BOOK VIII - Page 6

Mitchell’s Institutionalist Critique

Haavelmo’s agenda had its Institutionalist critics long before the rational-expectations advocates and data-mining practitioners.  Morgan also notes in her History of Econometric Ideas that some econom­ists including the Institutionalist economist Wesley Clair Mitchell (1874-1948) opposed Haavelmo’s approach.  Mitchell had an initiating rôle in founding the prestigious National Bureau of Economic Research (N.B.E.R.), where he was the Research Director for twenty-five years.  In 1952 the National Bureau published a biographical memorial volume titled Wesley Clair Mitchell: The Economic Scientist edited by Arthur Burns, a long-time colleague and later a Federal Reserve Board Chairman. 

Mitchell’s principal interest was the business cycle, and in 1913 he published a descriptive analysis titled Business Cycles.   Haavelmo’s proposal to construct models based on existing economic theory may be contrasted with a paper by Mitchell titled “Quantitative Analysis in Economic Theory” in American Economic Review (1925).  Mitchell predicted that quantitative and statistical analyses in economics will result in a radical change in the content of economic theory from the prevailing type such as may be found in the works of classical economist Alfred Marshall.  Mitchell said that instead of interpreting the data in terms of subjective motives, which are assumed as constitut­ing an explanation and which are added to the data, quanti­tative economists may either just disregard motives, or more likely they may regard them as problems for investigation rather than assumed explanations and draw any conclusions about them from the data.  Thus while Simon’s thesis of bounded rationality is a radical departure from the neoclassical optimizing concept of rationality, Mitchell’s is much more radical, because he dispensed altogether with such imputed motives.

In his “Prospects of Economics” in Tugwell’s Trend of Economics (1924) Mitchell also said that economists would have a special predilection for the study of institutions, because institutions standardize behavior thus enabling generalizations and facilitating statistical inferences.  He prognosticated in 1924 that as data becomes more available, economics would become a quantitative science less concerned with puzzles about economic motives and more concerned about the objective validity of its account of economic processes.  While many neoclassical economists view Mitchell’s approach as atheoretical, Mitchell had a very erudite knowledge of economic theories as evi­denced in the monumental two-volume work Types of Economic Theory (ed. Dorfman, 1967).

Mitchell’s principal work setting forth the findings from his empirical investigations is his Measuring Business Cycles co-authored with Arthur F. Burns and published by the National Bureau in 1946.  This five-hundred page over-sized book contains no regression-estimated Marshallian supply or demand equations.  Instead it reports on the authors’ examination of more than a thousand time series describing the business cycle in four industrialized national economies, namely the U.S., Britain, France and Germany.  The authors explicitly reject the idea of testing business cycle theories, of which there were then a great many.  They state that they have surveyed such theories in an effort to identify which time series may be relevant to their interest.  Their stated agenda is to concentrate on a systematic examination of the cyclical movements in different economic activities as measured by historical time series, and to classify these data with respect to their phasing and amplitude.  They hoped to trace causal relations exhibited in the sequence that different economic activities represented by the time series reveal in the cycle’s critical inflection points.  To accomplish this they aggregate the individual time series so that the economic activities represented are not so atomized that the cyclical behavior is obscured by perturbations due to idiosyncrasies of the small individual units.

The merits and deficiencies of the alternative methodologies used by the Cowles Commission group and the National Bureau were argued in the economics literature in the late 1940’s.  In Readings in Business Cycles (1965) the American Economic Association has reprinted selections from this contentious literature.  Defense of Haavelmo’s structural-equation approach was given by 1975 Nobel-laureate economist Tjalling C. Koopmans, who wrote a review of Mitchell’s Measuring Business Cycles in the Review of Economic Statistics in 1947 under the title “Measurement without Theory.”  Koopmans compared Burns and Mitchell’s findings to Kepler’s laws in astronomy and he compared Haavelmo’s approach to Newton’s theory of gravitation.  He notes that Burns and Mitchell’s objective is merely to make generalizing descriptions of the business cycle, while the objective of Haavelmo’s structural-equation approach is to develop “genuine explanations” in terms of the behavior of groups of economic agents, such as consumers, workers, entrepreneurs, etc., who with their motives for their actions are the ultimate determinants of the economic variables.  Then he adds that unlike Newton, economists today already have a systematized body of theory of man’s behavior and its motives, and that such theory is indispensable for a quantitative empirical economics.  He furthermore advocates use of the Neyman-Pearson statistical inference theory, and calls Burns and Mitchell’s statistical techniques “pedestrian.”

