The Loss of Serendipity in Psychopharmacology

This Commentary on the psychopharmacological revolution focuses on 2 mysteries: fostering medication discovery and finding out how they work. When I entered psychiatric training in 1953 at Creedmoor State Hospital, a 6000-bed institution with few therapeutic aspirations, psychotropic drugs were an impossible dream. For those individuals who have not had such an experience, an extremely morbid imagination is needed to conjure up that bedlam. It was rendered just tolerable by knowing that this training made one fit to be a candidate psychoanalyst. The next 2 years were spent at the US Public Health Service Hospital in Lexington, Kentucky, a 1000-bed federal therapeutic prison for opioid addicts, which amazingly included the most advanced center for human psychopharmacological experimentation in the world. The Addiction Research Center, led by the rigorous scientists Wikler and Isbell,¹ incisively demanded objective, unbiased work and conducted pioneering studies of chlorpromazine, reserpine, and lysergic acid diethylamide.

There was a seismic shift in psychiatry between 1950 and 1970. These were disorienting, delirious, exhilarating, and enchanting times. Therapeutic discoveries resulted from chance observations of unexpected clinical benefits or as inadvertant outcomes of blind pharmaceutical searches. The pace of discovery of entirely new classes of psychotropic drugs in the 1950s and 1960s was dizzying, and included lithium, lysergic acid diethylamide, chlorpromazine, iproniazid, reserpine, imipramine, chlordiazepoxide, haloperidol, and clozapine.

All of these major classes of psychotropic drugs were serendipitously discovered and had entered the psychiatric literature by 1969. But what stymied such generative serendipity over the next 40 years? Several anti-serendipity factors can be suggested. They include the expectation that serendipity would be replaced by rational drug design fostered by translational research, the radical compression of clinical time from cost-control measures, and ironically the adoption of the parallel-group, placebo-controlled, double-blind trial as the sole method for demonstrating drug efficacy.

The discovery of DNA in 1953 foreshadowed that genetics and molecular biology would revolutionize medicine. The newfound psychotropes prompted an explosion of neurotransmitter and receptor function studies, which deeply enriched knowledge of central nervous system function. Furthermore, these studies raised high hopes of rational drug development and enhanced the still prevailing conventional wisdom that medicine flows from bench to bedside, and reenforced the notion that knowledge of normal function is necessary before addressing abnormal function.

However, that does not correspond with medicine's history, wherein studies of pathology often led both to therapeutics and discovery of unsuspected normal functions. The serendipitous observation that cowpox infection induced smallpox immunity led to vaccination, the study of beverage contamination led to pasteurization, and the injection of rabid dog's dried spinal cords prevented the inevitable development of fatal human rabies. These treatments initiated germ theory, bacteriology, virology, and immunology. The clinical study of scurvy led to lime juice treatment and prophylaxis. Beri beri and pellagra studies led to nutritional supplements (despite the conventional wisdom of bacterial infection), leading to specific vitamins and enzymatic cofactors as the key to their efficacy. Other diseases, treated by nutritional supplements, revealed human's specific inability to synthesize essential amino acids. Liver treatment of pernicious anemia led to the discovery of vitamin B₁₂, as well as malabsorption syndromes that revealed unknown distinct intestinal functions. The lesson for psychopharmacology is to once again focus on understanding how medications work in ill humans.

A neglected issue in past psychiatric successes is where the definitive clinical observations were made. The benefits of lithium, chlorpromazine, imipramine, reserpine, and clozapine were verified by observations in chronic state psychiatric institutions and the antidepressant effects of iproniazid appeared in a chronic tuberculosis ward. This suggests a hypothesis about the anti-serendipity of the past 40 years. It may be due to the radical constriction of time for informed clinical observation of unexpected medication benefits as well as their follow-up. The drastic changes in medical practice and academic medicine since 1970 not only led to severe constriction of clinicians' treatment time per patient, but also to any opportunity for serendipitous discovery.

How did this occur? Hospital-based academic medicine was largely supported by hospital income allocated to support research. This freed up time for clinicians to follow through with surprising benefits. The bottom line approach of managed care and the insurance industry effectively destroyed this form of research support by declaring it irrelevant to direct treatment benefit. The same forces radically shortened hospital stays, preventing longitudinal study of inpatients, who are regularly discharged before the effects of a new therapeutic regimen become clear. The current administrative boast is how effective a hospital has been in reducing length of stay.

In current psychiatric practice, insurance demands time limits and paperwork, leading to a clinical practice with little time for fresh observations, much less discovery. Clinical research organizations sap industrial support from academic research while performing preformed, exquisitely structured protocols less expensively.

Chance favors the prepared mind, said Pasteur, but there must be proper environments that foster chance observations, allowing prepared minds to pursue promising leads. Surprisingly, the current clinical trial model contributes to anti-serendipity. Random assignment to concurrent placebo and putative treatment groups was rapidly incorporated into pharmacological trials in the 1950s. The antipsychotic action of chlorpromazine was greeted with profound skepticism, if not open derision. Largely to address frequent claims that the evidence for pharmacotherapeutic benefits was invalid or due to “chemical straight jackets,” clinical trials were amplified by double-blind precautions.

