In November 1935 at Lisbon’s Santa Marta Hospital, Portuguese neurologist António Egas Moniz drilled into the skulls of his first twenty psychiatric patients, severing the white-matter tracts of the frontal lobes, and reported — on the basis of a few weeks of observation and no controls — that he had cured or improved most of them; the gap between that claim and the documented reality is the entire case. The reality was a procedure that, in its American form, lobotomized roughly 40,000 to 50,000 people, blunted or destroyed the personalities of a large fraction of them, killed on the order of one in twenty, and was performed most heavily on women, the institutionalized, children, and the powerless who could not consent. It was not validated against a sham, not measured against an inert comparator, not followed over the years it would have taken to see what it did; it was launched on the authority of a respected clinician working fast in a field that had nothing else to offer overcrowded asylums.
The operation did not fail quietly in a backwater. It was crowned. Moniz received the 1949 Nobel Prize in Physiology or Medicine “for his discovery of the therapeutic value of leucotomy in certain psychoses,” the only Nobel ever awarded for a surgical destruction of healthy brain tissue. That prize functioned as a regulatory and reputational green light: it converted an undertested operation into a respectable standard of care and supercharged its American evangelist, neurologist Walter Jackson Freeman II, who by the late 1960s had performed or supervised more than 3,500 lobotomies — a death toll among his own patients estimated at roughly 490.
Freeman’s signature innovation was to remove the operating room entirely. His “transorbital” or “ice-pick” lobotomy, first performed on a living patient on January 17, 1946, drove a leucotome through the thin bone of the eye socket and swept it across the frontal lobes, often in under ten minutes, frequently with no surgeon present and no general anaesthetic — he stunned patients with electroshock instead. He performed it on minors, on patients with headaches and depression, and on Rosemary Kennedy in 1941, who was left permanently incapacitated. The surrogate endpoint — a calmer, more “manageable” ward patient — was achieved. The actual endpoint — a recovered human being — usually was not.
The reckoning came not from a tribunal but from a molecule. Chlorpromazine, synthesized in 1950 and shown to control psychosis by 1952, offered the same institutional benefit — quieter, more tractable patients — without drilling through the skull. Within roughly a decade the lobotomy collapsed from a Nobel-honored frontier therapy to a byword for medical hubris. It was never recalled, never banned by a single statute; it was simply abandoned, made obsolete by a pill, and is now the textbook case of how prestige, a flattering surrogate measure, and an absence of controlled evidence can scale a mutilating procedure to tens of thousands before anyone is required to prove it works.
In 1957 surgeon J. Roderick Kitchell and colleagues at Presbyterian Hospital in Philadelphia, following an Italian lead, began tying off the internal mammary arteries in the chests of angina patients and reporting that roughly two-thirds felt better — and the gap between that reported relief and the operation’s actual physiological effect is the entire case, because the operation did almost nothing the body could measure. The procedure was supposed to relieve the crushing chest pain of coronary disease by occluding the internal mammary arteries so that blood would be diverted into the heart muscle. It was simple, it was fast, it was performed under local anaesthetic, and within two or three years it had been carried out on thousands of patients across Italy and the United States on the strength of uncontrolled before-and-after testimonials.
The reported numbers looked persuasive: in the largest case series, on the order of two-thirds to three-quarters of patients said their angina improved, many dramatically, with effects holding up over months and years of follow-up. What no one had done was ask whether the cut, rather than the ligature, was doing the work. Angina is a subjective, fluctuating symptom, and the act of being operated on by a confident surgeon is among the most powerful placebos in medicine.
The reckoning was unusually clean and unusually fast. Between 1959 and 1960 two small randomized trials — Leonard A. Cobb’s group at the University of Washington and E. Grey Dimond’s at the University of Kansas — did something no surgical evaluation had done before: they randomized angina patients to either the real ligation or a sham operation, an identical skin incision in which the arteries were exposed but left intact, with neither the patient nor the assessing physician knowing which had been done. The sham patients improved exactly as much as the ligated ones. The exercise electrocardiograms were unchanged by either operation. The benefit was real to the patients and entirely placebo in origin.