The approach of Burns and Mitchell was defended by Rutledge Vining, who wrote a reply to Koopmans in the Review of Economics and Statistics in 1949 under the title “Koopmans on the Choice of Variables to be Studied and the Methods of Measurement.”  Vining argues that Burns and Mitchell’s work is one of discovery, search, and hypothesis seeking rather than one of hypothesis testing, and that even admitting that observation is always made with some theoretical framework in mind, such exploratory work cannot be confined to theoretical preconceptions having the prescribed form that is tested by use of the Neyman-Pearson technique.  He also argues that the business cycle of a given category of economic activity is a perfectly acceptable unit of analysis, and that many statistical regularities observed in population phenomena involve social “organisms” that are distinctively more than simple algebraic aggregates of consciously economizing individuals.  He says that the aggregates have an existence over and above the existence of Koopmans’ individual units and their characteristics may not be deducible from the behavior characteristics of the component units.

Koopmans wrote “Reply” in the same issue of the same journal.  He admitted that hypothesis seeking is still an unsolved problem at the very foundations of statistical theory, and that it is doubtful that all hypothesis-seeking activity can be described and formalized as a choice from a pre-assigned range of alternatives.  But he stands by his criticism of Burns and Mitchell’s statistical measures, because he says that science has historically progressed by restricting the range of alternative hypotheses, and he advocates crucial experiments.  He claims that crucial experiments deciding between the wave and particle theories of light in physics were beneficial to the advancement of physics before the modern quantum theory rejected the dichotomy.  He also continues to adhere to his view that it is necessary for economics to seek a basis in theories of individual decisions, and says that he cannot understand what Vining means by saying that the aggregate has an existence apart from its constituent components, and that it has behavior characteristics of its own that are not deducible from the behavior characteristics of the components.  He maintains that individual behavior characteristics are logically equivalent to those of the group’s, and that there is no opening wedge for essentially new group characteristics.

In the same issue of the same journal Vining wrote “A Rejoinder”, in which he said that it is gratuitous for anyone to specify any particular entity as necessarily the ultimate unit for a whole range of inquiry in an unexplored field of study.  The question is not a matter of logic, but of fact; the choice of unit for analyses is an empirical matter.  Some philosophers have called Koopmans’ thesis “methodological individualism”.  Students of elementary logic will recognize Koopmans’ reductionist requirement as an instance if the fallacy of composition, in which one attributes to a whole the properties of its components.  Thus just as the properties of water waves cannot be described exclusively or exhaustively in terms of the physical properties of constituent water molecules, so too for the economic waves of the business cycles cannot be describe exclusively or exhaustively in terms of the behavior of participant individuals.  Both types of waves may be described as “real”, even if the reality is not easily described as an “entity”. 

As it happens in the history of post-World War II economics, a reluctant pluralism has prevailed.  For many years the U.S. Department of Commerce, Bureau of Economic Analysis (B.E.A.) published the National Bureau’s business cycle leading-indicators with selections of its many cyclical time series and charts in their monthly Survey of Current Business, which is the Federal agency’s principal monthly periodical.  In 1996 the function was also taken over by the Conference Board, which calculates and releases the monthly Index of Leading Indicators based on Mitchell’s approach.  The index has been occasionally reported in national media such as The Wall Street Journal.  On the other hand the Cowles Commission’s structural-equation agenda has effectively conquered the curricula of academic economics; today in the universities empirical economics has become synonymous with “econometrics” in the sense given to it by Haavelmo.

Nevertheless the history of economics has taken its revenge on Koopmans’ reductionist agenda.  Had the Cowles Commission implemented their structural-equation agenda in Walrasian general equilibrium theory, the reductionist agenda would have appeared to be vindicated.  But the macroeconomics that was actually used for implementation was not a macroeconomics that is just an extension of Walrasian microeconomics; it was the Keynesian macroeconomics.  Even before Smith’s Wealth of Nations economists were interested in what may be called macroeconomics in the sense of a theory of the overall level of output for a national economy.  With the 1871 marginalist revolution economists had developed an economic psychology based on the classical rationality thesis of maximizing behavior, which enabled economists to use differential calculus to express and develop their theory.  And this in turn occasioned the mathematically elegant Walrasian general equilibrium theory that affirmed that the rational maximizing behavior of individual consumers and entrepreneurs would result in the maximum level of employment and output for the whole national macroeconomy.  The Great Depression of the 1930’s debunked this optimism, and Keynes’ macroeconomic theory offered an alternative thesis of the less-than-full-employment equilibrium.  This created a distinctively macroeconomic perspective, because it made the problem of determining the level of total output and employment a different one than the older problem of determining the most efficient interindustry resource allocation in response to consumer preferences as revealed by relative prices.

