Early inroads into the absoluteness and dogmatism of positivist science were made by a pair of eminent physicists, Werner Heisenberg (1901- 76) and Niels Bohr (1885-1962).
Heisenberg, a German scientist, is one of the founders of ‘quantum theory’. He articulates an ‘uncertainty principle’ which well and truly calls into question positivist science’s claims to certitude and objectivity. According to Heisenberg’s principle, it is impossible to determine both the position and momentum of a subatomic particle (an electron, for instance) with any real accuracy. Not only does this preclude the ability to predict a future state with certainty but it suggests that the observed particle is altered in the very act of its being observed, thus challenging the notion that observer and observed are independent. This principle has the effect of turning the laws of physics into relative statements and to some degree into subjective perceptions rather than an expression of objective certainties.
Bohr, a Dane, received the 1922 Nobel Prize in Physics for his work on the structure of the atom. Like Heisenberg, Bohr is concerned with uncertainty but he has a different view about the nature of the uncertainty in question. Heisenberg’s argument is epistemological: in pointing to science’s inability to determine subatomic dynamics with accuracy, he locates this limitation in the very way in which we humans know what we know. For Bohr, however, the limitation is ontological rather than epistemological: it is due not to how humans know but to how subatomic particles are. In fine, these particles need to be seen as a kind of reality different from the reality we are used to dealing with. In thinking or talking about them, we need a new set of concepts. We cannot simply take classical concepts like position and momentum and apply them with accuracy to particles. The traditional concepts may, of course, be the best we have, and we may have no alternative but to make do with them. Yet, we should not succumb too easily to the tyranny of prevailing concepts. Bohr urges us to complement their use with other kinds of description that offer a different frame for our considerations. However successful we may be in doing that, the essentially ambiguous character of human knowledge, including scientific knowledge, cannot be sidestepped, as Bohr’s whole discussion underlines very cogendy.
The impact of Heisenberg’s and Bohr’s thought has been far- reaching. These scientists sound a note of uncertainty within what has been a very self-confident philosophy of positivist science. That note comes to echo even more loudly as other thinkers begin to address similar issues within science.
One of the factors prompting this concern with epistemology and the philosophy of science has been the recognition that a contradiction exists in scientific practice. There is a chasm between what science purports to do and what it actually does. For all the positivist concern that statements be verified by observation before being accepted as meaningful, a host of elaborate scientific theories have emerged whose development clearly requires the acceptance of much more than direct conclusions from sense-data. Many of the so-called ‘facts’ that serve as elements of these theories are not direcdy observed at all. Instead, they have been quite purposefully contrived and introduced as mere heuristic and explanatory devices. This is true of alleged ‘entities’ such as particles, waves and fields. Scientists act as if these exist and function in the way they postulate and, in terms of their purposes, this may prove an effective way to proceed. In this situation, it is very easy to go on to reify4 these presumptions. Yet, by positivism’s own criteria, such reification is unjustified.
What is emerging in this line of thought is the picture of scientists actively constructing scientific knowledge rather than passively noting laws that are found in nature. This has clear implications for the status that scientific knowledge deserves to have ascribed to it. Many thinkers —philosophers or scientists, or both—have not been slow to point out these implications.
1. POPPER’S PRINCIPLE OF FALSIFICATION
Sir Karl Popper (1902-94) was bom in Vienna. In the 1930s, like so many other figures we are considering here, he was forced by Nazism’s advent to power to quit his native land. After a brief period in England, he spent the years of World War II in New Zealand, returning to England in 1946 and serving as a professor at the London School of Economics from 1949 to 1969.
Popper is interested in the philosophical and political implications of genuinely scientific work. He contrasts scientific work with what is done in the ‘pseudo-sciences’ and tries to draw a clear line of demarcation between the two. His early ideas are found in The Logic of Scientific Discovery and The Open Society and Its Enemies. Later works include Objective Knowledge: An Evolutionary Approach and The Self and Its Brain, the latter coauthored with J.C. Eccles.
