Ideology and Science in Economic Theory

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Abstract

This paper argues, using a development of Kuhn’s notion of paradigm, that all economic theories are to some extent ideological.  This does not mean, however, that economic theories are necessarily purely ideological.  An economic theory might be both ideological and scientific.  To investigate whether an economic theory is scientific we need a criterion for the scientificity of a theory.  The paper first considers one approach to this problem due to Kant, but this is rejected as incorrect and called ‘the Kantian fallacy’.  Another approach is then put forward: ‘the empirical confirmation principle’, and reasons are given for accepting this as correct.  Using this principle, it is then argued that that neoclassical economics is purely ideological, but that Keynes’ theory is scientific as well as being ideological.

Posted for comments on 12 Dec 2019, 10:05 am.

Comments (9)

  • Arne Heise says:

    Donald Gillies paper sends an extremely sympathetic message to Keynesian economists: Keynesian economics is scientific while neoclassical economics is not – it is pure ideology. Most Keynesian economists would, probably, subscribe to that message – yet, most neoclassical economists would probably not. And, I am afraid, they would be right – the story is simply not convincing.

    It all starts with an ommission: how is the term, or rather, concept ‘ideology’ defined? According to Karl Mannheim, there are two different definitions: an ideology can be a vision of a desired societal delopment in order to guide political actions. In this definition, ideology gets a positive connotation. The second definition refers to a biased or plainly wrong interpretation of reality in order to serve particular interests – this would be ‘ideology’ with a negative connotation. Which one does Gillies assume in his article?

    One may suppose that he refers to the first, positively connotated definition when he states that all theoretical schools/paradigms are to some extend ideological. This is so as every theoretical school/paradigm is based on a pre-analytical vision (the ontological Dimension in Lakatos’ terms). Although this pre-analytical vision ought to be chosen on the understanding that it is the best approximation of the object of investigation (in our case: the capitalist economy), it may, nevertheless, contain imputations in line with the scientist’s world vision (which seems to be clearly the case with Marxists). However, when Donald Gillies conflates (confounds?) economics schools/paradigms with political orientations, it appears that he refers to the second, negative connotation.

    Moreover, his ideas to discriminate between theoretical schools/paradigms by way of empirical confirmation appears to ignore important parts of the philosophy of science literature (is that why he elaborates on Kant in an otherwise quite unnecessary way?): due to the induction problem, theories cannot be confirmed but merely falsified. Accepting the famous Duhem-Quine critique theoretical schools/paradigms can never be falsified entirety but only single causal statements can be refuted.

    Last, but not least, I am (very much to my grief) not aware of any empirical refutation of neoclassical economics (of course, many theoretical deductions (ex ante predictions) from neoclassical economics proved wrong and caused ‘repair work’ – the number of labour market theories trying to explain involuntary unemployment could be a case in point) as much as I would not be convinced (if I would be an opponent of Keynesian economics) by the empirical evidence provided in the article to ‘confirm’ Keynesian economics.

    • Donald Gillies says:

      From Donald Gillies;

      Many thanks to Arne Heise for taking the trouble to read and comment on my paper. Here are my answers to the criticisms he makes.

      First of all he thinks that I should begin by defining the term ‘ideology’. However, many philosophers have the view that it is wrong to begin philosophical discussions with the attempt to define the terms used. Popper, for example, objects that this leads to an infinite regress or vicious circle. Wittgenstein thinks that one should study the meaning of a term by examining how it is used in the ‘language games’ in which it occurs. Both Popper and Wittgenstein condemn the search for definitions as ‘essentialism’. My own approach follows these critics of the search for definitions. The alternative approach is to explain the meaning of a term by giving examples of its use. This I do by considering in turn the three principal paradigms in economics (from left to right: Marxism, Keynesianism and Neo-Classical Economics) and describing the political ideology associated with each paradigm. This listing of examples seems to me a better approach than that of trying to give a definition.

      Arne Heise thinks that I elaborate on Kant in a quite unnecessary way. This I find surprising since Kant is usually held to be such a great philosopher that it is always quite appropriate to consider his views on any philosophical question. Perhaps Arne Heise thinks that Kant is now too out-dated to be relevant to contemporary issues in philosophy of science. But this is not true. There is at present a flourishing school of philosophers of science who are admirers of Kant and try to apply his philosophy to contemporary science. The 2015 Fernando Gil International Prize in Philosophy of Science was awarded to one of the leading members of this school, the American philosopher: Michael Friedman, for his book: Kant’s Construction of Nature. A Reading of the Metaphysical Foundations of Natural Science. My quotation from Kant comes from Kant’s book: The Metaphysical Foundations of Natural Science, which is mentioned in Friedman’s title.