This new macro perspective also brought certain other less obvious novelties.  Ostensibly the achievement of Keynes’ theory was to explain the less-than-full-employment equilibrium by the classical economic psychology that explains economic behavior in terms of the heroically imputed maximizing rationality theses.  The economic historian Mark Blaug of the University of London writes in his Economic History and the History of Economics that Keynes’ consumption function is not derived from individual maximizing behavior, but is instead a bold inference based on the known relationship between aggregate consumer expenditures and aggregate national income. Supporters as well as critics of Keynes knew there is a problem in deriving a theory in terms of communities of individuals and groups of commodities from the classical theory set forth in terms of individuals and single commodities.

For example in Keynes’ macroeconomic theory saving and investment behaviors have a different outcome than in microeconomic theory, a difference known as “the paradox of saving”.  When the individual increases his saving he assumes his income will be unaffected by his action.  But when the aggregate population seeks to increase its savings, consumption is thereby reduced and consequently the incomes of others and perhaps themselves will be affected, such that in the aggregate savings are reduced.  Thus a motivated attempt to increase saving by individuals causes a reduction of their savings.  In his Keynesian Revolution the 1980 Nobel-laureate econometrician Lawrence Klein called attempts to derive aggregate macroeconomic relations from individual microeconomic decisions “the problem of aggregation”, and he notes that classical economists have never adequately solved this problem. One of the reasons that the transition to Keynes macroeconomic theory is called the “Keynesian Revolution” is recognition of a distinctive macro perspective that is not reducible to the psychological perspective in microeconomics, the rationality postulate that is its economic psychology.  An evident example is Keynes “law of consumption”, which he called a psychological law, a law that is ad hoc with no relation to the classical rationality postulate. Sociologists do not yet recognize any distinctively macro perspective and still require motivational analyses.

Joseph Schumpeter, a Harvard University economist of the Austrian school and a critic of Keynes, was one of those older economists who were immune from contagious Keynesianism.  In his History of Economic Analysis he regarded Walrasian general equilibrium analysis the greatest achievement in the history of economics.  And in his review of Keynes’ General Theory in Journal of the American Statistical Association (1936) he described Keynes’ “Propensity to Consume” as nothing but a deus ex machina that is valueless if we do not understand the “mechanism” of changing situations in which consumers’ expenditures fluctuate, and he goes on to say that Keynes’ “Inducement to Invest”, his “Multiplier”, and his “Liquidity Preference”, are all an Olympus of such hypotheses which should be replaced by concepts drawn from the economic processes that lie behind the surface phenomena.  In other words this expositor of the Austrian school of marginalist economics regarded Keynes’ theory as hardly less atheoretical than if Keynes had used data analysis.  Schumpeter would accept only a macroeconomic theory that is an extension of microeconomics.

But economists could not wait for the approval of dogmatists like Schumpeter, because the Great Depression had made them desperately pragmatic.  Keynesian economics became the principal source of theoretical equation specifications for macroeconometric modeling.  In 1955 Klein and Goldberger published their Keynesian macroeconometric model of the U.S. national economy, which later evolved into the elaborate WEFA macroeconometric model of hundreds of equations.  And this is not the only large Keynesian macroeconometric model; there are now many others, such as the DRI model, now the DRI-WEFA model, the Moody’s model and the Economy.com model.  These have spawned a successful for-profit information-consulting industry marketing to both business and government.  But there are considerable differences among these large macroeconometric models, and these differences are not decided by reference to purported derivations from rationality postulates or microeconomic theory, even though some econometricians still ostensibly subscribe to Haavelmo’s structural-equation programme and include relative prices in their equations.  The criterion that is effectively operative in the choice among the alternative business-cycle models is unabashedly pragmatic; it is their forecasting performance that enables these consulting firms to profit and stay in business.

