The Lithium Controversy: A Historical Autopsy
By Barry Blackwell
I am delighted Larry Stein has joined Jose de Leon in expressing interest and concern about aspects of an ancient controversy that may have contemporary relevance. Perhaps it is time to engage in a more detailed and complete analysis of the issues raised, many of which are dealt with in my memoir, “Bits and Pieces of a Psychiatrist’s Life”, and will be cited in this essay (Blackwell 2012).
It is now almost half a century since Michael Shepherd and I published our article “ProphylacticLithium; Another Therapeutic Myth?” in the Lancet, which commented on and critiqued a previously published study by Mogens Schou and his colleague in the Archives of General Psychiatry (Baastrup and Schou 1967), making the claim that lithium had a unique effect in preventing future episodes of manic depressive disorder. Their riposte to our critique appeared later the following year (Baastrup and Schou 1968).
If history has anything to offer today then such past events deserve to be dissected. As possibly the sole remaining protagonist in the fierce debate these two papers generated, I offer this autopsy, personally performed, and invite INHN members to comment.
This essay will be in three parts; reciting the facts themselves; an analysis and interpretation of the scientific zeitgeist prevailing at the time, commenting on the emotions aroused; and, finally, the possible relevance of such matters today.
I completed five years of psychiatric training at the London University Institute of Psychiatry and Maudsley Hospital, including a two year fellowship in animal research leading to my doctoral degree in Pharmacology from Cambridge University. Following this, I completed a two year research fellowship with Michael Shepherd. At his suggestion, I undertook to analyze and critique Schou’s data claiming that continuous administration of lithium prevented future episodes of manic depression. There was no control substance since other “mood stabilizers” were far in the futureand Schou rejected placebo as unethical based on his clinical experience and convictions of efficacy. So, there was no double blind procedure to protect against potential observer bias, although a placebo control was included in the definitive studies that confirmed his beliefs many years in the future (see later). The possibility of bias existed both due to the study design and because Schou was quite open to admitting enthusiasm for his hypothesis, derived from a family member’s benefit after all else had failed to stifle recurrences. At this time, prophylaxis was such a unique and unexpected claim it might have evoked a “too good to be true” skepticism, which heightened our concern about potential bias in an uncontrolled study.
There was no established method, at this time, with which to evaluate such a unique claim; Schou’s series included a heterogeneous collection of subjects broadly interpreted as suffering from manic depressive disorders but with varying affective manifestations, of differing duration, frequency and severity. This created concerns about the specificity of the claim as well as statistical issues, primarily concerned with regression to the mean – spontaneous remission from a high baseline in a fluctuating disorder. Other statistical concerns were displayed and discussed in sophisticated terms in a paper read to an NIMH/VA study group and subsequently published in Frank Ayd’s newsletter (Blackwell 1969). Similar statistical and methodological criticisms were made by Malcolm Lader in the Lancet (1968). The essence of these concerns focused on the impossibility of distinguishing dependency on a medication, or spontaneous remission from prophylaxis, a problem I dubbed the “panacea paradigm”. The scientific caveats evoked sharp rebuttals from clinicians who knew better, including Nate Kline in America (Kline 1968) and Sargent in Britain (Sargant 1968). Sargant’s comments are especially illustrative of the tone and angst aroused in this debate. He appealed for the abandonment of “crude statistics” and “valueless double blind sampling” in favor of “bedside observations for the sake of England’s treatment reputation in world psychiatry.”
Seldom noted or commented on is that in addition to concerns about methodology we applied Schou’s statistical technique to a convenience sample of 13 manic-depressive patients from the Maudsley data base treated with imipramine and found results comparable to lithium.
It is important to place these events in their broader historical perspective and consider how this colored the controversy. Until the Flexner revolution in the early twentieth century, medicine was an apprentice profession whose materiamedica included many panaceas, nostrums and placebos, the popularity of which depended largely on the status of the apothecaries, physicians or barber surgeons who dispensed and endorsed them. As medicine became more scientific and moved from the community into academic medical centers, its remedies became potentially more effective. Trial methodology and statistical analyses developed to rigorously evaluate therapeutic claims. Eventually, the double blind controlled study became the gold standard. Psychiatry lagged behind in this regard; chloral hydrate, barbiturates, paraldehyde and amphetamines were synthesized and well established with regard to effectiveness and shortcomings but nothing new or potentially more effective existed to compare them against.