      Arne Heise thinks that my ideas appear “to ignore important parts of the philosophy of science literature” citing as examples “the induction problem” and “the Duhem-Quine critique”. In fact I have written extensively on these problems. For example, in my book: Philosophy of Science in the Twentieth Century. Four Central Themes, I argue at length that falsifiability is not an adequate criterion for demarcating between science and metaphysics and should be replaced by confirmability. Obviously I could not repeat all this argument in a short paper on philosophy of economics, but perhaps I should have given a reference to this longer treatment of the question, and will do so in any revision of the paper.

      Arne Heise says, quite correctly in my view: “Accepting the famous Duhem-Quine critique theoretical schools/paradigms can never be falsified.” However, in the next sentence he writes: “I am (very much to my grief) not aware of any empirical refutation of neoclassical economics”. But if, as he himself has just pointed out, because of the Duhem-Quine thesis no paradigm can be empirically refuted, how could it be a cause of grief that neoclassical economics has not been refuted? There is something close to a contradiction here. My own criticism of Neo-Classical economics is not that is has been falsified, but that it has not been confirmed empirically.

      Arne Heise writes: “I would not be convinced (if I would be an opponent of Keynesian economics) by the empirical evidence provided in the article to ‘confirm’ Keynesian economics.” However, it does not seem to me enough to say that, under those hypothetical circumstances, he would not be convinced. He needs to give reasons why he would not be convinced. After all I present the empirical evidence in detail. It consists partly of correct explanations of already collected empirical data, and partly of empirical verifications, by further data, of often quite surprising predictions. This is just the sort of evidence, which is taken as having confirmed standard theories in the natural sciences such as Newton’s theory. Why should it not be regarded as confirming Keynesian theory?

      As this is an open peer discussion forum, I would like to conclude by asking Arne Heise a couple of questions. The first concerns his attitude to one of the issues considered in my paper, namely whether high-level economic theories can be scientific. He seems to regard Kant’s views as irrelevant to this question. He argues quite correctly in my opinion that such theories cannot in the light of the Duhem-Quine thesis be falsified. He further seems to express doubts about whether economic theories can be confirmed empirically. In the light of these opinions, it seems to me difficult for him to claim that high-level economic theories can be scientific at all. Does he really think that it is not possible for a high-level economic theory to be scientific? That is my first question.

      My second question is more specific. He speaks of: “the ontological Dimension in Lakatos’ terms”. I was a PhD student of Lakatos and knew him well for many years. However, I don’t remember him ever using the expression ‘the ontological Dimension’. I searched the indices of Lakatos’ philosophical papers and of his book, but the term ‘ontological Dimension’ does not appear either under ‘ontological’ or under ‘Dimension’. I have naturally become curious, and so would be very grateful if Arne Heise could let me know where Lakatos uses the expression ‘the ontological Dimension’. Many thanks.

      • Arne Heise says:

        Just a few comments:
        I do not doubt that many philosophers start philosophical discussions without clearly defining the object of their discussion. Yet, I would argue that that is not the approach taken in economics in I wouldn’t know what the point is to call something ‘ideological’ if I don’t know what is meant by this discription.

        Donald Gillies believes to have caught me in ‘something close to a contradiction’ because I am in grief over the non-falsification of neoclassical economics. This sentiment – as I believe every sentiment is – is an emotional, not a rational statement – can emotions be ‘something close to a contradiction’? I don’t think so. Yet, even accepting that entire paradigms can not empirically be falsified, so can – as I mentioned – single causal relations. Some of them may be crucial to the paradigm, other rather marginal. If crucial relations have been empirically falsified and no ex post theoretical repair work has been able to reconcile the deductive speculation with empirical findings, still the entire paradigm might not be falsified, yet would definitely be in a crisis. Actually, it was this that I had in mind when I uttered my grievance of the non-falsification of neo-classical economics even in this restricted sense.