1970 Nobel-laureate economist Paul Samuelson, who wrote in Keynes General Theory: Reports of Three Decades that it is impossible for modern students to realize the full effect of the “Keynesian Revolution” upon those of brought up in the orthodox classical tradition.  He noted that what beginners today often regard as trite and obvious was to us puzzling, novel and heretical.  He added that Keynes’ theory caught most economists under the age of thirty-five with the unexpected virulence of a disease first attacking and decimating an isolated tribe of South Sea Islanders, while older economists [like Schumpeter] were immune.

Muth’s Rationalist Expectations Agenda

After Muth’s papers, interest in the rational-expectations hypothesis died, and the rational-expectations lit­erary corpus was entombed in the tomes of the profession’s periodical literature for almost two decades.  Then unstable national macroeconomic conditions including the deep reces­sion of 1974 and the high inflation of the 1970’s created embarrassments for macroeconomic forecasters who relied upon the large structural-equation macroeconometric models based on Keynes’ theory.  These large models had been gratifyingly successful in the 1960’s, but their structural breakdown in the 1970’s occasioned a more critical attitude toward them and a proliferation of alternative views.  One consequence was the disinterment and revitalization of interest in the rational-expectations hypothesis.

Most economists today attribute these economic events of the 1970’s to the sudden quadrupling of crude oil prices in October 1973 imposed by the Organiza­tion of Petroleum Exporting Countries (O.P.E.C.).  But some economists chose to ignore the fact that the quadrupling of oil prices had induced pervasive and perverse cost-push inflation, which propagated throughout the nation’s transportation system from local delivery trucks to sea-going container ships and thus affected every product that the system carries.  Commercial econometric consulting firms addressed this problem by introducing oil prices into their macroeconometric models, a solution mentioned by Haavelmo in his 1944 paper; they had to be pragmatic to retain their clients.  These conditions were exacerbated by Federal fiscal deficits that were relatively large for the time and by the Federal Reserve Board’s permissive monetary policies under the chairmanship of Arthur Burns, which stimulated demand-pull inflation.  These macroeconomic policy actions became targets of criticism, in which the structural-equation type of models containing such fiscal and monetary policy variables was attacked using the rational-expectations hypothesis.

1995 Nobel-laureate economist Robert E. Lucas (b. 1937) criticized the traditional structural-­equation type of econometric model.  He was for a time at Carnegie-Mellon, and had come from University of Chicago, to which he has since returned.  Lucas’ “Econometric Policy Evaluation: A Critique” in The Phillips Curve and Labor Markets (1976) states on the basis of Muth’s papers, that any change in policy will systematically alter the structure of econo­metric models, because it changes the optimal decision rules underlying the statistically estimated structural parameters in the econometric models.  Haavelmo had addressed the same type of problem in his discussion of the irreversibility of economic relations, and his prescription for all occasions of structural breakdown is the addition of the missing vari­ables responsible for the failure.  Curiously, however, in his presidential address to the American Economic Association in 2003, five years before the onset of the Great Recession, Lucas proclaimed that macroeconomics has succeeded, because its central problem of depression prevention has been solved.  And in October 2008 with the onset of the Great Recession he is quoted by Time magazine as saying that everyone is a Keynesian in a foxhole.

2011 Nobel-laureate Thomas J. Sargent, an economist at the University of Minnesota and an advisor to the Federal Reserve Bank of Minneapolis joined Lucas in the rational-expectations cri­tique of structural models in their jointly authored “After Keynesian Macro­economics” (1979) reprinted in their Rational Expectations and Econometric Practice (1981).  They state that Keynes’ verbal statement of his theory set forth in his General Theory (1936) does not contain reliable prior information as to what variables should be excluded from the explanatory right-hand side of the structural equations of the macroeconometric models based on Keynes’ theory.  This is a facile statement since Keynes’ theory stated what explanatory factors should be included.  Sargent furthermore stated that neoclassical theory of optimizing behavior almost never implies either the exclu­sionary restrictions the authors find suggested by Keynes or those imposed by modern large macroeconometric models.  The authors maintain that the parameters identified as structural by current structural-equation macroecono­metric methods are not in fact structural, and that these models have not isolated structures that remain invariant.  This criticism of the structural-equation models is perhaps better described as specifically criticism of the structural-equation models based on Keynesian macroeconomic theory.  The authors tacitly leave open the possibility that non-Keynesian structural-equation business-cycle econometric models could nevertheless be constructed that would not be used for policy analysis, and which are consistent with the authors’ rational-expectations alternative.  