Lithium had a persisting role in this evolution. A naturally occurring metallic ion with no commercial potential or synthetic rivals, it was introduced into medical practice, in 1859, as a bone fide treatment for gout but then increasingly as a panacea with Lithia tablets used for a wide variety of ailments, despite absence of benefit and occurrence of side effects. In the earlier days of scientific medicine, it was used as a salt substitute in cardiac disease until the absence of a method for measuring blood levels led to cases of fatal toxicity. It was withdrawn from medical practice, in 1949, the identical year Cade reported its therapeutic effect in psychotic manic patients.
Many pioneers in psychopharmacology consider the two decades from 1950 to 1970 as the seedbed for all the original treatments in every category of psychiatric disorder. Lithium provides twin bookends for this exciting epoch, beginning with Cade’s discovery of lithium for acute mania and ending with Schou’s discovery of prophylaxis- both enabled by discovery of a method for measuring lithium levels in the blood. In an account of his own discovery, Cade recognizes Schou as “The person who has done most to achieve this recognition.”
The trajectory of lithium’s ascendancy as a prophylactic agent during these two decades is best told by Schou himself (Schou 1998) and Paul Grof, with whom he collaborated (Grof 1998) and who wrote Schou’s obituary at the time of his death in 2005 at age 87 (Grof 2006). The obituary is an appropriate paean of praise for a colleague who was twice nominated for the Nobel Prize in medicine and physiology. Grof traces Schou’s dedication to our field from vivid childhood memories of depressed patients in the asylum where his father was medical director, “wandering in the hospital park with drooping heads and melancholic faces waiting for the depression to pass and fearing future recurrences.” This impressed on Mogens the need for a sustained prevention of depression “at the time when maintenance ECT was clearly not the ideal.”
When Cade published his findings on lithium, in 1949, it attracted Schou’s attention although Cade himself had only demonstrated an acute effect in manic psychosis and found that “in three chronically depressed patients, lithium produced neither aggravation nor alleviation of their symptoms.”(Cade 1971). Despite this fact, Schou’s interest was piqued by his concern that since age 25, his brother had experienced “yearly episodes of depression. In spite of ECT, drug treatment and hospitalization the depressive attacks came again and again” (Schou 1998). During the decade 1950-1960 that Cade vigorously pursued his interest and research on lithium,imipramine was probably not available until towards the end of the decade and it is likely that during this interlude,Schou prescribed his brother lithium, which “changed his life and the lives of his wife and children.” This leads me to wonder if, in fact, his brother manifested a Type 2 bipolar disorder, in which mild hypomania went unremarked. Grof notes that late in his career,Schou developed a special interest in “hidden bipolars” – patients with depression who had unrecognized bipolar disorders. Schou’s last scientific presentation, shortly before his death, was on this topic and a new study he was proposing (Grof 2006).
Schou was not a founding member of the CINP but participated in the first Congress in Rome, in 1958, when he contributed to the final session, a “General Discussion”. He recalls his comment that “On the chemotherapeutic firmament lithium is one of the smaller stars” (Schou 1998).Baastrup and Schou’s seminal publication in the Lancet (Baastrup and Schou 1968) had been underway for seven years, begun probably in 1961. The above facts help explain why imipramine was not included as a comparative drug, even though the population included both unipolar and bipolar depressed patients. Later on, as his familiarity with imipramine grew, he used the term “normothymics” to include both lithium and imipramine (Schou 1963).
These events resonate with the concerns raised in our paper criticizing Baastrup and Schou’s methodology and conclusions (Blackwell and Shepherd 1968) regarding the uncertain specificity of lithium and the absence of a control comparison. To be fair, Schou and Grof draw attention to the problem of using a placebo control based on the high suicide rate in untreated affective disorder. Schou eventually resolved this obstacle with a novel trial design in which sequential analysis of paired placebo and lithium patients was coupled with an immediate switch to open treatment for any recurrence(Schou 1998).
Because the ad hominem aspects of this debate still linger, I will quote a few laudatory comments made by his friend and colleague Paul Grof in the obituary. Schou was “a caring man with great humility”, with a “love and compassion for people” and also a “highly meticulous” researcher who “never left a task undone”.