The operation was abandoned almost immediately — not banned by any agency, not litigated, but disproven and quietly dropped. Its lasting legacy is the opposite of its intended one: internal mammary artery ligation is now the founding textbook example of why surgery, like a drug, must be tested against a placebo, and of how a self-limiting subjective symptom plus an enthusiastic operator can manufacture thousands of “cures” out of nothing but expectation and a scar.
In May 1962, University of Minnesota surgical chairman Owen H. Wangensteen announced in JAMA that a duodenal ulcer could be cured without an operation by swallowing a balloon and chilling the stomach to roughly minus-10 degrees Celsius — a bloodless “physiological gastrectomy” — and within two years thousands of Americans had been frozen on refrigeration machines that had never passed a single controlled trial; the gap between that announcement and the 1969 finding that a fake freeze worked exactly as well is the entire case. Gastric freezing was not a fringe quackery. It was launched by one of the most decorated academic surgeons in the United States, published in the country’s leading medical journal, and adopted at scale before anyone tested it against a placebo.
The promise rested on a plausible mechanism and a flattering measure. Wangensteen reasoned that supercooling the gastric mucosa would knock out the acid-secreting cells that drove ulcer disease, achieving by cold what surgeons then achieved by cutting out half the stomach. Early uncontrolled series were spectacular: investigators reported that on the order of 85 percent of patients had prompt relief of pain and apparent healing of ulcer craters. That surrogate — short-term symptom relief, the most placebo-responsive endpoint in all of medicine — was mistaken for cure. The acid suppression was real but transient, returning to baseline within weeks to months, and the symptom relief was, it later emerged, almost entirely the patient’s own expectation.
The reckoning came from the design that the launch had skipped. By 1964 controlled and double-blind studies were appearing, and in July 1969 a multi-institution cooperative trial led by Julian Ruffin reported in the New England Journal of Medicine that patients given a genuine gastric freeze did no better than patients given a sham freeze in which the same balloon circulated fluid that was never chilled. The treatment effect, against a proper control, was zero. Gastric freezing collapsed almost as fast as it had spread. It was never banned and never recalled; it was abandoned — and it survives in textbooks as the canonical demonstration of why a new procedure must be tested against a sham before, not after, it is sold to thousands.
In 1894, Johns Hopkins surgeon William Stewart Halsted published the results of his “complete operation” for breast cancer — an en-bloc amputation of the breast, both pectoral muscles, and the axillary lymph nodes — and reported that it had cut local recurrence from the 51–82% rates of his European contemporaries to a fraction of that; the gap between that local-control victory and the survival it never delivered is the entire case. The radical mastectomy controlled the wound bed and was mistaken, for three-quarters of a century, for a control of the disease. It was performed on the order of nine in ten American women with breast cancer well into the 1970s, left them with a hollowed chest wall, a frozen shoulder, and near-ubiquitous arm lymphedema, and — as randomized trials would eventually show — bought not one additional day of survival over far lesser surgery.
The operation did not fail because it was crude. It was, by the standards of 1894, a genuine advance: Halsted’s en-bloc dissection and his obsession with surgical technique made him one of the founders of modern American surgery, and the early survival figures — a five-year survival roughly double that of untreated women — were real. The error was theoretical. Halsted built the operation on an anatomical hypothesis: that breast cancer spread in an orderly, centrifugal, contiguous fashion outward from the breast through the lymphatics, so that cutting wider and deeper must, by geometry, cut ahead of the disease. If the theory were true, more radical surgery would mean more cures. The theory was false.