But while Lucas and Sargent offer the non-Keynesian theory that business fluctuations are due to errors in expectations resulting from unanticipated events, they do not offer a new structural-equation model.  They reject the use of expectations measurement data, and proposed a distinctive type of rational-expectations macroeconometric model.

Rejection of Expectations Data and Evolution of VAR Models

The rejection of the use of expectations measurement data antedates Muth’s rational-expectations hypothesis.  In 1957 University of Chicago economist Milton Friedman set forth his permanent income hypothesis in his Theory of the Consumption Function.  This is the thesis for which he was awarded the Noble Prize in 1976, and in his Nobel Lecture, published in Journal of Political Economy (1977) he expressed approval of the rational-expectations hypothesis and explicitly referenced the contributions of Muth, Lucas and Sargent.  In the third chapter of his book, “The Permanent Income Hypothesis”, he discusses the semantics of his theory and of measure­ment data.  He states that the magnitudes termed “permanent” are ex ante “theoretical constructs”, which he maintains cannot be observed directly for an individual consumer.  He says that only actual income expenditures and receipts during some definite period can be observed, and that these observed measurements are ex post empirical data, although verbal ex ante statements made by the consu­mer about his future expenditures may supplement these ex post data.  Friedman explains that his theoretical concept of per­manent income is understood to reflect the effect of factors that the income earner regards as determining his capital value, i.e., his subjective estimate of a discounted future income stream.

Friedman subdivides total measured income into a permanent part and a transitory part.  He says that in a large group the empirical data tend to average out, so that their mean average or expected value is the permanent part, and the residual transitory part has a mean average of zero.  In another statement he says that permanent income for the whole community can be regarded as a weighted average of current and past incomes adjusted by a secular trend, with the weights declining as one goes back further in time.  When this type of relationship is expressed as an empirical model, it is a type known as an autoregressive model, and it is the type that is very strategic for representation of the rational-expectations hypothesis in the VAR type of model in contrast to the structural-equation type of econometric model.

Muth does not follow Friedman’s neopositivist dichotomizing of the semantics of theory and observation.  In his rational-expectations hypothesis he simply ignores the idea of establishing any correspondence by analogy or otherwise between the purportedly unobserv­able theoretical concept and the statistical concept of expected value, and heroically makes the statistical con­cept of “expected value” the literal meaning of “psychological expectations.”  In 1960 Muth published “Optimal Properties of Exponentially Weighted Forecasts” in American Statistical Associa­tion Journal.  He referenced this paper in his “Rational Expectations” paper, but this paper contains no reference to empirically gathered expectations data. 

Muth says that Friedman’s determination of permanent income is “vague”, and he proposes instead that an exponentially weighted-average of past observations of income can be interpreted as the expected value of the income time series.  He develops such an autoregressive model, and shows that it produces the minimum-variance forecast for the period immediately ahead for any future time period, because it gives an estimate of the permanent part of measured income.  The exponentially weighted average type of model had been used instrumentally for forecasting in production planning and inventory planning by business firms, but economists had not thought that such autoregressive models have any economic significance.  Muth’s identification of the statistical concept of expected value with subjective expectations in the minds of the population gave the autoregressive forecasting models a new – and imaginative – economic relevance.  Ironically, however, the forecasting success or failure of these models does not test the rational-expectations hypothesis, because they have no relation to the neoclassical theory based on maximizing rationality theses with or without expectations.

Nearly two decades later there occurred the development of a more elaborate type of autoregressive model called the “vector autoregression” or “VAR” model set forth by Thomas J. Sargent in his “Rational Expectations, Econometric Exo­geniety, and Consumption” in Journal of Political Economy (1978).  Building on the work of Friedman, Muth and Lucas, Sargent developed a two-equation linear autoregressive model for consumption and income, in which each dependent variable is determined by multiple lagged values of all of the variables in the model.  This is called the “unrestricted vector autoregression” model.  It implements Muth’s thesis that expectations depend on the structure of the entire economic system, because all factors in the model enter into consideration by all economic participants in all their economic roles.  The VAR model dispenses with Haavelmo’s autonomy concept, since there is no attempt to identify the factors determining the preferences of any particular economic group, because on the rational-expectations hypothesis everyone considers everything.