        To come to the two Questions:

        1) Do I really believe that high-level economic theory can be scientific? Yes, I do. If the methodological standards that a scientific community has set itself are met, theories/theoretical schools/paradigms can be regarded as scientific. Economics has set itself very high methodological standards which exclude a radical ‘anything goes’ – still the scientifically created knowledge is merely ‘conjectural knowledge’ (Vermutungswissen) and, due to the methodological restrictions, most likely there will be competeing ‘conjectural knowledge’ (or pluralism).

        2) Where does the ‘ontologial dimension’ in Lakatos comes from. Lakatos does (probably) not use the term ‘ontological dimension’ but, at least that is my understanding, his (positive and negative) heuristic of a scientific research programme (see Lakatos, I.; Criticism and the Methodology of Scientific Research Programmes, in: Proceedings of the Aristotelian Society, New Series, Vol. 69 (1968 – 1969), p 176ff.) can be called ‘ontological dimension’ of a srp.

  • Rafael Galvão de Almeida says:

    The study of how ideology impacts economic theory is something that has a lot of potential, so I’m glad that there are more articles in this topic. I have tackled these issues in my own PhD. dissertation, so it’s within my field of interest and I hope you forgive me for self-citations.

    As a general comment, the article feels more like an article of general scientific methodology instead of an article on economic methodology. It is by no means a bad thing, but I call the attention to this because there might be differences on writing style, as Dr. Heise mentioned in his review (“I do not doubt that many philosophers start philosophical discussions without clearly defining the object of their discussion. Yet, I would argue that that is not the approach taken in economics in I wouldn’t know what the point is to call something ‘ideological’ if I don’t know what is meant by this description”, the literature in history of economic thought and economic methodology has not evolved to make a critique of essentialism). Though, I was interested in the focus on the philosophical question of whether science is ideological or not, by dialoguing with important philosophers, such as Kuhn and Kant. However, I feel it still there are some issues.

    I do believe the article could benefit from more history of thought. I am aware that there are other dozens of possibilities to deal with economics and ideology that could derail the article (like, it could go on with critical theory, questions of economics imperialism, and influence of McCarthyism in the 1950s science) and I try to recommend to not go on tangents, but while the affirmation that “neoclassical economics is ideological” is a weighty affirmation, it is also not new, in the sense that neoclassical economists have tackled these issues.

    At this point, the only major recommendation to add to your references in the paper is Lionel Robbins. Since he was the one that defined economics “the science which studies human behavior as a relationship between ends and scarce means which have alternative uses” (Robbins, 1932, p. 15), he was also the one that established (neoclassical) economics as non-ideological, value-free (assuming we can consider “value judgements” and “ideology” to be synonyms) and helped to make the economic theory in the state that it is today, which is the object of your critique. He wrote:

    “No less an authority than Gunnar Myrdal has devoted a whole book to the argument that, explicitly or implicitly, all propositions of economic theory, all classifications of happenings having an economic aspect, must involve judgments of value. I do not agree with this position. I don’t think that the proposition that, if the market is free and demand exceeds supply, prices will tend to rise, has any ethical content whatever.” (Robbins, 1981, p. 4; also see Robbins, 1961)

    And this is the thought of many economists. The question is, then, why would Robbins be wrong?

    Robbins himself made a distinction between value-free “economics”, and “political economy” where “should not only include, but should necessarily embrace” values (Colander, 2009, p. 438). Even so, for example, a lot of economists working on political models (such as the ones from the new political macroeconomics tradition) have attempted to make more ideology-free models (they did that because they considered the public choice models were too ideological, in the libertarian sense, see chapter 3 of my thesis, Almeida, 2019a). Even a very model-oriented economist such as Jean-Jacques Laffont wrote that most economists have chosen to ignore the interaction between economic policy and politics because of ideology, “some even believe that it is not ‘politically correct’ to develop policy recommendations altered by political considerations.” (Laffont, 2000, p. 5; Almeida, 2019a, p. 109). So, does the argument of your article mean that their efforts would be fated to fail?

    I might be going into a tangent, but it should be noted that the pendulum swings a lot: back in the 1950s, economics was more interventionist – see the socialist calculation debate, in which neoclassicals were socialists, and Jan Tinbergen’s theory of economic policy, in which he intended to use heavy math for optimal state intervention – and free-market economics was considered heterodox, even ideological (I wrote about in Almeida (2019b), but I consider Backhouse (2012) to be the best text on this issue), so there’s an entire economic practice to get away from ideology and value judgements. Though, even neoclassical economists are starting to realize that the use of mathematical and econometric models does not give full protection against ideology (Azam, 2019).

