DO WE NEED A RULE OF ACCEPTANCE OF OBSERVATION REPORTS?
With this, I leave exegesis of Popper for the moment, and move to the question, ‘do we have to affirm basic statements affirmed by others?’ To be more precise, ‘are we obliged, qua scientists, to affirm basic statement affirmed by other scientists?’ To be still more precise, the obligation referred to in the previous question must read not in a legal or a moral sense but as to whether the rule is recommendable to and/or accepted in the commonwealth of learning.
The question, should we believe hear-say in science, has, to my knowledge, often been raised only to incant the injunction - originated by Bacon - trust only your own senses! As I said this rule is mad; anyone who doubts for a moment that he was born of a human female is mad, regardless of whether he has ever observed birth, human or animal, and regardless of from whom he had heard the facts of life and how reliable his informant happens to be.
Some writers, such as Sir John Herschel, in the opening chapter of his Preliminary Discourse to the Study of Natural Philosophy of 1831, stress the opposite, the fact that men of science are bona fide credible, that there are few hoaxes in science, i.e. that false observation reports are seldom made fraudulently. Some writers see this as the basis for scientific objectivity. They rightly conclude that good faith is what makes the chief difference between science and pseudo-science, including alchemy, astrology, mesmerism, phrenology, etc. Herschel seems to concur, though only in a passing footnote which is no sufficient indication of his view. Popper, however, certainly does not concur.
It is hard to say what Popper’s view is on the place of good faith in the commonwealth of learning. He stresses that objectivity in science is rooted not in the good intentions of the scientist, even when they undoubtedly exist and are operative, but in the institution of intersubjective tests.
Yet institutions involve mutual understanding and some measure of trust. It is not that tests are the opposite of trust, of course; indeed, the subtlety of the situation stems from the fact that when we test regardless of trust trust may flourish, whereas, when trust is declared to be exclusive of testing it immediately becomes strained. One may note that this is so regardless of whether the trust or test are of scientific or political information, or personal matters of any sort. Tests are generally not the opposite of trust, and so the question can arise, when we are told of a test, and when we are told that its result supports the theory it came to test or otherwise, do we have to believe the report?Certainly we can doubt the report in the sense of wishing to repeat the test ourselves; we have seen that. Certainly we may offer internal criticism of the test and say its preparation was not precise enough to procure results that may conflict with the theory in question and so it was not a genuine test. (This point is one of Popper’s great contributions to methodology even though he merely sharpened a thesis already offered by William Whewell over a century ago.) But supposing I do not intend to repeat the test and see nothing methodologically wrong with it. Do I have to declare its results true? If so, why?
Suppose I am not allowed to declare the result false and stick to my own hypothesis which contradicts it. Do I have to declare the result true if it corroborates my hypothesis? Do I have to declare it true if it relates to a hypothesis I have no stake in? What is the import of endorsement of an experimental report anyway?
A tacit reply can be found elsewhere in Popper’s work: we wish to explain facts, and as we endorse people’s reports of facts our stock of reported facts increases and the task we have undertaken - to explain facts - becomes more challenging and interesting.
This reply takes us away from our initial problem. Our initial problem was, when should we prefer a theory to a conflicting report of facts; now we speak of a stock of factual evidence to be explained.
Our questions then, can be connected thus. Surely, when we endorse a theory in the face of an observation report we do not explain it. When, in particular, we have rejected an observation report on the basis of later and better ones, we do not want to have it explained by our theories, since only a refuted theory explains a refuted report and we want newer unrefuted theories. Do we, then, have the task of explaining past mistakes? No doubt, we do not want to explain, as physicists or chemists, all sort of superstitions and fables about physics - as this is the task of ethnographers, social historians, and cultural historians. But do we wish, as physicists - not as historians of physics - to explain persistent errors in past physics?This indicates, I hope, that discussion about science easily spills over into discussion about the nature and role of scientific institutions as institutions, as well as into discussion of how much can we comprehend an activity, science or other, without its history.
Perhaps this is unavoidable. Mario Bunge seems to hold the view that our intellectual activities integrate so deeply into their background that at times all separation looks arbitrary. I have great sympathy with Bunge’s philosophy in general and with this view in particular. Yet I think that at times we may avoid big questions even when discussing methodology.
What I tried to show in Chapter V above was that Popper’s theory of testability and/or of simplicity may include a solution to the central problem of the present Chapter: If the rejection of a hypothesis is the more testable option then reject the hypothesis; if the rejection of an observation report is the more testable option, then reject the report; in particular, if an observation report is rejected because of a very testable hypothesis, so much the better. Now the way to make the rejection of an observation report based on a highly testable hypothesis is generally very plain: we can try to argue that the observation is inaccurate, that it is only an approximation to the truth.
This, then, explains, along Popper’s methodology, a few items. First, it explains the fact that at times men of science prefer to reject reports which conflict with their hypotheses, at times they prefer to reject the hypotheses. It explains, second, why a new hypothesis is more often preferred to reports which conflict with it than an old one. It further explains the difference between a new and an old hypothesis by viewing the new hypothesis which conflicts with reports and is then tested (refuted or corroborated) as graduating to the status of an old hypothesis. (The more observation reports we have the more difficult it is to match the testability and simplicity of what goes with them.) It explains, thereby, the role of corroboration in Popper’s methodology - and in a manner quite contrary to Popper’s since it takes it as enhancing explanatory power, simplicity, and testability, whereas Popper erroneously considers corroboration a value in itself and endorses Boyle’s rule. It also explains the fact, or is it an alleged fact, that the hierarchy of hypotheses reported in science text-books consists not of all testable hypotheses which were ever proposed as explanations, but only those which were highly corroborated and thus constitute stages in a simplified history of the science. (This again is contrary to Popper’s theory of corroboration since it allows for the corroboration of theories known from the start to be false, such as Bohr’s model.) It finally explains the hierarchy as that of explanations of ever increasing levels, of both theories and observation reports as approximations in stages. This, then, makes a simplified history of a science part and parcel of that science.All this, particularly the idea that an explanation may stand in the relation of logical contradiction to the explained observation report, and the idea of hierarchy of theories as approximations, is fairly Popperian, of course, much in accord with Popper’s own ‘Three Views Concerning Human Knowledge’ and his ‘The Aims of Science’.
It is also in plain contradiction to the theory of explanation (as deduction) presented in Popper’s Logic of Scientific Discovery, to the theory of the (compulsory) emperical basis offered there, and even to the theory of degrees of testability (rather than levels of approximation). It seems to me that Popper’s refusal to admit past inconsistency in open and clear expression prevents him from seeing the force of his own views - in a streamlined version, as I have presented it here, or in some other way.Impressive as I find this streamlined version, I nevertheless reject it. Meanwhile Bartley has taught us that testability need not always be interesting. Certainly today’s aerodynamics is much more testable yet much less interesting than several branches of today’s physics. What Bartley suggests, in his classic paper of 1968, is that it is more important to be able to discuss different possibilities, different frameworks, research programs and procedures, different kinds of hypotheses, compare the preference for an observation report with the preference for a conflicting hypothesis, and so on. As long as things keep moving, and interestingly so, Bartley says, things are going well.
What should we rule about dogmatism, and should we allay Bacon’s fear of it, Boyle’s fear of it, Popper’s fear of it? If Bartley is right then this fear is misplaced. Those who wish to dogmatize will do so; and with little ingenuity circumvent every rule in the book. Better let them dogmatize. The free spirits questing for new ideas and new truths will have little patience with dogmas but may develop much patience with dogmatists.