In his “Estimating Vector Autoregressions Using Methods Not Based On Explicit Economic Theories” in Federal Reserve Bank of Minneapolis Quarterly Review (Summer, 1979), Sargent explains that the VAR model is not constructed with the same procedural limitations that must be respected for construc­tion of the structural-equation model.  Construction of the structural-equation model requires firstly that the relevant economic theory be referenced as prior information, and assumes that no variables may be included in a particular equation other than those variables for which there is a theoretical justi­fication.  This follows from Haavelmo's premise that the probability approach in econometrics is merely a testing method based upon application of the Neyman-Pearson statistical inference technique to equations having their specifications determined a priori by economic theory.  But when the rational-expectations hypothesis is implemented with the VAR model, the situation changes because expectations are viewed as conditioned on past values of all variables in the system and may enter all the decision func­tions. Therefore the semantics of the VAR model describes the much wider range of factors considered by the economic participants, a range that Simon deems humanly impossible.  Rational-expectations thus makes the opposite assumption more appropriate, namely that in general it is likely that movements of all variables affect behavior of all other variables, and all the econometrician’s decisions in constructing the model are guided by the statistical properties and performance characteristics of the model rather than by a priori theory.  Sargent also notes that VAR models are vulnerable to Lucas’ critique, and that these models cannot be used for policy analyses.  The objective of the VAR model is principally accurate forecasting.

2011 Nobel-laureate Christopher A. Sims of Yale University makes criticisms of structural-equation models similar to those made by Lucas and Sargent. Sims, a colleague of Sargent while at the University of Minnesota, advocates the rational-expectations hypothesis and the development of VAR models in his “Macroeconomics and Reality” in Econometrica (1980).  He also states that the coefficients of the VAR models are not easily interpreted for their economic meaning, and he proposes that economic information be developed from these models by simulating the occurrence of random shocks and then observ­ing the reaction of the model.  Sims thus inverts the relation between economic interpretation and model construction advanced by Haavelmo: instead of beginning with the theoretical understanding and then imposing its structural restrictions on data in the process of constructing the equations of the empirical model, Sims firstly constructs the VAR model from data, and then develops an understanding of economic structure from simulation analyses with the model.  He thus uses VAR model interpretation for discovery rather than just for testing.

In the Federal Reserve Bank of Minneapolis Quarterly Review (Winter, 1986) Sims states that VAR modelers have been using these models for policy analysis in spite of caveats about the practice.  Not surprisingly this policy advisor to a Federal Reserve Bank does not dismiss such models for policy analysis and evaluation.  He says that use of any models for policy analysis involves making economic interpretations of the models, and that predicting the effects of policy actions thus involves making assumptions for identifying a structure from the VAR model.  For this purpose he uses shock simulations with the completed model. But shock simulations admit to more than one structural form for the same VAR model, and he offers no procedure for choosing among alternative structures.

Litterman’s BVAR Models and Discovery System

In his “Forecasting with Bayesian Vector Autoregression: Four Years of Experience” in the 1984 Proceedings of the American Statistical Association, also written as a Federal Reserve Bank of Minneapolis Working Paper, Robert Litterman, at the time a staff economist for the Federal Reserve Bank of Minnea­polis, who has since moved to Wall Street, says that the original idea to use a VAR model for macroeconometric forecasting at the Minneapolis Federal Reserve Bank came from Sargent.  Litterman’s own involvement, which began as a research assistant at the Bank, was to write a computer program to estimate VAR models and to forecast with them.  He reports that the initial forecasting results with this unrestricted VAR model were so disappointing, that a simple univariate autoregressive time series model could have done a better job, and it was evident that the unre­stricted VAR models are not successful.  In his “Are Forecasting Models Usable for Policy Analy­sis?” Litterman noted that the unrestricted VAR model is overparameterized, i.e., attempted to fit too many variables to too few observations.  This overparameterization of regression models is a well known and elementary error.  Avoiding it led to his develop­ment of the Bayesian VAR model, which became the basis for Litterman’s doctoral thesis titled Techniques for Forecasting Using Vector Autoregression (University of Minnesota, 1980).

In the Bayesian vector autoregression or “BVAR” model, there is a prior matrix that is included in the ordinary least squares estimation of the coefficients of the model, and the parameters that are the elements in this prior matrix thereby influence the values of the estimated coefficients.  This prior matrix is an a priori imposition on a model like economic theory in the conventional structural-equation econometric model as described by Haavelmo, because it has the desired effect of restricting the number of variables in the model.  But the prior matrix is systematically revised as part of the constructional procedure. Litterman argues that in the construction of structural-equation models the economist rarely attempts to justify the exclusion of variables on the basis of economic theory.  He says that the use of such exclusionary restric­tions does not allow a realistic specification of a priori knowledge.  His Bayesian specification, on the other hand, includes all variables in the system at several time lags, but it also includes the prior matrix indicating uncertainty about the structure of the economy.  Like Sargent, Litterman is critical of the adequacy of conventional macroeconomic theory, and he maintains that economists are more likely to find the regularities needed for better forecasts in the data than in some a priori economic theory.  Thus his objective is explicitly discovery by data analysis.