Cancer that had spread had usually spread through the bloodstream before the surgeon ever arrived, and cancer that had not spread was cured by far less. The radical mastectomy’s mutilating margins therefore changed the scar without changing the outcome. Critics — Geoffrey Keynes in England, George “Barney” Crile Jr. at the Cleveland Clinic — argued this from the 1930s and 1950s and were dismissed by a surgical establishment that treated the Halsted operation as settled doctrine.
The reckoning came from a randomized trial run by a surgeon who had once performed the operation himself. Bernard Fisher’s NSABP Protocol B-04, begun in 1971, randomized 1,665 women among radical mastectomy and two lesser procedures; B-06, begun in 1976, added lumpectomy. At every follow-up out to 25 years, survival was statistically identical. The Halsted hypothesis of contiguous spread was replaced by the systemic-disease model — that breast cancer is, at diagnosis, often already a whole-body problem the scalpel cannot outrun. The radical mastectomy was not banned; it was abandoned, retired by evidence as the textbook case of a mutilating operation sustained for 75 years by an elegant theory that happened to be wrong.
In July 2002, orthopedic surgeon J. Bruce Moseley and a Houston Veterans Affairs team reported in the New England Journal of Medicine that 180 patients with osteoarthritis of the knee, randomized double-blind to arthroscopic débridement, arthroscopic lavage, or a sham operation in which surgeons made skin incisions but inserted no instrument, had identical outcomes — and the gap between that finding and a decade of confident practice is the entire case. By 2002 the scope-and-clean operation for the arthritic knee was being performed on the order of 650,000 times a year in the United States at roughly $5,000 apiece, a multi-billion-dollar standard of care, on the mechanistic premise that flushing out debris and trimming frayed cartilage relieved pain. The trial showed it relieved nothing the placebo did not.
The harm here was not a body count of deaths but of unnecessary operations: hundreds of thousands of patients each year underwent a real surgery — anesthesia, incisions, infection risk, recovery, deductibles — to obtain a benefit indistinguishable from being wheeled into an operating room, cut, and sewn shut. At no point over two years of follow-up did either intervention group report less pain or better function than the sham group; the 95 percent confidence intervals excluded any clinically meaningful difference. The wonder of arthroscopy had been real for torn menisci and loose bodies, but for arthritis pain it was theater.
What makes the episode an exemplar of withdrawal is that it was killed by the right kind of evidence. Surgery had long been treated as exempt from the placebo-controlled standard demanded of drugs, on the assumption that an operation cannot ethically be faked. Moseley’s team did precisely that — and the result was so clean that the Centers for Medicare and Medicaid Services moved within a year to defund the procedure for osteoarthritis. A 2008 Canadian trial led by Alexandra Kirkley confirmed that arthroscopy added nothing to optimized physical and medical therapy, and by 2017 international guideline panels were issuing strong recommendations against it. The operation was never recalled or banned. It was disconfirmed, defunded, and abandoned — a textbook demonstration that a popular surgery can be a placebo, and that without a sham control no one would have known.
In 1987 the French neuroradiologist Hervé Galibert reported injecting acrylic bone cement into a single cervical vertebra eaten away by a hemangioma, and by the mid-1990s that salvage technique had been repurposed into a booming outpatient business — percutaneous vertebroplasty for the painful spinal fractures of ordinary osteoporosis — on the strength of nothing but uncontrolled case series in which patients reported feeling better; the gap between that universal operator conviction that the procedure plainly worked and what a blinded comparison actually showed is the entire case. When the procedure was finally tested against a credible fake in 2009, the cement turned out to do nothing the placebo did not do.
The clinical claim was seductive and mechanically intuitive: drive a needle through the back under imaging, inject polymethyl methacrylate (PMMA) into the collapsed vertebral body, stabilize the fracture, and abolish pain — often, operators said, on the table. By the mid-2000s the operation and its cousin kyphoplasty were a multibillion-dollar global market; U.S. Medicare alone was paying for vertebral augmentation in roughly a fifth to a quarter of compression-fracture patients, on the order of tens of thousands of procedures a year. The evidence underneath was almost entirely uncontrolled. Pain from an acute vertebral fracture improves substantially on its own over weeks, and a needle in the back is a powerful theatrical placebo — two facts the case series could not separate from any true effect of the cement.