Despite early association with the Vienna Circle, Popper offers a view of human knowledge very different from that of logical positivism. Not for him any limiting of valid knowledge to statements capable of empirical verification. How, then, does he see scientific knowledge being established? We find a clue to that in the tide of yet another of his books, Conjectures and Refutations: The Growth of Scientific Knowledge. Instead of scientists proceeding by way of observation and experimentation, thereby pinpointing scientific laws evident in nature itself, Popper sees them engaging in a continual process of conjecture and falsification. An advance in science is not a matter of scientists making a discovery and then proving it to be right. It is a matter of scientists making a guess and then finding themselves unable to prove the guess wrong, despite strenuous efforts to do so.
In putting this position forward, Popper is taking issue with the scientific method as it has been traditionally understood. In fact, he is challenging one of its pivotal notions. He is confronting head on the role that scientific method ascribes to induction. Induction is the process whereby a general law is established by accumulating particular instances. For example, because scientists find time and time again that water boils at 100°C, at least under certain definable conditions, they have felt confident in ascribing to this ‘fact’ the status of a universal law of physics. Not everyone has shared their confidence. Eighteenth-century philosopher David Hume characterised that confidence as a matter of psychology but not an outcome of logic. We might boil water a thousand times and find in every case that it boils at 100°C; but in Hume’s view this provides no logical justification for the belief that it must always boil at 100°C. To assume that it must is to assume a world in which the regularities we perceive today will remain unchanged in the future. That is an assumption, not an empirically established truth. A number of later philosophers, Bertrand Russell and CD. Broad among them, side with Hume in this, seeing induction as very much the weak link in the chain of empiricist science. Scientists may be as empirical as they like in their observations and experiments; yet they must reckon with the consideration—an unpalatable consideration, perhaps—that a non- empirical logical principle remains intrinsic to scientific method.
Popper’s solution to this impasse is to substitute falsification for verification at the heart of scientific method. No matter how many examples we muster in support of a general principle, we are unable, logically, to prove it true in absolute terms; yet it takes only one example at variance with a general law to prove, logically and in absolute terms, that it is false. So Popper believes that, in engaging in observation and experiment, scientists are called upon not to prove a theory (they can never do that) but to try to prove it wrong.
For the Baconian understanding of science as an inductive process Popper has substituted the idea of science as hypothetico-deductive. Scientific method is like this: (a) scientific theories are proposed hypothetically; (b) propositions are deduced from these theories; and (c) the propositions are then tested, that is, every effort is made to prove them false. It is this falsifiability that sets scientific claims apart from non-scientific or pseudo-scientific claims. A theory or hypothesis not open to refutation by observation and experiment cannot be regarded as scientific. With this goal of falsification in view, Popper recommends that all scientific theories be presented as clearly as possible so as to lay them wide open to refutation.
It is only when propositions deduced from scientific theory have survived every attempt to refute them that the theory can be provisionally accepted as true. Here the operative word is ‘provisionally’. The conviction that no theory can ever be definitively accepted as true lies at the heart of Popper’s philosophy. As he put it (1959, p. 280), ‘every scientific statement must remain tentative for ever’.
All this evinces a very different picture of science, and of the scientist, from the one we find at large among the positivists.
First, in the search for scientific truth, there is a place for guesswork, intuition, the following up of ‘hunches’. Not for Popper the image of the scientist as the detached observer of nature. In fact, he does not believe such disinterested observation is possible. Observation takes place within the context of theory and is always shaped by theory. All our observing is done within a horizon of expectations and is therefore necessarily selective.
Second, on Popper’s accounting, what is put forward as scientific truth turns out to be, not something shown to be true, but simply something that scientists have so far been unable to prove false. This turns scientific truths into merely provisional statements. ‘Our science’, warns Popper (1959, p. 278), ‘is not knowledge (episteme): it can never claim to have attained truth, or even a substitute for it, such as probability’.