The difficult part of constructing BVAR models is cons­tructing a realistic prior matrix, and Litterman describes his procedure in his Specifying Vector Autoregression for Macroeconomic Forecasting, a Federal Reserve Bank of Minnea­polis Staff Report published in 1984.  His prior matrix, which he calls the “Minnesota prior”, suggests with varying degrees of uncertainty that all the coefficients in the model except those for the dependent variables’ first lagged values are close to zero.  The varying degrees of uncer­tainty are indicated by the standard deviations calculated from benchmark out-of-sample retrodictive forecasts made with simple univariate models, and the degrees of uncertainty are assumed to decrease as the time lags increase.  The parameters in the prior matrix are calculated from these standard deviations and from “hyperparameter” factors that vary along a continuum that indicates how likely the coefficients on the lagged values of the variables deviate from a prior mean of zero.

One extreme of this continuum is the univariate autoregres­sive model, and the opposite extreme is the multivariate unrestricted VAR containing all the variables in each equation of the model.  By varying such hyperparameters and by making successive out-of-sample retrodictive forecasts, it is possible to map different prior distributions to a measure of forecasting accuracy according to how much multivariate interaction is allowed.  The measure of accuracy that Litterman uses is the determinant matrix of the logarithms of the out-of-sample retrodic­tive forecast errors for the whole BVAR model.  Forecast errors measured in this manner are minimized in a search along the continuum between univariate and unrestricted VAR models.  Litterman calls this procedure a “prior search”, which resembles Simon’s heuristic-search procedure in that it is recursive, but Litterman’s is explicitly Bayesian.  The procedure has been made commerci­ally available in a computer system called by a memorable acronym, “RATS”, which is marketed by VAR Econometrics Inc., Minneapolis, MN.  This system also contains the ability to make the shock simulations of the type that Sims proposed for economic interpretation of the BVAR models.

Economists typically do not consider the VAR or BVAR models to be econ­omic theories or “theoretical models”.  The concept of the­ory in economics, such as may be found in Haavelmo’ paper, originates in the romantic philosophy of science, according to which the language of theory must describe the rational decision-making process in the economic participants’ attempts to max­imize utility or profits.  In other words the semantics of the theory must describe the motivating mental deliberations of the economic participants whose behavior the theory explains, and this amounts to the a priori requirement for a mentalistic ontology.  The opposing view is that of the positivists, or more specifically the Behaviorists, who reject all theory in this sense, except that behaviorists do not make economic models.  Both views are similar in that they have semantic concepts of theory. 

The contemporary pragmatists on the other hand admit any semantics/ontology into theory, but reject all a priori semantical and/or ontological criteria for scientific criticism, whether mentalistic or antimentalistic, even when these criteria are built into such meta­linguistic terms as “theory” and “observation.”  Contemporary pragmatists instead define theory language on the basis of its use or function in scientific research, and not on the basis of its semantics or ontology: according to the pragmatist view theory language is that which is proposed for testing.  Theory is dis­tinguished by the hypothetical attitude of the scientist toward a proposed solution to a problem.  Therefore, according to the contemporary pragmatist philosophy of science, Litterman’s system is a discovery system, because it produces economic theories, i.e., models proposed for testing.

Ironically the rejection of the structural-equation type of econometric model by rational-expectations advocates is a de facto implementation of the contemporary pragmatist philosophy of science.  Sargent described rational expecta­tions with its greater fidelity to the maximizing postulates as a “counterrevolution” against the ad hoc aspects of the Keynesian revolution.  But from the point of view of the prevailing romantic philosophy of science practiced in economics, their accomplishment in creating the BVAR model is a radical revolution in the philosophy and method­ology of economics, because ironically there is actually no connection between the rational-expectations thesis and the BVAR model.  Rational expectations play no rôle in the specification of the BVAR model.  Empirical tests of the model could not test the rational-expectations “hypothesis” even if it actually were an empirical hypothesis instead of merely an economic dogma.  And their exclusion of empirical expectations measurement data justifies denying that the model even describes any mental expectations experienced by the economic participants.  The rational-expectations hypothesis associated with the BVAR models is merely a decorative discourse, a fig leaf giving the pragmatism of the BVAR models a fictitious decency for romantics.