In 1970, two years after I immigrated to America, my mentor Frank Ayd and I conceived the idea to invite all the scientists and clinicians who had discovered the original therapeutic compounds in each disorder to tell their own story at a conference in Baltimore. These first person accounts were published the following year in our edited book, “Discoveries in Biological Psychiatry” (Ayd and Blackwell 1971). They included Albert Hoffman (Hallucinogens), Frank Berger (Meprobamate), Irv Cohen (Benzodiazepines), Pierre Deniker (Neuroleptics), Nate Kline (MAO Inhibitors), Roland Kuhn (Imipramine), John Cade (Lithium), Paul Janssen (butyrophenones), and Jorgen Ravn(Thioxanthines). I contributed a chapter on The Process of Discovery, using the interaction of cheese and the MAOI as a template and Frank Ayd concluded with a summary on The Impact of Biological Psychiatry.
Noteworthy now, but not discussed at the time, was that Frank did not include Schou. Perhaps, speculatively, this might have been for two reasons. First, Schou’s contribution was derivative to Cade’s and more adaptive than original; secondly, because the benefits of all these “serendipitous” discoveries had all been confirmed in well controlled clinical studies. The methodological difficulty of proving prophylaxis and the specificity of lithium in doing so, would linger experimentally (but not in practice) for almost twenty years, until the definitive studies, in 1984, by the Medical Research Council in Britain (Glen et al) and the NIMH study group in the USA (Prien et al). This latter study, larger of the two, involved a two year follow up of 117 bipolar and 150 unipolar patients given lithium, imipramine, both drugs or placebo. It reached three major conclusions:
(1) Imipramine is preferable to lithium for long term prevention following recovery from an acute episode of unipolar depression.
(2) For both bipolar and unipolar disorders, the preventative effects of both lithium and imipramine parallel their effects in acute episodes.
(3) Even when lithium and imipramine are effective, they are not panaceas. Only a quarter to a third of patients with either bipolar or unipolar disease were treatment successes.
Eighteen years after Schou’s original study, the issues of diagnostic specificity, comparative and specific benefits for lithium or imipramine and their magnitude were scientifically defined in the absence of potential observer bias and statistical flaws.
In retrospect, some of the angst directed to Shepherd and I might have emanated from various attributions; methodological puritanism, unjust allegations of bias or of potential therapeutic nihilism- for which the Maudsley was rather unjustly credited. Nevertheless, it was a contemporary and colleague of mine from the Maudsley who, in comments on events in the 1960’s,made the satirical observation that, “Writing from the Olympian heights of the Institute of Psychiatry Barry Blackwell and Michael Shepherd airily dismissed Schou’s evidence” (Silverstone 1998). But we were all scientific babes in the wood when it came to prophylaxis, bias must always be assumed unless it is eliminated and, while the atmosphere at the Institute was decidedly empirical, it was also benevolent to developments in psychopharmacology. The 1998 book, “The Rise of Psychopharmacology and the Story of the CINP”, lists the 33 Founders of the organization. 27 were clinicians but only three were from Britain. Sir Aubrey Lewis, Michael Shepherd and Lindford Rees. Sir Aubrey was an active participant in the first CINP Congress.
My first rotation at the Maudsley as a resident, in 1962, was under Lindford Rees, a dedicated psychopharmacologist who carried out early studies on imipramine; my second rotation was on the Professorial Unit, where Aubrey Lewis took me under his wing and, once he was sure I was not interested in psychoanalysis, arranged and endorsed my psychopharmacology training. True, Michael Shepherd was a sceptic and scientific purist but, lest he be blamed for any perceived disrespect towards Schou, I must make clear that I was first author on our Lancet paper, chose its title and was responsible for the data analysis and conclusions reached.
Nor were either of us wedded uncritically to double blind methodology. We were well aware of its shortcomings. Immediately before our paper on lithium, Shepherd and I worked on a drug study for a pharmaceutical company which went nowhere because of rigid, impractical and unrepresentative criteria for recruiting subjects. We published our conclusions on contemporary trial methodology in the Lancet (Blackwell and Shepherd 1967). During my psychopharmacology research in animals, I collaborated with a colleague evaluating and recording the outpatient use of MAO Inhibitors by all the consultants and residents at the Maudsley. This must have been among the first “effectiveness” studies to look beyond the boundaries of conventional controlled clinical trials at what happens in real life (Blackwell and Taylor 1967). The results were unusual and revealing. One intriguing finding was how the interaction between prescriber and drug influenced outcome, precisely what the double blind study is designed to stifle or eliminate. The most powerful effect on outcome, above diagnostic and demographic variables, was prescriber behavior. Those who used MAOI’s a lot, as “first choice” drugs,” had better outcomes than those who used them more reluctantly, as “second choice” drugs. The reasons appear self-evident. First choice prescribers reaped the benefits of their enthusiasm, the placebo response, spontaneous remission and perhaps a willingness to tolerate side effects. The “second choice” population contained more treatment resistant and side-effect sensitive patients alert to the physician’s skepticism. Needless to say, these outcomes were likely to reinforce physician attitudes and behaviors. Pharmaceutical reps soon learned to capitalize on this phenomenon by offering physicians a stipend in return for using their new drug in “the next few patients you see.”