On 6 August 2009 the New England Journal of Medicine published, in a single issue, two independent randomized double-blind sham-controlled trials. David Kallmes’s multicenter INVEST trial (131 patients) and Rachelle Buchbinder’s Australian trial (78 patients) both gave control patients the full ritual — the same positioning, the same local anesthetic, the same room, the smell of mixed cement — but no PMMA. Both found no meaningful difference. Pain and disability fell sharply in both arms, by roughly the same amount, at every follow-up point.
No agency banned vertebroplasty and no court enjoined it. It was discredited by its own pivotal trials and then slowly throttled by guidelines, payers, and a 2018 Cochrane review, surviving today only as a restricted, narrow-indication option rather than the routine fracture treatment it had been. It stands as the textbook modern lesson that a procedure can feel like it works to every operator and every patient and still be a placebo — and that the only way to know is the sham control almost nobody wanted to run.
In 1987 a team led by neurologist Olle Lindvall and neuroscientist Anders Björklund at Lund University, Sweden, began implanting dopamine-producing cells dissected from aborted human fetuses into the brains of Parkinson’s patients; the open-label results of the 1990s — surviving grafts on PET, patients walking who had been frozen — were celebrated as the first biological cure for a neurodegenerative disease. The gap between that promise and the controlled evidence is the case. Tested the way a drug would be — against sham brain surgery, double-blind — the graft did not beat placebo on its primary endpoint and inflicted a new, largely untreatable harm: persistent involuntary movements that ran on after every drop of levodopa was withdrawn.
Both trials that ended the era were funded by the U.S. National Institutes of Health and built around a placebo arm earlier enthusiasts had called unnecessary. In Curt Freed’s Denver–Columbia trial, published in The New England Journal of Medicine on March 8, 2001, 40 patients aged 34 to 75 were randomized to a fetal-tissue graft or to sham surgery — burr holes drilled, no cells implanted. The graft showed no benefit on the pre-specified global rating; a positive signal appeared only in a post-hoc subgroup aged 60 or younger. Then came the harm: dystonia and dyskinesias in roughly 15 percent of grafted patients (5 of 33), persisting after levodopa was reduced or stopped. The second NIH trial, run by neurologist C. Warren Olanow and published in Annals of Neurology in September 2003, deepened the failure: across 34 patients, no significant effect on the motor UPDRS (p = 0.244) at 24 months, 56 percent with off-medication dyskinesia, and a conclusion that transplantation “currently cannot be recommended as a therapy.”
The case is exemplary because the grafts worked biologically and failed clinically. Fluorodopa uptake rose; dopamine neurons survived robustly and were confirmed at autopsy. The cells lived — but thriving grafts drove a runaway, unregulated release of dopamine the brain could not modulate, leaving a procedure that could not be titrated, withdrawn, or reversed: a worse failure mode than the disease it meant to cure. The field abandoned routine fetal grafting and turned to the problem it had skipped — proving, against placebo, that putting cells in a brain helps the person attached to it.
Between roughly 1989 and 2002 American oncologists put an estimated 30,000–40,000 women with breast cancer through high-dose chemotherapy with autologous bone-marrow or stem-cell rescue (HDC/ABMT) before a single randomized trial had shown it saved lives; when the trials reported in 2000, the gap between promise and result was total. The regimen — massive cytotoxic doses that destroyed the marrow, followed by reinfusion of the patient’s banked cells to keep her alive — offered no survival benefit over conventional-dose chemotherapy, killed a meaningful fraction of patients through treatment-related toxicity, and cost an estimated $3.4 billion to deliver. The one study claiming a dramatic advantage was found to be fraudulent.