Testing if these new medications were actively and specifically effective was the priority. Statistical superiority of a test drug to placebo, measured by average outcome scale scores, established specific medication activity. The 1962 Kefauver-Harris US Food and Drug Administration (FDA) amendment required the demonstration of acute medication efficacy before marketing, without any stipulation concerning effect size, translation into clinical benefit, determination of just who would benefit, systematic attention to long-term benefit maintenance, or late-onset toxicities. The pursuit of short-term statistical superiority to placebo became industry's Holy Grail of marketability.

This incurred several persisting ambiguities. If 60% of those individuals treated with medication had substantial scale-measured improvements, while only 30% of those treated with placebo did so (assuming statistical significance), it follows that for approximately half of those who improved while receiving medication, the medication was not causing the improvement. The individual who required specific beneficial pharmacodynamic action for clinical improvement remained unknown. Therefore, attempts to determine how a medication brought about specific benefits, by studying those individuals who improved while receiving medication, is sabotaged by actually studying a causal mixture.

Early statistical attempts by using regression analysis to contrast the effects of different medications from each other and placebo attempted to identify subgroups with distinctive response patterns. However, many findings did not replicate. The pharmacological dissection approach has been most successful when applied to hypothesized subsyndromes, for which distinctive therapeutic response had already been clinically noted. Validation requires controlled treatment trials (eg, panic disorders, distinguished from other anxiety disorders² ; agoraphobia, distinguished from other phobias² ; atypical depression, distinguished from other major depressions³ ; and schizophrenia with childhood asociality, distinguished from patients with schizophrenia with superior antipsychotic benefit).⁴

However, pharmacological dissection failed to thrive as the 2 major funding sources (Veterans Administration and National Institute of Mental Health [NIMH]) turned away. NIMH abandoned support for placebo-controlled studies of marketed medications, arguing that this was the proper province of industry. NIMH and academia were to focus on basic processes. Industry also did not pursue pharmacological dissection because finding a statistically significant benefit was the sole efficacy requirement needed for FDA marketing approval. Worse, narrowing a broad syndrome that otherwise would allow the broadest marketing would diminish profitability. The unintended effect of NIMH completely allocating placebo-controlled trials of marketed agents to industry was to prevent improving clinical psychopharmacological approaches to nosology and elucidating pathophysiology.

Given the still unbridged gap between translational research and drug discovery, can serendipity be revitalized? Because this would require reversing the constrictions of clinical discovery time, it is probably a utopian fantasy. Imagine a network of computerized science–run day hospitals devoted to open pilot trials of safe but unusual medications. What sort of drugs? Initial clinical hints come from epileptology and addiction medicine considering that the full range of anticonvulsants^{5 - 6} and mixed agonist-antagonist opioids⁷ have been barely touched on. Such pilot observations must be followed by definitive studies because for any particular patient who remits during medication treatment, it is still not known if he or she benefited from a specific pharmacological action or just improved on his or her own. Because medications have risks, this uncertainty has clinical as well as scientific implications.

Whether a treatment intervention actually works in an individual patient can be studied by “intensive design”⁸ ; that is, repeated periods of intervening and nonintervening, judging whether benefit synchronizes with intervention. Therefore, an alternative trial design is to initially treat all patients openly with the study medication, titrating for the individual's optimal dose, until it is clear if there is an insufficient therapeutic response. If the proportion of such nonresponders is high, this unpromising investigation can be terminated. If the proportion is high, responders would be maintained with medication for a period, but then randomly, double-blindly assigned to receive placebo or to continue receiving the medication. To avoid discontinuation effects, placebo substitution should be slowly incremental. Slow withdrawal also makes detection of signs of relapse easier and remediable by restoring the optimum medication dose. All patients would be closely followed up for defined signs of relapse. A significantly higher relapse rate in the placebo-substituted group than in the medication-maintained group would provide clear evidence of medication efficacy.

Those patients who showed signs of relapse when shifted to receiving placebo likely had actually benefited by pharmacodynamic action, as distinct from other causes. Those patients who responded during medication treatment but continued to do well when switched to placebo would be less likely to be specific medication responders. This design would define specific individuals as likely specific medication responders, likely nonspecific responders, and nonresponders. Other practical benefits are that all patients initially receive active treatment. This fosters recruitment because many patients will not accept the risk of immediate assignment to placebo. Also, patients will learn whether the medication is necessary for them to remit. Academic investigators have successfully used this design.^{9 - 10}

Embedding objective measures (imaging, genetics, psychophysiology) in studies of specific medication response should enrich theories of medication action. If an objective predictor of specific medication-induced remission is also specifically treatment responsive, it becomes a central clue to elucidating both pathophysiology and medication response. Such studies could uniquely advance psychopharmacological scientific practice.

The imaginative objective study of the successful specific treatment of patients with illness to determine how treatments work should be a major focus of medical sciences. Given the distressing decline in pharmaceutical innovation, should serendipity continue to atrophy? The proposed revitalizations would require a far different, initially difficult to support, but probably a qualitatively superior medical environment. Is it not time to resurrect an already proven method of serendipity in science?