    Another issue is that the article also has a lot of wide, unsourced remarks, like “the central claim of the Marxist paradigm is that the profits made by capitalists arise out of the exploitation of workers”, “Keynes himself reached this conclusion during the 1930s when the free market seemed to have delivered the great depression with massive unemployment and under-utilisation of capacity”, “the left wing of the Post-Keynesians overlaps to some extent with the Marxist school” (I know a few conservative Post-Keynesians, they aren’t common, but they exist, though Keynes himself considered Marxism to be a poor approach to economics, see Keynes, 1932), “This is a highly mathematical theory, but it has never been applied in physics or in any other science” and a few more others. They might be common knowledge, but mentioning them without source might not be the best practice in usual history of economic thought literature.

    This is the reason why I went on to mention Robbins in a previous paragraph, to dissipate ambiguities that may be caused by common knowledge. Though I’d contest the affirmation that Keynes changed his views during the Great Depression; he showed his dissatisfaction as early as the Economic consequences of peace, and this is present throughout his 1920s writings, like Keynes (1930) and (1932). In his Treatise on Money he said, in a chapter he wrote in 1927, on index prices:

    “The Jevonian concept would have been intellectually delightful and of great scientific convenience if it had been based on a true analysis. It is one of the several quasi-mathematical economic conceptions, borrowed by analogy from the physical sciences, which seemed likely to be so fruitful when they first devised fifty or sixty years ago, but which have had to be discarded on further reflection, in whole or in part.” (Keynes, 1930, v. 1, p. 78).

    Keynes’s issue with the orthodoxy of its time was complicated, but his detachment from it was a process that started earlier.

    Though the exposition of the Kantian fallacy was interesting in section 3. It’s the first time I heard of the term, but I won’t deny its subtextual presence in economic debates. V. V. Chari, in a Senate hearing on the causes of the 2007-8 crisis, said that “If you have an interesting and a coherent story to tell, you can do so within a DSGE model. If you cannot, it probably is incoherent” (Chari, 2010, p. 32). Therefore, “from this perspective, there is no other game in town.” (ibid., p. 35).

    However, I wonder if there are other examples of the Kantian fallacy in the current literature (as a term, and as concept). I have to admit I thought it seems to me to be related to physics envy (Nelson, 2015).

    As for section 4, as far as I understood, the “empirical confirmation principle” (another term which is the first time I hear) depends on the empirical confirmation of a theory. How is it different from Milton Friedman’s proposition, in an extremely summarized way, of his article that what matters is the result, not the premises of the model (Friedman, 1953)? I’m using this example because Friedman (1953) is a text that the readers of the journal would be mostly familiar with. As we all know, Friedman was a very ideological person, though the principles of that article guide economists independent of ideology (though admittedly it might be a topic for a future article, still a passing reference should be enough).

    In the end, the article needs proper revisions, because of the issues of style and needs to be a bit more robust on the citations, and to dialogue better with other articles relevant in the economic methodology and history of economic thought. As Dr. Heise wrote, some terms might need explanation or a reference to the literature, just as you did the revision of Keynes exposition in section 5 (incidentally, I believe most readers of the journal would be more familiar with Keynes’s exposition than Kantian fallacy, for example) – an example where this would be useful in your statement that you concluded in a previous paper that there is no empirical confirmation to neoclassical economics and that seems to be an important point of section 4, but it’s not safe to assume your readers read that paper (I checked this reference in Google Scholar and out of the citations registered there, none was made by an economist by formation), if you could summarize the argument it could be good, or else readers might be unconvinced of the thesis “neoclassical economics is value free” and still follow Robbins’s argument. I hope my comments can be useful.