Another finding was the intriguing comment one enthusiastic prescriber made in the chart, “Although this patient never looked depressed before, she looks less depressed now.” Perhaps drug outcomes sometimes influence diagnostic habits. So, in retrospect, one wonders if Schou’s late-life interest in “hidden bipolars” was evoked by his extensive experience and enthusiasm for lithium. Perhaps he was curious to find if there were subtle and covert clinical indicators of hypomania in some recurrent unipolar patients who, like his brother, unexpectedly benefited from lithium.
Also relevant to the prophylaxis debate was our finding that 18% of that population remained on an MAOI for 3 years after recovering from an initial episode of “atypical” depression and relapsing on attempts at withdrawal, a finding we attributed to “dependence” but identical to the 11 out of 60 patients (18%) who took lithium for 3 years and where “prophylaxis” was the explanation (Baastrup and Schou 1967). Further complexity is added by noting that, independent of diagnosis or treatment method, about 80% of all outpatients at the Maudsley stopped treatment within 3 months, while the remaining 20% remained, sometimes for years. What then is the difference between “dependency” and “prophylaxis”? This raises semantic, philosophical and clinical issues and attempts to discriminate by stopping treatment introduce an ethical dimension of potential harm. Perhaps this introduces an “eye of the beholder” component concerning which semantic meaning one applies and is this, in turn, partly based on the physician’s temperament?
I am ambivalent; my heart tells me one thing and my head another. Am I a neutral researcher, seeker after truth, or a benevolent healer following the Hippocratic ideal of “first do no harm”? Is what I see “prophylaxis” or “dependence,” perhaps some of each?
The issue of potential clinical bias is nuanced; an intimate interaction between clinician and patient, particularly a friend or relative, can sow the seed of a new idea, worthy of further investigation or testing as a hypothesis. The problem arises in how to remove this bias towards the new idea from the outcome of an investigation. Sometimes it is more difficult than others and in my own initiation into research I was fortunate.
As a first year resident, I became involved in the interaction of MAOI and tyramine containing foods. The first clue to the possible cause of a sometimes fatal hypertensive crisis came when a hospital pharmacist (GEF Rowe) read a letter I wrote to the Lancet describing the syndrome and its symptoms – predominantly a sudden severe pounding headache. He recognized and described this process in his wife on two consecutive occasions after she ate cheese; “Could there be something in the cheese?” So a fellow resident and I took an MAOI for two weeks before eating cheese from the hospital cafeteria. Nothing happened. Nevertheless, I subsequently obtained data from twelve cases in less than 9 months, some including measures of blood pressure and one produced under experimental conditions (Blackwell 1963). Nobody suggested my interest and potential bias was artificially elevating a patient’s blood pressure or causing a headache. But the research director of the pharmaceutical company making the MAOI did write a letter to the Lancet stating that my conclusions were “unscientific and premature”. Within weeks, researchers at another hospital had isolated tyramine in their body fluids after eating cheese. The issue was no longer moot. Physiological and physical parameters are less subject to observer bias than emotional and behavioral outcomes but finding a glib reason to disparage either is easy.
The issue at stake is also a matter of semantics and timing. The word “bias” has a pejorative connotation, especially when applied retrospectively, to allege an investigator’s potential faulty judgment in an uncontrolled study. The term then assumes an unpleasant but perhaps unintended ad hominem element. Contrast this with the prospective benign intent of a controlled study- to protect an investigator from his or her laudable compassion and therapeutic enthusiasm.