The procedure was never FDA-approved as a breast-cancer cure and never validated by a controlled trial during its boom. It spread on a seductive mechanistic story — breast cancer was dose-responsive, so more poison meant more cures — and on a litigation campaign that turned insurers’ refusal to pay into public scandal. The 1993 Fox v. Health Net verdict, awarding a dead schoolteacher’s family $89 million including $77 million in punitive damages, taught every HMO that denying the transplant was costlier than paying for it; coverage cascaded and four state legislatures mandated it.
The keystone of clinical belief was the work of South African oncologist Werner Bezwoda of the University of the Witwatersrand, whose trials alone reported a roughly three-fold survival advantage; when four randomized trials were presented together at the 1999 American Society of Clinical Oncology (ASCO) meeting, the other three showed no benefit. U.S. auditors who reached Johannesburg in early 2000 found his randomization existed only on paper and his control group had never received the standard treatment he reported. He was fired for “scientific misrepresentation” in 2000 and the Journal of Clinical Oncology retracted his work in 2001. HDC/ABMT for breast cancer is now the textbook case of an unproven, lethal intervention scaled to tens of thousands by hope, courtroom pressure, and a single fraud — abandoned not because it was banned, but because the evidence it had skipped finally arrived and demolished it.
In 1933 the Austrian psychiatrist Manfred Sakel announced from Vienna that he could break schizophrenia by injecting patients with enough insulin to crash their blood sugar into deep coma — and reported, on uncontrolled case series with no comparison group, recovery rates of 70 to 80 percent; the distance between that claim and what a controlled trial eventually found is the whole of this case. The procedure that resulted held patients in repeated, deliberately induced hypoglycemic comas — typically a course of 20 to 60 sessions, each lasting up to an hour, terminated by glucose — across asylums in Europe and North America for two decades, and killed on the order of one to two patients in every hundred treated, with some series running higher.
Insulin coma therapy (ICT) did not survive on evidence. It survived on enthusiasm and on a flattering selection effect. As the British psychiatrist Harold Bourne argued in his 1953 Lancet paper “The Insulin Myth,” ICT units selected younger, recently-ill, better-prognosis patients, lavished them with intensive nursing in dedicated wards, and then credited insulin for an improvement that the selection and the attention had largely produced. Bourne’s verdict — that insulin patients were “an elite group sharing common privileges and perils,” and that the coma added nothing specific — was a theoretical demolition that the field initially refused to print; the Journal of Mental Science sat on his manuscript for a year and rejected it, telling him to “get more experience.”
The empirical reckoning arrived in 1957, when Brian Ackner, Arthur Harris and A.J. Oldham published in The Lancet one of the first randomized controlled trials in psychiatric history. Fifty schizophrenia patients were randomly allocated either to insulin coma or to an identical regimen in which the unconsciousness was produced by barbiturates instead — same ward, same nursing, same coma, different agent. There was no difference in outcome. Whatever the regimen achieved, insulin was not the active ingredient. Within a few years ICT had collapsed, helped over the edge by chlorpromazine, which by the late 1950s delivered comparable results without driving anyone into a coma. It was never recalled and never banned; it was simply discredited and abandoned, and it is now taught as the first major therapy retired by a randomized controlled trial — and a textbook illustration of how a selection effect can masquerade as a cure.
Beginning around 1916 at the New Jersey State Hospital in Trenton, its medical director Henry Andrews Cotton announced that insanity was not a disease of the mind but a hidden bacterial infection — “focal sepsis” — seeded in the teeth, tonsils, sinuses, stomach, spleen, cervix, and above all the colon, and curable by cutting those organs out; the gap between his claimed 85 percent cure rate and the documented reality, in which his colon resections killed on the order of 30 percent of patients and cured essentially none, is the entire case. Cotton extracted teeth by the tens of thousands and performed serial abdominal surgeries on institutionalized, frequently non-consenting psychiatric patients, on the theory that a “detoxified” body would yield a sound mind.