    References

    Almeida, Rafael Galvão de. Dreaming of unity: essays on the history of new political economy. Thesis, Doctor in Economics. Belo Horizonte: UFMG, 2019a. Available at
    Almeida, Rafael Galvão de. How economics became an interventionist science (and how it ceased to be). Texto para discussão nº 612. Belo Horizonte: UFMG, 2019b.
    Azam, Jean-Pierre. Let’s call their bluff: the politics of econometric methodology. TSE Working Papers 19-1030.Toulouse: Toulouse School of Economics, 2019.
    Backhouse, Roger. Economics. In: Backhouse, Roger; Fontaine, Phillippe (eds.). The History of Social Sciences since 1945. Cambridge: Cambridge University Press, p. 38ff, 2010.
    Chari, V. V. Statement of V. V. Chari, Paul W. Frenzel Land Grant professor of liberal arts, University of Minnesota. In: BUILDING A SCIENCE OF ECONOMICS FOR THE REAL WORLD. Hearing before the Subcommittee on Investigations and Oversight, Committee on Science and Technology, House of Representatives, One Hundred Eleventh Congress, Second Session, Jul. 20, 2010. Serial No. 111–106. Washington: U. S. Government Printing Office, 2010, p. 32-37.
    Colander, David. What was “it” that Robbins was defining? Journal of the History of Economic Thought, v. 31, n. 4, p. 437-448, 2009.
    Friedman, Milton. The methodology of positive economics. 1953. In: Friedman, Milton. Essays in positive economics. Chicago: University of Chicago Press, p. 3-43, 1966.
    Keynes, John Maynard. Treatise on money. London: Macmilliam, 1930.
    Keynes, John Maynard. Essays in Persuasion. London: Macmillian, 1932.
    Laffont, Jean-Jacques. Incentives and political economy. Oxford: Oxford University Press, 2000.
    Nelson, Richard. R. Physics envy: get over it. Issues in Science and Technology, v. 31, n. 3, p. 71-78, 2015.
    Robbins, Lionel. An essay on the nature and significance of economic science. London: Macmillian, 1932.
    Robbins, Lionel. On the relationship between politics and economics. 1961. In: Robbins, Lionel. Politics and economics. London: Macmillian, 1963.
    Robbins, Lionel. Economics and political economy. American Economic Review, v. 71, n. 2, p. 1-10, 1981.

  • Dave Taylor says:

    I agree with Arne Heise: Gillies’ story is not convincing, although I would have liked his abstract to be true. My old dictionary reveals the positive and negative connotations of ‘ideology’ as ‘metaphysics’ and ‘abstract theory, with Kant being the metaphysician and Adam Smith’s mentor David Hume the ideologue condemning it, and attempting to build social science on sand of the ‘theory’ of the impossibility of knowing what you can’t see, i.e causality. The father of modern science was Francis Bacon, who advocated taking things to bits so you COULD see how they worked, small things like a compass needle revealing influences you wouldn’t see in an iron bar. But anyway, Donald Gillies doesn’t seem to have seen the significance of his own argument against what he sees as ‘Kant’s mistake’, nor Kuhn’s distinction between ‘revolutionary’ and ‘normal science’, i.e.’ fundamental’ and ‘applied science’. The point is that Newton’s cosmology was applied science built on the foundation of his equations of motion, expressing which required Kant’s ‘metaphysical language of Space, Time and Cause. This was not a mistake: it was Kant (and before him Aristotle) going beyond naive observation to realise the significance of language. Not only chemistry has changed since then: so has the language of mathematics, which now has to account for processes. In today’s language, ‘Kant’s mistake’ was to take for granted the need to “operationalise” symbols like ‘+’: i.e. proof that they can be carried out. Economics still gaily commit the fallacy of aggregation, adding the price of apples to that of bananas.
    The question economists need to ask themselves is, what fundamental science is economics an application of? Newton’s force or Shannon’s information? DSGE or Cybernetics? (Wiener’s sub-title is “Control and Communication in the [human] animal and the [economic] machine”), The rival paradigms (exemplars), I suggest, are now DSGE and PID control, the former being about random forces on average balancing each other out and the latter Newton’s parallelogram of forces being remotely directed via human information channels, including brains. Fifty years ago, reading Keynes with a control engineering rather than economics training, I saw Keynes anticipating PID control by adding the I feedback (acting to counter information on build-up of unemployment) to the classical P feedback (continuous adjusting price information to counter scarcity of supply or demand). Instability due to too much entrepreneurial D feedback was explained much later by chaos theory. Minsky matters.

    • Donald Gillies says:

      My thanks to Dave Taylor for his comment on my paper. There are two points I would like to make about what he says.

