At the end of this long and complicated journey, the time has come for me to revisit the obstacles I felt I needed to circumvent for the purposes of this research. Throughout this task, I have prioritized the resolution of certain scientific problems and have focused on trying to understand the real in the light of questions of disciplinary adherence or of scientific identity. I have attempted to resolve a certain number of problems, to rework them and, most importantly, to make links between them even though they are or were initially formulated, worked on and discussed in very different sectors of the great continent of human and social sciences, and by very different communities of researchers. In order to quietly resolve such problems, I needed to prioritize the basic task and avoid the distractions and dilution of too many extraneous activities. This even meant, to the possible displeasure of the administrations governing research who swear and judge solely on the number of articles published, refraining from the compulsive production of any such articles.1 ‘To keep oneself apart, take one’s time, become silent, become slow’ – such is the wise programme already advocated by Nietzsche in his preface to Daybreak, a programme which, more than ever, should be an inspiration to researchers.
From this point of view, the story of how the British mathematician Andrew Wiles came to solve Fermat’s last theorem should be reflected on and taught across all scientific networks, including those of the human and social sciences. Convinced that it was possible to solve a problem that the mathematical world regarded as insoluble, he was obliged to withdraw from his field and invent a whole series of strategies in order to work patiently, if somewhat stubbornly, in peace:
Wiles abandoned any work which was not directly relevant to proving Fermat’s last theorem and stopped attending the never-ending round of conferences and colloquia. Because he still had responsibilities in the Princeton Mathematics Department, Wiles continued to attend seminars, lecture to undergraduates and give tutorials. Whenever possible he would avoid the distractions of being a faculty member by working at home where he could retreat into his attic study.2
What his story demonstrates in particular is the fact that all too often collaborative work is confused with ‘collaborative gatherings’ (debates or scientific dialogues, interpersonal dialogues, seminars, conferences, joint publications). In reality, collaborative work is essentially everything that the researcher focuses on and mobilizes in order to solve the problems he or she has identified. So, for example, in order to develop a new argument, Wiles found himself drawing on very different fields of mathematics, and on work produced by other people. Sometimes interpersonal dialogue, dialogue between highly competent researchers or some simple advice on some appropriate reading matter, can boost the creative process, help to clarify thinking, produce flashes of inspiration or enable a proof to be demonstrated. Nevertheless, without the ground work, often conducted in solitude but supported by results from a gradual accumulation of work, too much discussion can result in the dilution and dispersion of focus.
During the whole course of this research, and with increasing intensity as the programme broadened its scope, I have reflected on the legitimacy of the steps I was taking. In effect, the logic of my investigations took me to periods of history and areas of knowledge which are regarded as being outside the realm of sociology. The only justification, in my view, for this profusion of sources of knowledge was the interest and the significance of the questions that this enabled me to cover and the sense that they were essential to my purposes. For want of being able to master all these domains in the manner of a specialist, I have always been careful to prioritize the work of researchers who are the true specialists of these domains and these eras.
The fields of research I have explored range from the political and cultural anthropology of stateless societies to art history, taking in Assyriology and the analysis of the first forms of the State in Mesopotamia, the history of Indo-European societies, the cultural history of ancient Greece, medieval history (and particularly that of sacramental theology), theological-political history, the history of religions and of the sacred and even the history of fakes and forgers. From a theoretical point of view, my research has included philosophical, historical, anthropological or sociological reflections on the weight of objectivized history, the anthropological theory of magic, the theory of secularization, theories of domination and of power, the theory of speech acts, the theory of the rites of institution and of legitimacy, theories of belief or of believing, the economic theory of value, aesthetic theories and even the study of the social life of objects and their biographies, all of which, to some extent or other, have been useful to my thinking. I need hardly add that all these references arise from a necessary series of interrogations – one thing leading on to another – and not from a programme of reading I had established in advance. If, by some chance or other, I had stumbled upon such a list before beginning my work, I would certainly have been utterly overwhelmed by the sheer scale of the task and very dubious about the possibility of ever completing it.
This crossing of domains and theoretical universes which requires time and investment not easily compatible with the objective of getting articles published, is not especially encouraged in the current climate of the social sciences. These sciences, which are becoming increasingly specialized, objectively play a role only rarely admitted and which, in a complex and highly differentiated society, involve throwing light on parts of the social world that the vast majority of readers have little or no knowledge of. So, for example, the ethnologist, the sociologist or the political scientist enable us to penetrate into the heart of political parties, of the financial world or the world of crack dealers, and plunge us into the depths of sports clubs, educational institutions, working-class or bourgeois areas, in this way bringing some answers to the legitimate need and simple curiosity to know ‘what is happening’ and ‘how it is happening’ in any given place or social sector. And the more esoteric the sector (law, science, finance, religion, etc.), the more the researcher needs to exhaust his or her talents in describing and explaining such complex activities.