The practice was not a fringe horror tolerated in obscurity. It was celebrated. Cotton, a protégé of the most powerful American psychiatrist of the era, Adolf Meyer of Johns Hopkins, was lauded in the press as a humane reformer who had abolished mechanical restraint and replaced it with “scientific” surgical cure. His 1921 book, The Defective, Delinquent and Insane, packaged focal-sepsis theory as the frontier of psychiatry, and visiting clinicians from Britain and the United States toured Trenton to watch the operations.
The reckoning was assembled but then buried. In 1924–25 Meyer commissioned a former student, the psychiatrist Phyllis Greenacre, to audit Cotton’s results; she tracked his surgical patients and found the records chaotic, the cure claims unsupported, the recovery rate no better — in fact worse — than for unoperated patients, and the mortality catastrophic. Meyer suppressed her report rather than publish it, protecting Cotton and his own reputation, and the surgeries continued for years. Only Cotton’s retirement in 1930 and his death in May 1933 finally ended them. The focal-infection theory of insanity collapsed entirely thereafter, and “surgical bacteriology” survives now as a textbook case of how a charismatic clinician, a surrogate endpoint, and a senior authority’s cowardice can sustain a lethal, evidence-free operation on the powerless for the better part of two decades.
For more than two thousand years, from the Hippocratic physicians of the fifth century BCE through the lancets of Benjamin Rush in 1793 and the basins that drained George Washington in 1799, the deliberate opening of a vein to let blood run was not fringe quackery but the central, prestige-laden therapy of Western medicine; the gap between that universal confidence and the documented absence of benefit — and frequent harm — is the entire case. Bloodletting was prescribed for fever, pneumonia, inflammation, apoplexy, melancholy, and almost everything else, on the strength of a humoral theory that mistook a visible physiological effect (a weaker pulse, a quieted patient) for a cure, and on the authority of an unbroken chain of celebrated practitioners who never once measured whether it worked.
The body count is impossible to total but enormous. In the “age of heroic medicine,” roughly 1780 to 1850, physicians escalated the dose: Rush bled Philadelphia’s yellow-fever patients to syncope and beyond during the 1793 epidemic, and Washington lost on the order of 80 ounces — about 40 percent of his blood volume, roughly 2.4 litres — across multiple bleedings in a single day before dying on December 14, 1799. The intervention reliably produced its surrogate endpoint, a slowed pulse and a sedated patient, while delivering anemia, hypovolemic shock, and accelerated death to people already weakened by disease.
The reckoning came not from a regulator but from arithmetic. In 1835 the Paris physician Pierre-Charles-Alexandre Louis published Recherches sur les effets de la saignée, applying what he called the “numerical method” to 77 pneumonia patients at La Charité. He compared those bled early (days 1–4 of illness) against those bled later (days 5–9) and found the result he himself called “startling and apparently absurd”: the early-bled died at 44 percent versus 25 percent for the late-bled, with no shortening of the disease that survived statistical scrutiny. The therapy that had defined medicine since antiquity was shown, by counting, to confer no benefit and probable harm.
No statute banned bloodletting. It was retired by evidence, by the rise of “therapeutic skepticism,” and by the gradual recognition that most fevers were self-limited and recovered despite, not because of, the lancet. It faded across the second half of the nineteenth century into obsolescence and is now the founding parable of evidence-based medicine: the case that proves the oldest, most universal, most authority-backed treatment can still be worthless once someone bothers to count.
The regimen that German obstetricians Bernhardt Krönig and Carl Joseph Gauss perfected at the Freiburg women’s clinic from 1906, and that an American feminist crusade exported to U.S. hospitals from June 1914, promised “painless childbirth” — and the entire case lives in the fact that it never delivered painlessness at all. The injection of scopolamine and morphine did not abolish the agony of labor; it abolished the patient’s memory of it. Women still felt every contraction and still screamed and thrashed through them; scopolamine merely erased the recollection afterward, so that a mother who had been strapped to a padded “crib” bed for hours, blindfolded and plugged with cotton, woke believing she had slept through a miracle. The surrogate endpoint — a patient who reported no memory of pain — was achieved. The actual endpoint — a labor that was safe and painless — was not.