      The first concerns the issue of what he calls: ‘Kant’s mistake’. This he defines as follows: “In today’s language, ‘Kant’s mistake’ was to take for granted the need to “operationalise” symbols like’+’: i.e. proof that they can be carried out.” Now it is true that Kant does discuss ‘+’ in his famous analysis of 5 + 7 = 12 in Prolegomena §2. Moreover, it is perfectly possible that Kant was mistaken in what he says about ‘+’, but this is not at all relevant to my paper in which I discuss a completely different passage from Kant on a different topic. The passage comes from Metaphysical Foundations of Natural Science and runs: “I maintain … that in every special doctrine of nature only so much science proper can be found as there is mathematics in it.” It is this passage from Kant which I claim to be mistaken rather his discussion of ‘+’.

      The second concerns the question of rival paradigms in economics. In my paper, partly following Kuhn, I argue that, in contrast to the natural sciences in periods of normal science, there are always rival paradigms in economics. I list the main rival paradigms as neoclassical, Keynesian, and Marxist. Dave Taylor seems to agree with me that there are rival paradigms in economics, but he classifies them differently. He says: “The rival paradigms (exemplars), I suggest, are now DSGE and PID control.” This however seems to be a classification unique to Dave Taylor. I have never heard anyone else use it. Economists are often described as being neo-classical, Keynesian or Marxist, but never as being DSGE or PID control economists. It seems to me more sensible to stick to the standard classification rather than switch to such a peculiar one.

  • Donald Gillies says:

    To Rafael Galvão de Almeida:

    Your comments were very useful and will help me revising the paper in several respects. The general comment that “the article feels more like an article of general scientific methodology instead of an article on economic methodology” contains a lot of truth. Essentially I have applied some ideas developed in the context of the natural sciences to economics, and this may make several things I say not very intelligible to the intended audience of economists. I think the situation could be improved by following some of your suggestions.

    Let me first discuss my treatment of ideology. It is important to stress here that I was not trying to develop a general theory of ideology. My line of argument is that, if we look at the assumptions of the main paradigms in economics, we can see that they imply conclusions, which would be accepted as ideological by anyone, no matter what their detailed view of ideology was. Take for instance Keen’s analysis of neoclassical economics, which I quote in section 2. He argues, quite correctly in my view, that neoclassical economics implies that one should oppose minimum wage legislation, and prefer the private to the public provision of services. But these conclusions are plainly ideological. One would have to adopt a strange sense of ‘ideological’ to claim that they are not ideological and indeed that they are not part of the political ideology which has been dominant in the last few decades. Exactly the same kind of argument can be used to show that Marxism is also ideological.

    I think you are right, however, that this line of argument could be improved by discussing the views of a well-known proponent of the opposite point of view, namely Lionel Robbins. Naturally I do think that Robbins is wrong. You also write: “a lot of economists … have attempted to make more ideology-free models … So, does the argument of your article mean that their efforts would be fated to fail?” The answer is: ‘yes’. My view is that economic theories will inevitably be ideological, but it is possible for them to be scientific as well. Thus the better programme for economists is to try to make their theories scientific.

    Now, in contrast to my treatment of ideology, I do try to characterise what it means to be ‘scientific’ and do not just rely on the usual sense of the term. Here my discussion is a development of what has been going on in the philosophy of the natural science, more specifically of a debate between the Kantians and the empiricists. I favour the empiricists in this debate and have tried to develop their position in other works, as I mentioned in my reply to Arne Heise. It is not surprising that you have not heard the terms ‘Kantian fallacy’ and ‘empirical confirmation principle’ before, since I introduce them for the first time in this paper (though I have used them in talks previously). You ask whether the Kantian fallacy is related to physics envy. My own view is that it is related less to envy of physics and more to the attempt to pass off economics as just as scientific as physics. In fact I put forward this view in a passage from the first draft of the paper, which I cut out, namely the following:

    “The extensive use of mathematics in neoclassical economics greatly adds to its ideological force. People are used to a highly mathematical physics, which produces accurate and reliable predictions that form the basis of successful practical applications. The theories of neoclassical economics look very like those of mathematical physics, and hence encourage people to think that they too will give reliable predictions, which can be used successfully in practice. This of course is an example of what I called earlier: ‘the Kantian fallacy’.”