Science is not a system of certain, or well-established, statements; nor is it a system which steadily advances towards a state of finality …
The old scientific ideal of episteme—of absolutely certain, demonstrable knowledge—has proved to be an idol… It may indeed be corroborated, but every corroboration is relative to other statements which, again, are tentative. Only in our subjective experiences of conviction, in our subjective faith, can we be ‘absolutely certain’ …
Science never pursues the illusory aim of making its answers final, or even probable. Its advance is, rather, towards the infinite yet attainable aim of ever discovering new, deeper, and more general problems, and of subjecting its ever tentative answers to ever renewed and ever more rigorous tests. (Popper 1959, pp. 278, 280, 281)
On that accounting, Olympian dogmatism would seem entirely out of place among Popperian scientists. One would expect of scientists, instead, a large measure of tentativeness, perhaps even a measure of humility.
Where does one find these Popperian scientists? There are humble scientists, to be sure, and scientists often put their hypotheses forward quite tentatively in the first place. Still, on the whole they do seem to be looking for verification rather than falsification, and the observer of the scientific scene is hard put to find any widespread and impassioned effort to prove scientific theories wrong. This is particularly true of the broader, more fundamental, realm of theory. This is rarely called into question. Even in the face of conflicting evidence scientists only too often cling to theory in a quite determined fashion. Obviously, and unsurprisingly, it takes more than falsification to break scientists loose from what they have known and experienced as the very matrix of their thought and practice. Achieving that, some would want to say, takes nothing short of revolution.
2. KUHN’S ‘SCIENTIFIC REVOLUTIONS’
Possibly the most influential book in modern-day philosophy of science is The Structure of Scientific Revolutions.
The ideas contained in this book were developed by Thomas Kuhn (1922-96) while he was a graduate student in theoretical physics at Harvard University. What provided the impetus and starting point for this work was an invitation Kuhn received from University President James B. Conant to do some lecturing in science. The course in question was for undergraduates majoring in the humanities and it was put to Kuhn that he should take an historical perspective. So he turned to the history of science to see what lessons it might hold for scientists today.
This is new territory for Kuhn and the lessons he comes to glean from history are not of the kind he has been anticipating. Led back to Aristode’s Physics, he is struck forcefully by what he sees as an utter disparity between Aristotelian physics and the physics of Newton. Not a difference of degree but a difference of kind. Not inchoate, less-formed notions in Aristotle that are later to be developed and brought to fruition in Newton. No, these two sets of ideas appear to him so different as to be incomparable. As Kuhn sees it, Aristotle and Newton do not stand at different points on a continuum; they are not even within the same spectrum.
Accordingly, Kuhn concludes, the thought of Newton cannot have grown and developed out of the thought of Aristotle. At some point, the basis and essential elements of Aristotelian physics must have been jettisoned and replaced by a whole new way of seeing things. There has to have been a revolution in scientific thinking.
It is this insight that leads Kuhn to the thesis he develops in The Structure of Scientific Revolutions. There, and elsewhere, he takes a much more historical and sociological perspective than philosophers of science before him. He begins by looking direcdy at scientists and what they do, whether they be scientists of the past or scientists of the present. Where Popper’s philosophising and his focus on logic lead him to see scientists and the process of scientific research in terms of what they ought to be rather than what they are, Kuhn’s starting point leads him at once to question the alleged objectivity and value-free neutrality of scientific discovery.
What Kuhn never ceases to emphasise is that scientists do their work in and out of a background of theory. This theory comprises a unitary package of beliefs about science and scientific knowledge. It is this set of beliefs that Kuhn calls a paradigm. It is an overarching conceptual construct, a particular way in which scientists make sense of the world or some segment of the world.