The criterion for scientific criticism that is actually operative in the BVAR model is perfectly empirical; it is forecasting performance.  And it is to this cri­terion that Litterman appeals.  In Forecasting with Bayesian Vector Autoregressions: Four Years of Experience he des­cribes the performance of a monthly national economic BVAR model constructed for the Federal Reserve Bank of Minnea­polis.  He reports that during the period 1981 through 1984 this BVAR model demonstrated superior perform­ance in forecasting the unemployment rate and the real GNP during the 1982 recession, which up to that time was the worst recession since the Great Depression of the 1930’s.  The BVAR model made more accurate forecasts than three leading struc­tural models at the time: Data Resources (DRI), Chase Econometrics, and Wharton Associates (WEFA).  However, he also reports that the BVAR model did not make a superior forecast of the inflation rate as measured by the annual percent change in the GNP deflator.

Thereafter Litterman continued to publish forecasts from the BVAR model in the Federal Reserve Bank of Minnea­polis Quarterly Review.  In the Fall, 1984, issue he fore­casted that the 1984 slowdown was a short pause in the post-1982 recession, and that the national economy would exhibit above-average growth rates in 1985 and 1986.  A year later in the Fall 1985 issue he noted that his BVAR model forecast for 1985 was overshooting the actual growth rates for 1985, but he also states that his model was more accur­ate than the three large leading structural-equation models named above.  In the Winter 1987 issue two of his sympathetic colleagues on the Federal Reserve Bank of Minneapolis research staff, William Roberds and Richard Todd, published a critique reporting that the BVAR model forecasts of the real GNP and the unemployment rate were overshooting measurements of actual events, and that competing structural models had performed better for 1986. Several economists working in regional economics have been experimenting with BVAR modeling of state economies. Such models have been used by the District Federal Reserve Banks of Dallas (Gruben and Donald, 1991), Cleveland (Hoehn and Balazsy, 1985), and Richmond (Kuprianov and Lupoletti, 1984), and by the University of Connecticut (Dua and Ray, 1995).  Only time will tell whether or not this new type of modeling survives.

Reports in the Minneapolis Bank’s Quarterly Review contain descriptions of how the BVAR national economic model is revised as part of its continuing development.  In the Fall 1984 issue the model is described as having altoget­her forty-six descriptive variables and equations, but it has a “core” sector of only eight variables and equations, which receives no feedback from the remainder of the model.  This core sector must make accurate forecasts, in order for the rest of the model to function accurately.  When the BVAR model is revised, the important changes are those made to the selection of variables in this core sector.  Reliance on this small number of variables is the principal weakness of this type of model.  It is not a vulnerability that is intrinsic to this type of model, but rather is a concession to computational limits of the computer, because construction of the Bayesian prior matrix made great demands on the computer resources available at the time.  In contrast the structural-equation models typically contain hundreds of different descriptive variables interacting most often as simultaneous-block-recursive models.  Improved computer hardware design will enable the BVAR models to be larger and contain more driving variables in the core.  But in the meanwhile they must perform heroic feats with very small amounts of descriptive information as they compete with the much larger structural-equation models containing much greater amounts of feedback information.

Unlike Simon’s simulations of historically significant scientific discoveries, Litterman does not separate the merit of his computerized discovery procedures for constructing his BVAR models form the scientific merit of the BVAR models he makes with his Bayesian-based discovery system.  Litterman is not recreating what Russell Hanson called “catalogue-science”, but is operating at the frontier of “research science.”  Furthermore, the approach of Litterman and colleagues is much more radical than that of the conventional economist, who needs only to propose some new “theory”, and then apply conventional structural-equation econometric modeling techniques.  The BVAR technique has been made commercially available for microcomputer use, but still the econometrician constructing the BVAR model must learn statistical techniques that he had not likely been taught in his professional education.  Many economists fail to recognize the pragmatic character of the BVAR models, and reject the technique out of hand, since they reject the rational-expectations hypothesis.

The bottom-line takeaway from the rational-expectations succession of pragmatic modeling experiments in economics is that data-driven model construction can produce more accurate forecasting models than the traditional structural-equation modeling with its presumptuous a priori romantic “theory” that still haunts the halls of academic economics.

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