    Your question of how the ‘empirical confirmation principle’ differs from Milton Friedman’s ideas on this subject is a very interesting one. The difference is that I regard confirmation as arising out of successful explanations and/or successful predictions (section 4), while Friedman mentions only predictions. I think it would be a good plan to discuss Friedman’s views at this point since they are familiar to most economists and would help to clarify my own position. Robbins could be discussed in this context as well, since his apriorist views form a striking contrast to empiricism.

    Regarding unsourced remarks, there is no problem about sourcing my claim about the Marxist paradigm. There are many quotations in Capital Vol 1, Chapter IX, section 1, which indeed is entitled: ‘The Degree of Exploitation of Labour-Power’. Regarding Keynes, I think I will modify what I say in the light of your point that Keynes may have reached some of his later conclusions before the 1930s. I agree too that it may be worth mentioning Keynes’ own opposition to Marxism. In his Essays in Persuasion (1931), he expresses astonishment (Collected Works Edition, p. 285) regarding Marxian socialism as to “how a doctrine so illogical and so dull can have exercised so powerful and enduring an influence over the minds of men, and, through them, the events of history.” I couldn’t, however, locate your quotation: “This is a highly mathematical theory …” Where does that occur?

    One final point of disagreement, I don’t think it is worth repeating my argument in the 2012 paper that neoclassical economics is not confirmed empirically. The 2012 paper is available on ResearchGate, so that anyone interested can look it up. The main claim of the present paper is that Keynes’ theory has been strongly empirically confirmed by data and so is scientific. Curiously neither you nor Arne Heise say whether you think this claim is correct.

  • Michel S. Zouboulakis says:

    The paper makes a very interesting critique of the ideological roots of mainstream economy theory and the empirical relevance of Keynesian Economics. Yet, it wishes to do that through the Kuhnian notion of Paradigm. The application of Kuhn’s ideas to social sciences has been debated too many times since the 1960’s and rejected as inapplicable to social sciences in general. Kuhn himself has explicitly recognized that, in the 2nd edition of his 1962 masterpiece. Strictly speaking, for Kuhn, social sciences are still in the pre-paradigmatic era.

    Economists tried to use the Paradigm scheme since 1965 (Gordon) and Coats (1969), but they failed to convince the community. There were many applications of the Kuhnian revolution scheme specifically to interpret the Keynesian shift by Stanfield (1974), Dillard (1974), and Jalladeau (1978). I believe one should worry about that literature and consider it. Even if we dismiss Kuhn’s own restriction to apply his scheme to social sciences, there are still many sound epistemic reasons for denying the existence of paradigmatic shift in Economics.

    After all, the author could make his point without any reference to Kuhn and still defend well his main thesis which is to state the superiority of the original Keynesian Economics vis-a-vis the Neoclassicals, based on its empirical relevance. In that case, the paper needs to be revised accordingly and leave the considerations about science and ideology to the introduction.

    Specific remarks

    p. 2: what is the difference between Schools of thought and Paradigms?

    p. 6: empirical confirmation leads to a dead end, as Popper has shown since 1938. Briefly put, you are never sure that new cases will corroborate what has been already confirmed. The whole refutability criterion is based on that principle.

    p. 11: The author says, “Subsequent events showed that this Keynesian argument was correct”. Could you be more specific? Which events? Decrease in US unemployment figures started long before 1936, the year of publication of Keynes’ General Theory.

    p. 15: the principle of predicting a new event e, very improbable on background knowledge looks very close to Lakatos’ criterion of empirical progressiveness (predicting novel facts). Is it so? Still, I wonder if empirical predictability is the only criterion of scientificity, what is the difference with Friedman’s methodology (1953)?

    It would be great to give the direct references to the online reviews made in the paper.

    A final suggestion: the paper should be entitled “On the empirical superiority of Keynesian Economics”.

    • Donald Gillies says:

      Reply to the comments of Michel Zouboulakis on my paper ‘Science and Ideology in Economic Theory’

      M.Z. disapproves of my use of the Kuhnian notion of paradigm in economics, and goes on to say: “After all, the author could make his point without any reference to Kuhn and still defend well his main thesis which is to state the superiority of the original Keynesian Economics vis-a-vis the Neoclassicals, based on its empirical relevance.” This is not my main thesis, however, since I consider not just the original Keynesian Economics, but also more recent work by Chick and Pettifor in what I would call the Keynesian paradigm. Thus the notion of a paradigm in economics is really essential to my thesis. I can, however, respond to M.Z.’s criticism by adding an additional argument in favour of the use of the concept of paradigm in economics. It is the following.