For scientists in general, the prevailing paradigm is the matrix that shapes the reality to be studied and legitimates the methodology and methods whereby it can be studied. More than that, the prevailing paradigm is quite simply taken for granted within the contemporary scientific ethos. Any challenges that are mounted tend, at the start at least, to be dismissed out of hand. Normal science, Kuhn says, ‘often suppresses fundamental novelties because they are necessarily subversive of its basic commitments’ (1970, p. 5). Thus, the paradigm establishes the parameters and sets the boundaries for scientific research and, in the ordinary course of events, scientific inquiry is carried out stricdy in line with it. At most, scientists will attempt to solve problems in ways that refine the paradigm and extend its scope. Even Popperian science, fiercely focused as it is on refuting the alleged findings of science, takes place in accordance with the dictates of the ruling paradigm. Such science—science in keeping with the paradigm of the day—is what Kuhn is calling ‘normal science’. He sees it as a ‘sort of puzzle-solving activity in which … most physical scientists are normally engaged’ (1977, pp. 221-2). As he puts it, ‘normal research, even the best of it, is a highly convergent activity based firmly upon a setded consensus acquired from scientific education and reinforced by subsequent life in the profession’ (1977, p. 227). Kuhn goes so far as to characterise normal science as ‘a complex and consuming mopping up operation’ (1977, p. 188). It ‘aims to elucidate the scientific tradition in which [the scientist] was raised rather than to change it’ (1977, p. 234).
There comes a time, however, when the paradigm proves inadequate. Findings are proposed that cannot be explained within the context of the paradigm that prevails. When anomalies like this arise, ‘nature has somehow violated the paradigm-induced expectations that govern normal science’ (Kuhn 1970, pp. 52-3). It is a time of crisis. New findings are being put forward in such cogent or widespread fashion, and theories espoused so fervendy, that they succeed in calling the paradigm itself into question. The process is often helped on its way by the impact of a revolutionary scientist—usually, Kuhn thinks, a younger person not schooled so long or so deeply in the paradigm guiding current scientific inquiry. Through factors such as these, it comes to be accepted that a whole new way of viewing reality is called for. It is time for a ‘paradigm shift’.
In this period of change, what emerges within science is a ‘willingness to try anything, the expression of explicit discontent, the recourse to philosophy and to debate over fundamentals’ (Kuhn 1970, p. 91). Normal science is being turned on its head and an era of ‘extraordinary science’ is being ushered in. It is this development that Kuhn styles a scientific revolution.
Once one begins to think in this fashion, it is not difficult to find revolutions enough in the history of science. Galileo (and the Leaning Tower of Pisa?) destroying forever the Aristotelian view that bodies fall at a speed proportional to their weight. Copernicus and his heliocentrism prevailing over earth-centred Ptolemeian astronomy. Lavoisier’s oxygen theory of combustion replacing Becher’s hypothesis of phlogiston. Darwin’s theory of natural selection overthrowing forms of scientific theorising that base themselves on a world governed by design. Einstein’s theory of relativity shaking the foundations of Newtonian physics. And so on. These are not mere changes within science that leave science itself very much as it was. These are changes of science. They alter forever the way scientists see the world they are trying to explain. For Kuhn, then, the history of science is not a story of steady advance through adding new data to those already in hand and gradually developing existing theory. Instead, the significant changes in science appear to have occurred through radical shifts in the way scientists view reality.
How have these shifts in perspective come about? Certainly, many non-scientific factors have played a part. Kuhn effectively relates the ‘doing’ of science to the broader sweep of history and to social factors and social change. Just as effectively, he links scientific effort to the interests, and the psychology, of both the scientific community and individual scientists. Because of this, his influential line of thought constitutes a further loosening of the hold positivism has taken on scientific thought and research. The picture Kuhn paints is not a picture of objective, valid, unchallengeable findings emerging from scientists working with detachment and in a spirit of unalloyed scientific dedication. To the contrary, scientific endeavour, as Kuhn conceives it, is a very human affair. Human interests, human values, human fallibility, human foibles—all play a part.