At a time when investigative journalists have become an increasingly rare breed, the social sciences have taken over the tasks of investigating and gathering information about the various parts of the world, tasks which bear some resemblance to the glory days of great journalistic investigations. ‘Super-journalists’, in the words of Robert Ezra Park, former journalist and sociologist and founder of the first Chicago School, they help us explore different areas of the social world and can also, in their critical capacity, put current events into their political and media context in order to reveal the illusions and fantasies lurking in their depths.
But by dint of focusing on the study of sectors of the social world and of paying close attention to the practices and social representations of individuals, whether in a school, in a particular family or area, in a library or in the rooms of a museum, there is the risk of reducing the investigation to a sort of social phenomenology or monography which, though detailed in its descriptions of the habits, ‘motivations’ and social representations of the individuals concerned, nevertheless prevents the more crucial questions being asked. Questions like, What is school? The family? Sport? The institution of the library? The nature of the Museum? etc. And yet answering such questions usually involves pondering where these realities come from (their evolution) and how they link to others (their place and meaning in the overall picture).
Of course, it is clearly preferable that the task of describing specific milieus or groups be carried out by rigorous researchers relying on empirical data produced and collected under strict control, rather than by essayists or investigators with little time, who are more inclined to give a subjective view of reality rather than an objective one. But when ambition stops there, it seems to me that researchers are failing to fully live up to their profession. In certain cases, we can even get the impression that the research simply provides knowledge that would be useful to any individual wishing to gain access to the universe studied. By describing the logics of actors from specific sectors, researchers lose sight of any broader, more general or deeper perspective on the social world. What does that reveal about the structures of this world or about its most frequently recurring mechanisms? How do the universes of our present behaviour link to structures which have sometimes formed over a very long timescale?
Clear links can be made between a certain objective victory in terms of the style of sociological work typical of the Chicago School, with its pragmatism, its theoretical discretion and its propensity for meticulously studied cases, and the present state of the discipline. In the sociology of the arts or of culture, for example, empirical studies on visitors to museums, libraries, cinemas or festivals, on their behaviour during their visits, the reasons behind their presence there, their perceptions, etc., focus on too small a part of a much greater issue and hinder any more general understanding of the social issues inherent in these different institutions. Implicitly or explicitly, such studies meet the expectations of the cultural institutions concerned, where desire for knowledge is confined by the limitations of their aims and their actions. Being better informed may indeed mean being able to adapt their offer, by improving the signage in the museum or library, or by using suitably adapted publicity strategies to attract new visitors, but this positivist knowledge is ultimately not scientifically satisfying. In such cases we may well wonder if sociology is doing any more than providing marketing services aimed at a better understanding of consumers and what motivates them. I am not really sure. It is, in any case, no longer in a position to understand, for example, the nature of the institution as an entity and how institutions of learning and culture such as libraries, theatres, concert halls or museums silently contribute to the separation of the profane and the sacred and are themselves linked to the manifestations of domination in our hierarchized societies.3
It seems to me that the most autonomous researchers in social science have always combined lofty intellectual ambitions, which could sometimes appear metaphysical, with the desire to support their ideas with proofs. This is in any case what has contributed to the strength and the interest of sociological work carried out by Durkheim, Weber, Mauss, Elias or Bourdieu. Some may insist that these are now figures of the past, but it seems to me clear that this kind of reference to a supposedly bygone past is usually the sign of a show of strength and a blatant wish to ‘move on’.
Throughout the history of the social sciences, all those who have constructed the broader programmes which necessitate crossing the disciplinary barriers and frontiers marking out areas of speciality, or reaching beyond theoretical boundaries, have run the risk of being criticized by those whose knowledge is limited in scope but erudite. The problem is aptly summed up by Marcel Gauchet when he writes: ‘The dilemma of the “specialist”, and I should like to know which wise judges would ever be able to resolve it: the solution to your problem is outside your field, but the laws of the academic tribe forbid your leaving it. You must choose between frustration or censure.’4
Thus, even in 1933, A.O. Lovejoy, the great historian of ideas who brought us his magnificent synthesis of the history of the conception of a ‘great chain of being’ was already outlining the potential difficulties of any attempt to think on a more ambitious scale:
Precisely because it aims at interpretation and unification and seeks to correlate things which often are not on the surface connected, it may easily degenerate into a species of merely imaginative historical generalization and because the historian of an idea is compelled by the nature of his enterprise to gather material from several fields of knowledge, he is inevitably, in at least some parts of his synthesis, liable to the errors that lie in wait for the non-specialist. I can only say that I am not unmindful of these dangers and have done what I could to avoid them; it would be too sanguine to suppose that I have in all cases succeeded in doing so. In spite of the probability, or perhaps the certainty, of partial failure, the enterprise seems worth attempting.5
In spite of the obstacles, Lovejoy suggests that specialization and the division of labour can be corrected by research which cuts across the different domains. In his case, the distribution of specialities by domain, country or language was particularly disastrous. Being a specialist in English literature or in German literature, being a specialist in literature, religion, politics, science or philosophy means accepting that the political or institutional limits of knowledge are fixed, whereas in fact schema, beliefs, tastes or intellectual habits do not stop at disciplinary frontiers. The history of ideas is not an activity for ‘highly departmentalized minds’.6
In the same way, and with a strong dose of irony, Georges Dumezil described his own difficulties with the specialists on the Roman era:
Someone who has worked exclusively in Roman literature and history, Roman archaeology, forms a particular idea, based on whatever elements he or she has to hand. In such circumstances the idea that India or Ireland could provide some element of explanation about the origins of Rome is a shocking one. And it is not a matter of lazy thinking, but because they are so comfortably ensconced in their cocoons that any beams of light from outside hurt their eyes. And it is the same thing for most areas […] The comparatist is always less well armed in each of the domains he studies than the person who deals exclusively with that domain, the specialist. There is always the possibility of being caught red-handed: ‘You haven’t used the right edition! You seem unaware of an illustrious discussion which took place fifty years ago.’ Well yes! But we have found something else.7
The historian pleads the cause in support of a comparative approach as the only one capable of capturing the relatively unchanging structures which escape the somewhat short-sighted gaze of the specialists of an area of civilization or of an era.