The harms were two-fold and physical. The mothers, delirious from scopolamine, became so disoriented and combative that obstetricians routinely restrained them with leather straps to a screened crib-bed, gauze over the eyes and wadding in the ears, so they could not injure themselves during the thrashing the drug induced. The newborns, whose blood took up the morphine that freely crossed the placenta, were born sedated — flaccid, cyanotic, with depressed reflexes and suppressed breathing, exposed to asphyxia and sometimes requiring resuscitation that early-twentieth-century obstetrics could not reliably provide.
What carried Twilight Sleep was not obstetric data but a consumer movement. A June 1914 McClure’s Magazine article, “Painless Childbirth,” by Marguerite Tracy and Constance Leupp, triggered thousands of letters; Manhattan suffragists founded the National Twilight Sleep Association that year and campaigned through the New York Times, the Ladies’ Home Journal, and lecture halls, framing the right to forget labor as a feminist demand. The reckoning was equally a matter of public sentiment. In August 1915 one of the movement’s own leading advocates, Mrs. Frances X. Carmody of Brooklyn, died of hemorrhage delivering her third child under Twilight Sleep at Long Island College Hospital; her physician and husband insisted the drugs were blameless, but the symbol was lethal to the cause, and demand collapsed within roughly fifteen months.
No statute banned it. The combination simply could not be administered safely outside the quiet, individualized, heavily-staffed Freiburg setting, and once safer regional and inhalational analgesia matured, the regimen was abandoned as a relic — a textbook case of an intervention validated by the memory of the patient rather than by her safety or her child’s.
In 1920 the Chicago obstetrician Joseph Bolivar DeLee, in a paper titled “The Prophylactic Forceps Operation,” urged physicians to cut the perineum of laboring women as a routine to spare them the worse damage of a ragged spontaneous tear — and the gap between that protective promise and the eventual evidence is the entire case. By the late twentieth century the operation DeLee reasoned his way into was one of the most common surgical procedures performed on American women, done on the order of a third of all vaginal deliveries (60.9% in 1979) and on a clear majority of first-time mothers, almost none told there was no trial behind it.
The justification was intuitive: a clean, controlled incision must heal better than a jagged laceration, and a pre-emptive cut must protect the pelvic floor against future prolapse and incontinence. The intuition was wrong in the most consequential way. When the procedure was finally tested against the comparator it had skipped for decades — selective use, cutting only on indication — the routine cut did not prevent severe trauma. A midline episiotomy extended the wound straight toward the anal sphincter and rectum, so the prophylactic incision was itself causally linked to the third- and fourth-degree tears it was meant to forestall.
The reckoning was slow because the practice was entrenched, not because the data were ambiguous. A 1983 interpretive review of more than 350 sources spanning 1860 to 1980 found no defensible evidence for routine use; the 1993 Argentine Episiotomy Trial, a randomized study of 2,606 women, showed routine use conferred no benefit and more harm; and the 2005 AHRQ-commissioned systematic review in JAMA closed the question, finding routine episiotomy improved no immediate outcome and prevented no incontinence or prolapse. In April 2006 the American College of Obstetricians and Gynecologists issued Practice Bulletin No. 71, recommending the routine be restricted. The procedure was not banned — it retains narrow, evidence-based indications — but its eighty-year career as a default was abandoned. It stands as obstetrics’ cleanest case of a plausible, near-universal intervention adopted on reasoning and reversed only by the trial that should have come first.