If one accepts Kuhn’s picture of things, it becomes very hard to sustain an image of science as a ‘garden enclosed’. Kuhn’s arguments make it impossible to elevate the work of the scientist over that of other professionals. Science now appears as run of the mill as any other human activity. Seen in the light of his arguments, how can science remain on the pedestal where the logical positivists have enshrined it? Change in science, it would seem, takes place in very much the same way as it occurs elsewhere—in art, say, or politics. It certainly does not necessarily come about in a disciplined or orderly fashion. Often, it just seems to ‘happen’, coming about in makeshift and fortuitous ways. In ‘anarchic’ fashion, perhaps? Could one go so far as to say that? Yes, even that.
3. FEYERABEND’S ‘FAREWELL TO REASON’
It is Paul Feyerabend (1924-94) who describes scientific progress as ‘anarchic’. Science, he tells us, ‘is an essentially anarchic enterprise’ (Feyerabend 1993, p. 9). This is not a criticism. For Feyerabend, working in anarchic fashion is simply the way things have to be. Rather than decrying scientific anarchism, we should embrace it warmly and celebrate it fervendy, for it is necessary for the progress of science and the development of culture. Scientific progress may mean different things to different people, but Feyerabend’s thesis is ‘that anarchism helps to achieve progress in any one of the senses one cares to choose’ (1993, p. 18). He goes on to oudine for us ‘an anarchistic methodology and a corresponding anarchistic science’ (1993, p. 13). Already we may be glimpsing why Feyerabend has so often been referred to as the enfant terrible of late twentieth-century philosophy of science.
Feyerabend too was bom in Vienna. He originally studied physics but, after working under Popper, he came to the fore as a philosopher of science in the 1960s. He spent several decades in Britain and the United States before becoming professor of the philosophy of science in Zurich, a post he filled for the last fifteen years of his life.
Feyerabend starts off reasonably close to the position of Popper, his one-time mentor and fellow Austrian. However, his forceful style of presentation provokes, even at the start, an accusation that has never been levelled at Popper—the charge of being an enemy of science. If Feyerabend’s critics brand him anti-science on the basis of his early thought, they very soon find further and more explosive ammunition in what he goes on to say and write. He moves not only well beyond Popper but even beyond Kuhn. One way in which he does so is in his attitude to ‘normal science’. For all his talk of normal science as a ‘mopping up operation’, and notwithstanding its failure to challenge the mling paradigm, Kuhn never fails to uphold the importance of its problemsolving function. Feyerabend, on the contrary, is thoroughly suspicious of this unchallenged continuance of normal science, alleging that it is based on indoctrination and constitutes a threat to academic freedom.
While Feyerabend may not be anti-science, he leaves no doubt about how he views the adulation traditionally offered to science.
On the other hand, we can agree that in a world full of scientific products scientists may be given a special status just as henchmen had a special status at times of social disorder or priests had when being a citizen coincided with being a member of a single universal Church. (Feyerabend 1993, p. 250)
In all this, Feyerabend insists that his quarry is positivism, not science as such. What he is questioning radically is the role of reason in science. He tides one of his books Farewell to Reason. Not that he is descending into wild irrationalism. He is querying the role of reason as it is generally understood. As he goes to some pains to emphasise in his posthumous autobiography, Killing Time, he is not denigrating reason as such but only attacking petrified and tyrannical versions of it. Feyerabend’s basic position is that, since science cannot be grounded philosophically in any compelling way, scientific findings are no more than beliefs and we should not privilege them over other kinds of belief —even Voodoo! Voodoo, in fact, ‘has a firm though still not sufficiently understood material basis’, writes Feyerabend, as he calls for a ‘pluralistic methodology’ (1993, pp. 36, 38).