      Kuhn introduces the concept of paradigm as follows (1962, p. 10):

      “Aristotle’s Physica, Ptolemy’s Almagest, Newton’s Principia and Opticks, Franklin’s Electricity, Lavoisier’s Chemistry, and Lyell’s Geology – these and many other works served for a time implicitly to define the legitimate problems and methods of a research field for succeeding generations of practitioners. They were able to do so because they shared two essential characteristics. Their achievement was sufficiently unprecedented to attract an enduring group of adherents away from competing modes of scientific activity. Simultaneously, it was sufficiently open-ended to leave all sorts of problems for the redefined group of practitioners to resolve.
      Achievements that share these two characteristics I shall henceforth refer to as ‘paradigms’ …”

      Kuhn here mentions key texts in the natural sciences, but, if we make a similar list of key texts in economics such as Marx, Capital, Keynes The General Theory and the books by the founding fathers of neo-classical economics, then we find that much of what Kuhn says applies also to these texts. These “works served for a time implicitly to define the legitimate problems and methods of a research field for succeeding generations of practitioners”. Taking Keynes The General Theory as an example, it is true to say that its “achievement was sufficiently unprecedented to attract an enduring group of adherents away from competing modes of … [economic] … activity” and that “it was sufficiently open-ended to leave all sorts of problems for the redefined group of practitioners to resolve”. This, I think, justifies the use of Kuhn’s term ‘paradigm’ in economics, but a key difference between economics and the natural sciences must not be forgotten. Keynes The General Theory did not establish a consensus in the field of economics. Many practitioners remained loyal to older paradigms such as the Marxist and the Neo-classical.
      I do, however, agree with M.Z.’s suggestion that I should change the title of the paper to something like ‘On the empirical superiority of Keynesian economics’. I think this would bring out the key point of the paper, which the present title fails to do. I prefer a slight alteration to ‘The empirical success of Keynesianism’. This is because I do not want to emphasize the comparison with neo-classical economics, as the case of neo-classical economics is dealt with in detail in another paper of mine [Gillies 2012] rather than the present one. In the revision, I’ll limit myself to a brief mention of my 2012 paper at the end.
      I now turn to a consideration of the specific remarks.

      p. 2: what is the difference between Schools of thought and Paradigms?
      Schools of thought are composed of individuals, while paradigms are sets of theoretical assumptions which guide the practice of the researchers.

      p. 6: empirical confirmation leads to a dead end, as Popper has shown since 1938. Briefly put, you are never sure that new cases will corroborate what has been already confirmed. The whole refutability criterion is based on that principle.
      This is a position which would have few supporters among philosophers of science today. I should say that the overwhelming majority of philosophers of science would regard Popper’s refutability criterion as having been shown to be wrong by the Duhem-Quine thesis – a point stressed by Lakatos in his criticism of Popper. Similarly the overwhelming majority would accept, contrary to Popper, that there is notion of empirical confirmation which is inductive in character. I will stress these points in the revised version of my paper, giving references to the literature.

      p. 11: The author says, “Subsequent events showed that this Keynesian argument was correct”. Could you be more specific? Which events? Decrease in US unemployment figures started long before 1936, the year of publication of Keynes’ General Theory.
      By “subsequent events” I meant events subsequent to 1939. These events are listed in the next paragraph. As what I wrote was not entirely clear, I will replace “subsequent events” by “events after 1939”.

      p. 15: the principle of predicting a new event e, very improbable on background knowledge looks very close to Lakatos’ criterion of empirical progressiveness (predicting novel facts). Is it so? Still, I wonder if empirical predictability is the only criterion of scientificity, what is the difference with Friedman’s methodology (1953)?
      In the paper I do say regarding the principle in question: “(For a discussion of this principle, see Gillies, 1998, p. 157)” If you had looked up this reference, you would have seen that I attribute the key idea behind this principle to Popper in 1959, which was before Lakatos. I will include some material explicitly from my 1998 paper in the revised version. Regarding Friedman (1953), Rafael Galvão de Almeida already suggested I should discuss this reference, which I agreed to do in my reply to him.

      I will certainly give direct references to the online reviews of my paper.

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