For roughly the first three-quarters of the twentieth century, tonsillectomy was the most frequently performed operation in the United States — a near-compulsory rite of childhood scheduled on the order of a million-plus times a year for sore throats, “mouth breathing,” poor appetite, and the vague proposition that a child would simply be healthier without tonsils; the gap between that universal promise and the evidence is the entire case, because the operation was never shown to deliver the broad benefits claimed, killed a measurable number of the children it was sold to protect, and for a period in the 1940s demonstrably raised the risk of paralytic polio. At its 1959 peak roughly 1.4 million tonsillectomies were performed annually in the U.S., the overwhelming majority on children, and by mid-century an estimated 30 percent of American children had lost their tonsils — many to surgeons who, examined honestly, could not say why.
The procedure rode the “focal infection” theory: the early-twentieth-century belief that lurking pockets of chronic infection in the tonsils seeded disease throughout the body and were best excised pre-emptively. On that theory the indication became, in practice, the mere possession of tonsils. The surrogate that justified the knife was not a measured health outcome but a clinical impression — the tonsils “looked enlarged” — and impressions, it turned out, were nearly random. In 1934 the American Child Health Association sent 1,000 New York schoolchildren through successive examinations and found 61 percent had already been tonsillectomized; of the remaining 39 percent, physicians recommended surgery for all but 65, then for nearly half of those who had just been cleared, and again for nearly half of that residue — a recursive demonstration that the indication lived in the examiner, not the child.
The disconfirming evidence accumulated for forty years before the practice yielded. James Alison Glover’s 1938 study showed English tonsillectomy rates varying by an order of magnitude between districts with no relation to disease — the founding observation of “unwarranted variation,” still called the Glover phenomenon. From 1942 onward, epidemiologists documented that children tonsillectomized shortly before exposure to poliovirus suffered the deadly bulbar form at multiples of the background rate. And in 1984 the first rigorous randomized trial, by Jack Paradise in the New England Journal of Medicine, found a real but narrow benefit only for the most severely and frequently infected children — a tiny slice of those who had been operated on for decades. The operation was not banned. It was restricted, its indications tightened, its volume cut by more than half, retired from routine use by evidence that arrived long after the harm.
On October 30, 1967, in Zurich, the neurosurgeon M. Gazi Yaşargil sutured a scalp artery to a cortical branch of the middle cerebral artery under the operating microscope, rerouting blood around a blocked vessel to feed a starving brain; the operation was elegant, technically dazzling, and — for the prevention of stroke in patients with carotid and middle-cerebral disease — almost entirely unproven, and that gap between surgical beauty and clinical benefit is the entire case. For nearly two decades the extracranial-intracranial (EC-IC) arterial bypass spread on the strength of its own plausibility and on case series reporting open grafts, until a single randomized trial showed it prevented nothing it claimed to prevent.
The operation was never a fraud and never a mass killer in the lobotomy sense. It killed and disabled quietly, at the margins: a procedure with a roughly 12 percent thirty-day rate of stroke or death imposed up front on patients who, the trial would show, were no better protected afterward. The surrogate that sustained it was graft patency — the bypass stayed open in about 96 percent of cases, a number surgeons and angiograms could see and celebrate. A patent vessel looked like a prevented stroke. It was not the same thing, and conflating the two is the mechanism that kept the operation alive.
The reckoning arrived not from a regulator or a court but from an eight-year, NIH-funded randomized controlled trial led by the Canadian neurologist Henry J. M. Barnett of London, Ontario. Published in the New England Journal of Medicine on November 7, 1985, the International EC/IC Bypass Study randomized 1,377 patients at 71 centers in 14 countries and found that surgery added to best medical care did not reduce fatal or nonfatal stroke; two subgroups — patients with severe middle-cerebral stenosis and those with persisting symptoms after carotid occlusion — actually fared worse with the operation. Within a few years the procedure collapsed from a flourishing subspecialty to a narrow, rarely-indicated salvage technique. It was not banned. It was disconfirmed, and it became one of medicine’s foundational lessons in why a trial must precede an operation, not follow it.