But in my own case, it was reading the work of the English anthropologist Jack Goody that rocked my beliefs as a specialized researcher. In the introduction to his magnificent work on the cognitive and organizational effects of the written word, Goody also felt the need to justify himself before the court of the specialists for fear of being declared unqualified:
I know too that I have trespassed on the well-cultivated gardens of other scholars, classicists, orientalists, psychologists, linguists and others, without having the comprehensive understanding of their subjects which they would expect of one another. It would be futile to protest that others have plundered the rougher pastures of social anthropology for just the same ends. I would rather rest my justification on the need to cross these disciplinary boundaries if anything is to be made of the comparative study of human behaviour.8
How could such a prolific scholar, a researcher whose ideas have shaken up our knowledge of societies, find himself apologizing for ignoring the need for specialization when no specialist has ever been capable of producing the level of knowledge he has attained?
History seems thus to repeat itself, generation after generation, and in conclusion it will be observed that Pierre Bourdieu ended up adding his voice to those of Lovejoy, Dumézil and Goody on the negative effects of an excessive division of scientific work. Long suspicious of broader perspectives of history and of long-term history which he saw as the place of a reprehensible ‘philosophy of history’, in his lecture course on the State, the philosopher found himself castigating the positivist vision of research which means that the only questions asked are those that can be answered with an immediate empirical proof:
The positivist representation of science that almost requires scientists never to propose anything that they cannot immediately demonstrate exercises a terrifying effect of castration and mutilation on the mind. One of the functions of science is also to conduct research programmes perceived as almost unrealizable; programmes of this kind have the effect of showing how research programmes viewed as scientific because realizable are not necessarily scientific. In positivist resignation, instead of seeking the truth where it lies, people look for it under the street lamp where they can see it.9
And in the same way, he attacks the deleterious effects of the specialization of disciplines and their internal fragmentation into so many different sectors of knowledge, defending himself in advance for the ‘mistakes’ that the non-specialist is likely to make.
Discredit cast onto the most ambitious research attempts, which come with the growing specialization of scientific domains, immediately rules out any larger scale investigation and any even slightly wider questioning process, ultimately preventing any possibility of putting objects into perspective and any hope of challenging those things most often taken for granted. Yet the observations I have cited show that it is high time to take a new look at work scorned as ‘second-hand work’. The blind defence of ‘first-hand work’ in which researchers comment on and discuss data that they have generated and nothing more than that, represents a major problem for the social sciences. Only limited objects, which can be empirically understood by any competent researcher are deemed worthy of interest. And yet the process of also supporting arguments by a critical re-reading of the empirical work carried out by others is exactly what the great founders of our discipline did.
Jean-Claude Passeron is, to my mind, a little too restrictive in signalling Weber as an exception in the scientific landscape of social sciences: ‘Weber’, he writes, ‘is one of the rare examples of the rich potential of “second-hand” in constructing a theory capable of retaining the attention of the relevant specialists.’10 It seems to me, however, that this applies just as well to Karl Marx, Émile Durkheim, Marcel Mauss, Fernand Braudel, Norbert Elias, Georges Dumézil, Claude Lévi-Strauss, Jack Goody or Pierre Bourdieu, to mention just these few by no means negligible names. There is often a tendency to confuse essays which are purely theoretical and which do not base themselves on an existing empirical work in order to put forward a certain number of theories, with ‘second-hand’ studies which take pains to base themselves only on empirical work of indisputable reliability, but which are still capable of developing more wide-ranging visions than if they were based on monographic or ‘first-hand’ case studies as the only legitimate and valid form of uncovering the truth.