Science, then, is ‘much more “sloppy” and “irrational” than its methodological image’ and ‘the attempt to make science more “rational” and more precise is bound to wipe it out’ (Feyerabend 1993, p. 157). In Feyerabend’s judgment, ‘what appears as “sloppiness”, “chaos” or “opportunism” . . . has a most important function in the development of those very theories which we today regard as essential parts of our knowledge of nature’ (1993, pp. 157-8). Hence his likening of the scientific anarchist to ‘an undercover agent who plays the game of Reason in order to undercut the authority of Reason’ (Feyerabend 1993, p. 23). He is influenced here by the Austrian satirists Johann Nestroy and Karl Kraus and by Dadaism, that nihilistic movement earlier this century which stressed the absurd and the unpredictable in artistic creation. Feyerabend stresses the absurd and the unpredictable in scientific knowledge.
Anything goes, then? Feyerabend does boldly say as much. He even describes this as the only principle ‘that can be defended under all circumstances and in all stages of human development’ (Feyerabend 1993, pp. 18-19). Yet he has norms of his own. For one thing, he demands that scientists test out their perceptions. The willingness to do this constitutes the difference between science and non-science (or, in his more forthright terms, between the domains of the respectable thinker and the crank). Adopting a certain point of view means a starting point for research, not some kind of conclusion. Cranks will flady deny that any issue exists or will be content to defend their position, but the respectable thinker thoroughly tests out the usefulness of the viewpoint, taking full account of factors that seem to favour its opponents. As one would expect from what has been said of Feyerabend already, he does not identify the respectable thinker simply with the person who is faithful to the accepted line in science. One example of this is his refusal to dismiss creationism out of hand as a crank viewpoint and his opposition to its exclusion from school curricula. If people are willing to test out their perceptions and have them tested out by others, they are respectable thinkers, no matter how unconventional their thinking, and they have a place in the generation of human knowledge.
How, then, should scientists test out their perceptions? By counterinduction. Counterinductive measures are not Popper-style attempts to falsify theories and hypotheses. ‘Methodologists may point to the importance of falsifications’, Feyerabend writes scathingly, ‘but they blithely use falsified theories’ (1993, p. 50). No, we need rules that will ‘enable us to choose between theories which we have already tested and which are falsified’ (Feyerabend 1993, p. 51). Counterinduction is just such a ‘measuring-stick’. Rather than an attempt to prove something false, it is a calling of ‘commonly-used concepts’ into question by developing something with which they can be compared.
Therefore, the first step in our criticism of customary concepts and customary reactions is to step outside the circle and either to invent a new conceptual system, for example, a new theory, that clashes with the most carefully established observational results and confounds the most plausible theoretical principles, or to import such a system from outside science, from religion, from mythology, from the ideas of incompetents, or the ramblings of madmen. (Feyerabend 1993, pp. 52-3)
Ideas of incompetents? Ramblings of madmen? Obviously, anything does go! Feyerabend’s point, of course, is that, if we want to examine something we are using all the time, we cannot discover it from the inside. We need, he tells us, ‘an external standard of criticism’, ‘a set of alternative assumptions’ (Feyerabend 1993, p. 22). This is his strategy of counterinduction. Counterinduction is ‘both a fact—science could not exist without it—and a legitimate and much needed move in the game of science’ (Feyerabend 1993, p. 53).
Behind this stance is Feyerabend’s recognition that scientific thinking, like all human thought, is historically conditioned through and through.
However, the material which a scientist actually has at his disposal, his laws, his experimental results, his mathematical techniques, his epistemological prejudices, his attitude towards the absurd consequences of the theories which he accepts, is indeterminate in many ways, ambiguous, and never fully separated from the historical background. (Feyerabend 1993, p. 51)
Ideas being historically conditioned and never absolute, Paul Feyerabend believes in pushing them to their extremes. In Three Dialogues on Knowledge, a series of dialogues based on the Socratic model, he reveals that, when he comes across unusual ideas, he tries them out. His way of trying them out is to push them to the limit. There is’, he tells us (1991, p. 50), ‘not a single idea, no matter how absurd and repulsive, that has not a sensible aspect, and there is not a single view, no matter how plausible and humanitarian, that does not encourage and then conceal our stupidity and our criminal tendencies’. Many would be comfortable enough with this thought when it is applied to cultural understandings and socio-political stances. People find it far more challenging when applied, as Feyerabend intends it to be applied, to scientific ‘truths’. The point is, of course, that Feyerabend refuses to accept the distinction. For him, scientific truths are no less cultural in character, and no less socio-political in origin, than any other of the beliefs we hold. He tells us, in fact, that ‘rationalists clamouring for objectivity and rationality are just trying to sell a tribal creed of their own’ (Feyerabend 1987, p. 301).
