government patronage of science and technology had existed in the Stone Age, we'd all have wonderful stone tools today, and no metals [6].
In his farewell address on January 17, 1961, President Dwight Eisenhower famously cautioned the nation about the influence of the "military–industrial complex," coining a phrase that became part of the political vernacular. However, in the same speech, he presciently warned that scientific and academic research might become too dependent on, and thus shaped by, government grants. He foresaw a situation in which "a government contract becomes virtually a substitute for intellectual curiosity." Many of the most essential medical discoveries came about through investigations that were driven by curiosity, creativity, and often a disregard for conventional wisdom. A concept may be abetted by technology but the foremost stimulus is the idea, the insight.
Gastrointestinal and abdominal radiology are replete with examples. Let's briefly consider three:
First, Basil Morson was a pathologist working at St. Mark's Hospital in London in the 1960s and 1970s. This was a small hospital, devoted exclusively to diseases of the colon. Often working alone, Morson established several central concepts:
We've become used to huge statistics, multi-center trials, meta-analyses. Morson's contributions testify that understanding disease processes can come from intense observations of a very limited material (Morson B, personal communication).
That carcinomas of the colon arise from polyps set the stage for screening programs and the development of colonoscopy and virtual colonoscopy.
Second, how to gain ready access to the vascular system was a challenge for many years. Sven-Ivar Seldinger was a 32-year-old radiologist at the Karolinska Institute in Stockholm when he devised the percutaneous approach to the vascular system with simple tools at hand: a needle, a guidewire, and a catheter. Seldinger explained (Seldinger S. I., personal communication):
My grandfather was a talented mechanic and constructor of tools and similar things. As a boy, I spent many days at the little factory and attained a fondness of things of the clever and cunning kind.
Neither intense training nor elaborate resources were needed—only, in Seldinger's words, "common sense." Interestingly, he couldn't obtain permission to travel to Helsinki where his paper was read by title only at the June 1952 Congress of the Northern Association of Medical Radiologists. As we know, his nine-page article published the following year is a medical milestone that has revolutionized radiology and interventional cardiology.
Seldinger's technique can be likened to William Harvey's discovery of the circulation of the blood—an explosive illumination that enabled vast advances.
Third, Barry Marshall was a 29-year-old medical resident when he revolutionized our concepts of peptic ulcer. Relatively new to gastroenterology, Marshall did not hold a set of well-entrenched beliefs. Working in Perth, Australia—about as remote as possible from the cathedrals of learning in the Western hemisphere—he established that a bacterium, Helicobacter pylori, is the underlying cause of ulcers of the stomach and duodenum, gastric cancer, and certain lymphomas of the stomach. He was unable to gather support from drug companies, which were reaping huge profits from marketing acid inhibitors (Marshall B, personal communication). It took 10 years for the dogma of acid-related and stress-related ulcerations to be overthrown and H. pylori to be accepted by the medical profession. In 2005, Marshall won the Nobel Prize.
These thoughts lead us to some considerations regarding peer review. Medicine and science have not come up with an alternative to peer review by granting agencies and journals, but its flaws must be recognized. Simply put, peer review tends to inhibit innovation. In research grant applications, it forces the researcher to work on a problem someone else thinks is important and describe the work in a way that convinces the reviewer that results will be obtained. This element of peer review thus demands conformity of thinking and tends to reinforce dogmatism. How can a venture into the unknown offer predictability of results? Who is truly the peer of a maverick, an individual who views a problem with fresh eyes? Two of the Nobel laureates in medicine, as recently as 2007, had their initial grant applications for gene targeting rejected on the grounds of unfeasibility [7].
Similarly, with scientific presentations—either at meetings or as journal articles—the true value of a contribution has been difficult to assess. Even in being scheduled at major conferences to present their findings, pioneering researchers have found that their work has not yet been appropriately judged. The presentation may be rescheduled at an embarrassingly limited venue for what would shortly be proved to be a major breakthrough.
Let us recall a few notorious examples, which happen to involve psychiatry, oncology, and gastroenterology, here [8]:
In each instance, their discoveries transformed the world.
Is it surprising that the core papers of a research front sometimes have difficulties in getting published because their original referees rejected them [9–11]?
Let me briefly highlight a few examples:
In science, prolixity and the number of co-authors may bear no relationship to the substance of a presentation. This is spectacularly illustrated by major contributions to scientific knowledge:
Wilhelm Roentgen [14] reported the discovery of X rays in 10 pages.
Albert Einstein [15] developed the special theory of relativity in 30 pages.
James Watson and Francis Crick [16] described the structure of DNA in 943 words.
Gerald Edelman [17] delineated the composition of immunoglobulins in 384 words.
Paul Lauterbur [12] presented the principles of MRI in 840 words.
So what do these past experiences teach us?
What can a young radiologist who is academically inclined learn from all this?
It is simply this: Advances may come from a single individual—often young, often working alone, often with limited resources, often not at what's considered a premier institution—who perseveres in the face of the conventional wisdom. It's the idea that counts.
Radiology will continue to thrive only when coupled with other disciplines. Medicine has been fragmented into multiple specialties, which, too often, consider themselves sovereign.
Elias Zerhouni, director of the National Institutes of Health since 2002—a radiologist—is boldly trying to break through the highly focused activities of the various institutes and is fostering interdisciplinary research teams.
The consequences of fragmentation among medical specialties are humorously illustrated in an incident related by Stephen E. Goldfinger [18], a Harvard Medical School professor of medicine. He was attending a local performance of Bruckner's Third Symphony, part of a series to which many physicians from the Boston community subscribed.
As the first movement ended, a small, elderly lady had a prolonged fainting spell. She was carried out to the lobby, where Goldfinger joined the throng of his colleagues who had followed her. Once placed on the floor, the woman fluttered her eyelids and gained consciousness. Then the questions began.
"Have you ever had a seizure?" asked a neurologist."No," she replied.
"Do you take insulin?" asked an endocrinologist. "No," she said.
"Have you ever had heart palpitations?" came from a cardiologist, and again the answer was "No."
Then it was Goldfinger's turn. Not out of shrewdness so much as the lack of any new hypothesis, he blurted out, "Well, what do you think it was?" Her eyes opened wide and her response was loud and unequivocal. "Bruckner!" she exclaimed [18].We must engage and be engaged. We seem to have forgotten Pasteur's famous dictum that there is only one science.
References
-globulin. (letter) Am
Chem Soc 1959; 81:3155
–3156[CrossRef]
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