Research as a Discipline

    When one takes up research as a professional activity one dedicates oneself, for the time being and while in that field, to the pursuit of truth. To be sure, however one tries, one is myopic or astigmatic by constitution, blinkered by past indoctrina­tions, perhaps even suffering from some form of hysterical amblyopia. But one can refrain from putting on the distorting spectacles on offer or try the effect of taking off the pair one normally wears and has grown used to. In sciences concerned with soft data and subjectively toned observations, blind techniques are helpful but are not enough. It is necessary to aim at being unbiased, to lean against rather than towards the motivations by which one is impelled. A conscious effort of mind and a lasting self‑discipline are called for. Those who are not prepared to try are a danger, and they would be better placed in fields in which uncritical enthusiasm brings the rewards. In his spare time the research worker should feel free to campaign and to crusade. When he turns to his professional task, figuratively or in fact, he should put on his white coat. While he wears that coat, he must accept the findings his work brings him, regardless of his preconceptions. Given a chance, he should put those preconceptions on trial by setting up the experiment or starting the enquiry which would seem to have the best chance of disproving them. Genuine observations, which bear the various hall‑marks of authenticity, must be received dispassionately and handled with respect, whether they come from his own work or from that of others, whether they tend to support or to rebut the working hypotheses which he uses as his tools. Above all, he must not identify himself with the results of his work or with the hypotheses to which they give rise. His loyalty to his brain‑children must be of a strictly limited kind, and go no further than seeing that they are given the chance of a fair fight when they come in conflict with others.

     I have tried to live up to these standards, when I remembered; I have tried to abandon the disproved hypothesis with a good grace, when it became untenable. When our Unit went out to get the results of a follow‑up of twin subjects of "hysteria," I confidently expected that positive concordances would emerge, higher in the MZ than in the DZ pairs. When quite different results came in, I imagine I was disappointed and I can remember feeling very perplexed. New ideas had to be taken into account; and I had to think the thing through from the ground up, to the point where I doubted the very existence of a hysterical syndrome (or reaction type, or personality type). It was painful. It meant I had to go back on ideas I had published, and had, for instance, to re‑write a section on "hysteria" in the textbook of psychiatry of which I was part author. It was a nolte face as uncomfortable and as invigorating as when a growing acquaintance with German phenomenological teaching drove me out of the comfortable school of Adolf Meyer.

    Not to be willing to give up old ideas when the evidence is produced which shows they have to be modified, is the sin against the light, not only for research workers though for them above all. Soon after the Tienari (1963) results came out, showing a zero concordance rate in the MZ co‑twins of schizophrenics, a colleague with a background in the social aspects of psychiatry remarked, "You know, all of us at the X Hospital, when we saw those results, just whooped for joy!"

    Perhaps it is not waste of time to consider the implications of this remark. The speaker had presumably adopted a sociogenic or psychogenic or at least environmental theory of the causation of schizophrenia and for a number of years had been aware of but had refused to accept the results of family and twin research in schizophrenia. These results had obviously not been considered on their merits but had been reacted to emotionally and had been felt as in some way hostile to the accepted environmental theory. This could only have been because the genetical results were not understood, since, if understood, they would have been felt to be complementary rather than contradictory. One can also conclude that the environmental theory had been accepted as some kind of a credo, accepted with passion, identified with high aims and ideals, and given an unquestioning loyalty. This could only have been because the environmental hypothesis itself had never been looked at with understanding, since all theories of causation are ethically indifferent. The mental set that resulted meant that no evidence could be considered on its merits, but valued only in so far as it tended to confirm already accepted ideas. When Tienari came along with a piece of evidence which confirmed those ideas, the conclusion was at once drawn that all the genetical work that had gone before was now disproved. A warm surge of certainties confirmed flooded the sys­tem, and the soul sang for joy.

    Tienari's results compelled others, including myself, to reconsider our positions; but I think we were able to do so without any very extravagant emotional reaction. This is the nub of the matter. It is a pity to be blinded by emotion; but it is the wilful self‑blinding which causes so much of the avoidable difficulties against which workers in such fields as psychiatry and behavioural genetics have to pit themselves. It is indeed necessary to take up a position, for argument's sake, or to have a point of departure for further work. But such positions are necessities of convenience and should claim no loyalty. We must not weep when we are forcibly moved on, or compelled to retreat.

    A primary requirement for good clinical work with patients is the working hypothesis that one knows the answers. Until one has convinced oneself of that, one can hardly make a beginning with treatment, or with settling any number of other practical issues. Over the years the good clinician, becoming more and more expe­rienced and skilful, gets more and more sure of himself, so that in the end he can look around his arena with sublime wisdom and certainty. For research work, the requisite working hypothesis is that one doesn't know the answers, but that, if one can only succeed in putting the right questions, some answer may emerge. Over the years one comes to learn a certain humility; if one begins to doubt some of the clinician's certainties, it is not because one is at all sure that one has anything more certainly true to put in their place.

    Speaking for myself, I like a monogenic theory for schizophrenia. It provides me with the kind of tool I like to handle. Wherever you start digging with it, it turns up questions, in family psychiatry, social psychiatry, epidemiology, just as much as, say, in chemical pathology. Burch's (1964) plurigenic theory does not appeal to me at all. I cannot use it heuristically, and I don't see how anyone else can. Perhaps one day a team of immunologists will come along with a demonstration of auto‑immune processes actually going on in schizophrenics; and then the theory will be on another footing. I guess that the polygenic theory of schizophrenia, favoured by my editors (Gottesman and Shields, 1967), appeals particularly to them because it fits in naturally with established ways of thinking, and is not merely a remarkably success­ful explanatory hypothesis, but also a good working tool. I would think that it must be preferred by psychologists and social scientists, while a monogenic theory would have more appeal for doctors, pathologists, chemists, and straight geneticists. This is small comfort for me, as doctors, pathologists, etc., usually run as hard as they can when schizophrenia looms over the horizon.

    It seems to me that genetical theories have an essential part to play in the understanding of schizophrenia. Even if one is mainly interested in, say, family dynamics, problems become easier to handle if one is prepared to allow some impor­tance to the genotype. Nearly all the socially and psycho dynamically interested schizophrenia workers (notably Alanen 1966, Kringlen 1967, Tienari 1963) have convinced themselves that there is a genctical aspect to causation, even if that is not the aspect to which they wish to devote their own endeavours.

     I have written this as if I thought that the working hypothesis one adopts is determined solely by one's past learning and one's temperament. This is, of course, only half true. As new facts emerge, one does get driven from hypothesis to hypoth­esis. It is my belief that the genetical facts, in their multiplicity and their systematic order, are now too powerful to be resisted by an open‑minded psychiatrist; the strongholds of the pan‑psychic and purely environmental theories are no longer defensible.

     If we turn now to manic‑depression, the situation is rather different, and has not advanced so far. Monogenic theories are beginning to look increasingly improbable (though they cannot be excluded for a part of the range of affective psychoses); it is polygenic theories that would seem to be the best bet. But they have to be compli­cated by making a much larger allowance for heterogeneity of the clinical material than is necessary in the case of schizophrenia. Maybe there are affective disorders, say the "neurotic" or "reactive depressions," in which genetical variance contributes very little to causation, or symptomatology, or course, or treatment susceptibili­ties. But we can be reasonably sure that over the greater part of the range of the affective disorders, genetical factors play a significant role.