Feyerabend, along with Popper and Kuhn, has had an impact. Positivism, as we have seen, postulates the objective existence of meaningful reality. It considers such meaningful reality to be value- neutral, ahistorical and cross-cultural. It believes that, if one goes about it in the right way, one can identify such reality with certitude. What people like Popper, Kuhn and Feyerabend have done is to question one or other, or all, of these tenets in quite radical fashion.
In the wake of their considerations, some have come to reject positivism and the objectivism that informs it and to adopt a constructionist view of meaningful reality. Others remain within the positivist camp but temper very significandy the status they ascribe to their findings, the claims they make about them. It is not possible, they have come to recognise, to find some Archimedean point from which realities in the world can be viewed free from any influence of the observer’s standpoint. They admit that, no matter how faithfully the scientist adheres to scientific method, research outcomes are neither totally objective nor unquestionably certain. They may claim a higher level of objectivity and certitude for scientific findings than for other opinions and beliefs, but the absoluteness has gone and claims to validity are tentative and qualified.
It is this humbler version of the scientific approach, one that no longer claims an epistemologically or metaphysically privileged position, that has come to be known as post-positivism.
Reporting our research requires us to set forth the research process we have engaged in and to do so faithfully and comprehensively. It is, after all, our account of the research process that establishes the credentials of our research. Why should anyone set store by what we are asserting as a result of our investigation? And what store should anyone set by it? The only satisfactory answer to these questions is, ‘Look at the way we have gone about it’. The process itself is our only justification. For that reason, expounding our research process, including its more theoretical moorings (or, if you prefer, the assumptions we bring to our methodology and methods), assumes obvious and crucial importance.
What store should anyone set by our research findings? Even in putting the question, we sense another question coming to the fore—and a prior question, into the bargain. What store are we asking people to set by our research findings? After all, we may be presenting our findings as objective truths, claiming validity, perhaps generalisability, on their behalf. In that case, we are calling upon people to accept our findings as established fact, or at least as close to established fact as our research has enabled us to reach. On the other hand, we may be offering our findings as interpretation. It is a certain spin we have put on the data. In that case we are inviting people to weigh our interpretation, judge whether it has been soundly arrived at and is plausible (convincing, even?), and decide whether it has application to their interests and concerns.
In other words, we may be presenting our research in positivist terms or non-positivist terms. Let us say it again: it is a matter of positivism vs non-positivism, not a matter of quantitative vs qualitative. It is possible for a quantitative piece of work to be offered in non-positivist form. On the other hand, there is plenty of scope for qualitative research to be understood positivistically or situated in an overall positivist setting, and, therefore, for even self-professed qualitative researchers to be quite positivist in orientation and purpose. When investigators talk, as they often do, of exploring meanings by way of qualitative methods and then ‘confirming’ or ‘validating’ their findings by a quantitative study, they are privileging the latter in a thoroughgoing positivist manner. What turns their study into a positivist piece of work is not the use of quantitative methods but the attribution of objectivity, validity and generalisability to quantitative findings.
Accordingly, our consideration of positivism and post-positivism in this chapter turns out to be relevant enough. Called upon to set forth our research process incisively and unequivocally, we find ourselves unable to do that without, for a start, confronting the objectivist understanding of meaning and the positivist understanding of reality—and declaring our hand.
Source: Michael J Crotty (1998), The Foundations of Social Research: Meaning and Perspective in the Research Process, SAGE Publications Ltd; First edition.