On which side of this semantic fence one sits, at a given moment or on a specific issue may be influenced by other factors, including the reputation and fame of the investigator and one’s acquaintance with them or sympathy with their claims or ideas. There is no better example than Linus Pauling’s orthomolecular beliefs and zeal in promulgating them. He was the only scientist to have won two unshared Nobel Prizes; Chemistry, in1954, and the Peace Prize, in 1962. No person on the planet had better scientific and humanistic credentials. But following the onset of Bright’s disease, he developed a strong belief that physical and mental illness might be alleviated by manipulating vitamin levels.In 1968, he published an article in Science on “Orthomolecular Psychiatry.” Pauling, himself, took 3 grams of Vitamin C daily to prevent the common cold and collaborated with a British cancer surgeon on its use in prolonging life. These claims were not disproved until over ten years later by controlled research at the Mayo Clinic. A physician critic, in an article in The Atlantic (Offit 2013) commented that although Pauling was “spectacularly right” in his early scientific career, his late career orthomolecular assertions were “so spectacularly wrong that he was arguably the world’s greatest quack.” Putting this cautionary tale aside, it is only just to remark that Schou was certainly right, while Pauling was unequivocally wrong.
By the time Schou was attempting to demonstrate the prophylactic potential of lithium in Scandinavia, the Congress in the United States had enacted the Harris-Kefauver legislation mandating that drug manufacturers prove their products were effective as well as safe. In 1968, I immigrated to America to become the Director of Psychotropic Drug Research for the Merrell Company, in Cincinnati. The company was just recovering from the stigma of having marketed thalidomide for insomnia and the market place was cluttered with compounds insearch of a credible rationale or proof they were more effective than a placebo. Merrell had two such products in the psychotropic domain and I had the daunting task of proving they could pass muster. One was “Alertonic” a cunningly named reddish-brown liquid popular in nursing homes for the elderly that contained small amounts of alcohol, B vitamins and an amphetamine like stimulant. A substantial placebo response made the task of proving efficacy impossible.
A still more dubious drug was Frenquel with the marketing claim that it stifled hallucinations whatever the diagnosis and the odd characteristic that the intravenous dose was higher than the oral one. Since no other drug had a similar claim, this was a niche product and the threat of withdrawal produced a flood of protests from patients and clinicians who “could not live without it.” The FDA was unimpressed and impervious to testimonials but I decided to visit one of the more credible supplicants to better define what was going on. The following account appears in my memoir in the piece on “The Pharmaceutical Industry” as a Bit titled “Snake Oil” (Blackwell 2012).
“I had a trip planned for New York and decided to call on one of the Frenquel seekers. The office where the cab let me off in Greenwich Village was next to a homeless drop in center. The doorbell was answered by a polite, casually dressed, older physician who greeted me and ushered me into a room in the basement furnished more like a family doctor’s office than a psychiatrist’s den. In the center of the room stood an examining table rather than a reclining couch with an attached shiny aluminum tray on which lay a large syringe containing a colorless liquid I assumed was Frenquel. Sitting on the table, legs dangling and wearing a brightly colored, mildly revealing dress was an attractive young woman. Almost before I could take in the scene, she leapt to the floor, faced me and began to shout, “So you’re the f----ing drug company man that’s going to ruin my life!”
The doctor moved quickly to take her arm, guided her back to the table, and did his best to calm her. She settled down and lay back, still eyeing me furiously, pulling up the sleeve of her dress to expose the veins in the hollow of her arm. This was obviously a well-practiced routine, which the doctor performed often. He inserted the needle and gently pushed the plunger as the patient closed her eyes and appeared to drift into a light sleep. Visibly relieved the doctor removed the needle, lay down the syringe and leaned towards her. “It’s all right, Martha, you can get up now.” Her eyes opened, she smiled at us, and thanked me for coming so far out if my way to help her.
Another surprise awaited me; the doctor suggested the three of us have lunch together. We walked to a nearby bistro, and over a meal paid for by Merrell I spent an hour in the company of two friendly, apparently normal people. Over lunch the doctor explained to me that the alcohol and drug detox clinic adjoining the homeless center used Frenquel often to help “bring down” people in drug withdrawal.
On the flight back to Cincinnati, I wrote up my “trip report” explaining I had found two “off-label” novel uses for Frenquel: to calm someone who, most likely, had a borderline personality, and to facilitate drug or alcohol withdrawal. I didn’t suggest Merrell pursue research into these potential new indications, but perhaps I was wrong. New uses for old drugs are often discovered by chance; looking for one thing and finding another. It’s called serendipity. On the other hand, it seemed more likely that everything attributed to Frenquel might be due to suggestion, the placebo response, or spontaneous remission.”
I did not state the obvious – that Frenquel clearly had mild sedative and calming properties but certainly not sufficient to justify the rigors of a controlled study in a market already including meprobamate and the first benzodiazepines. Nor were Alertonic and Frenquel a worthy match for lithium in the effort it would take to prove they were effective remedies for a specific problem.
Finally, we come to the saddest part of this tale – the extent to which scientific disagreements can degenerate into strident squabbles. Almost twenty years after our Lancet article, Michael Shepherd asked me to review the book, “The History of Lithium Therapy” (F.N. Johnson, Macmillan Press: 1984). It was published in Psychological Medicine the following year. The author, an academic psychologist, had authored three previous texts on lithium and claimed Schou and Cade as his friends. In unrestrained hyperbole, verging on the ludicrous, he endorses the enthusiasts who see lithium as “the King of drugs” responsible for the “third revolution in psychiatry”. The following quotations illustrate the polemical nature of the book. Lithium is being taken by “one person in every two thousand in most civilized countries” because “depression (sic) is a crippling condition”. Lithium alone triggered the chemical revolution in psychiatry; “At a stroke, the elusive ethereal Freudian psyche was replaced as the primary object of attention in psychiatry by the polyphasic, physic-chemical system called the brain.” Lithium, “like no other single event, led to psychiatry becoming truly interdisciplinary.” Its ubiquitous use “suggests a new basis for classification of psychopathological states.” And it is so cheap and easy to administer it will “transform health care in underdeveloped countries.”
These absurd claims provoked me to satire and to ending my review by suggesting that those who might buy the book would be those who shared the author’s view that lithium was the “Cinderella of psychopharmacology” and who wished to have an unabridged version of the fairy tale at their fingertips. These comments were, in part, a reprise of a lively debate between Nate Kline and me in the correspondence columns of the American Journal of Psychiatry.
The final irony is that this book was published shortly before the two definitive controlled studies (referred to previously) finally arrived at an accurate scientific demonstration of the specific and fairly modest benefits of lithium and imipramine in preventing recurrences of bipolar and unipolar disorders, respectively.
Some reservations about the impact of unbridled enthusiasm for prophylactic treatment have been expressed from the scientific sector. Paul Grof notes that the use of prophylactic treatment for “nearly everyone with recurrent affective disorders has led to the point that the natural history of affective disorder the illness is not known anymore. He also notes that with the extensive use of lithium “the concept of affective disorders has dramatically broadened and mood symptoms, rather than comprehensively assessed psychopathology have become the center of psychiatry assessment.” (Grof 1998).It is worth adding that the parsimony of the DSM system has colluded in this outcome.
What can we make of all this today? To begin with, the testing of new psychotropic drugs has passed almost entirely out of the hands of academic clinicians and federally funded projects and into the realm of the pharmaceutical industry and subcontracted commercial companies who, while they adhere to FDA minimal requirements for controlled studies, have adopted other dubious ways to degrade the process and bias the outcomes. We have also learned that even the best of controlled double blind studies may not mirror or predict what happens in real worldeffectiveness. I would gladly return to the time when experienced dedicated clinicians like Mogens Schou did the very best they could, however imperfectly, to show us what works in real practice. After all, their original study was really an “effectiveness” one and not a controlled scientific evaluation. And Schou was, after all, correct. But perhaps MogensSchou’s legacy is better served by the recognition that his truly innovative contribution was the concept of “prophylaxis” itself and not the agents used to accomplish it. This was the very fact that relentlessly recurrent episodes of affective disorder could be checked by continuous, rather than episodic treatment, a technique that also suppressed the phenomenon of kindling.
Now we come to the most tantalizing question raised by this autopsy. Suppose that each of us, Schou, Shepherd, Blackwell and Grof are double blind neuroscientists groping the same elephant. That prophylaxis of recurrent affective disorders is Schou’s reality- the body, but that lithium is not a panacea for all its forms (Blackwell and Shepherd)- the tail, and that more scrupulous analysis of the phenomenology, genetics and neurochemistry might reveal which subtypes respond specifically to lithium, imipramine or valproic acid (Grof)- the head. This is a puzzle beyond the capacity of DSM 5 or contemporary trial methodology to solve; worse still, all three compounds are orphan drugs – either un-patentable or generic, so that support for research is unlikely unless the national or federal funding agencies in Britain and America reverse course and revive clinical psychopharmacology research.
At the same time, claims that exceed the level of proof available in efficacy or effectiveness studies should always be challenged and those who exaggerate them beyond belief are free game for Anglo Saxon satire. Mea culpa!
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June 19, 2014