In 1973, Harry W. Richardson, a urban economist at the University of Kent, expressed concern about “some uses of mathematical models in urban economics.” His attack was directed at two 1972 congestion models developed by Robert Solow and James Mirrlees. Solow’s model was a typical constrained optimization program in which consumers choose their residential location (space and distance from center) under cost and congestion constraints. The state has to decide how much space to allocate to housing and roads. Slow solved the program with differential equation techniques and provided a numerical example. Mirrlees derived the conditions for optimum town size by maximizing a continuous social utility function with population density under consumption and population constraints. While the use of Lagrange multipliers was anything but new in 70s economics, their import into urban models was.
Richardson complained that Mirrleess and Solow’s math required forcing oversimplified assumptions into the model (homogeneity, linearities, perfect competition and similar city sizes). As the result, most of their conclusions – rent is a decreasing function and space occupied an increasing function of distance from the city center, etc – were, in spite of mathematical sophistication, somewhat trivial to urban economists. And the policy traction of the models was disappointing :
The key impulse to urban economic research is … the urgent policy needs of how to handle and control metropolitan cities. A danger in papers of the kind discussed here is that they are likely to distract the attention of researchers away from the policy end of the spectrum towards the mathematical modeling end …This would be a good thing if the models developed were capable of aiding policy solutions, but my fear is that … the choice of model structures will be determined by their capacity to yield to mathematical tricks, and that this implies the most abstracts and simple cases. It would be a disaster if a policy-oriented field such as urban economics went the way of growth theory
It was not every math that Richardson opposed, but one he explicitly associated with “MIT economics.” Two other venues seemed more promising, he explained (no less associated with MIT, ironically):
The much maligned Jay Forrester has words of wisdom on this point: ‘Nonlinearity is easy to handle once we stop demanding analytical solutions to systems of equations and accept the less elegant and more empirical approach of system simulation.’ Forrester’s own urban system model has been rightly criticized – its economics is so bad, but it doesn’t mean his general approach was wrong […] It’s interesting that a recently proposed urban econometric model (Engle, Fisher, Harris and Rothenberg 1972), although it has not escaped criticism, aims to deal with many of the important problems in urban economics difficult to incorporate in the strictly mathematical models.
Solow and Mirrlees fired back. The former claimed that policy relevance was not the direct purpose of his paper, and offered his usual defense of simplified “toy-models”:
After all, what one expects from pure theory is a partial hint as to how complex systems might behave, and some understanding of the inferential links that make it so. I once described simple mathematical models as ‘reconnaissance exercises’ and that is as true in urban economics as elsewhere. Simplifying assumptions are not an excrescence on model building; they are its essence. Lewis Carroll once remarked that a map on the scale of one-to-one would serve no purpose […]
I think he has much to learn about the strategy and tactics of economic theory…. one possible strategy is the construction of a variety of pencil-and-paper theoretical models, each trying to isolate one or a few aspects of the problem and running the risk that omitted interactions might matter a lot. The other is the construction of large-scale simulation models which can take account of many more variables and interactions, at the cost that no one can fully understand what is happening in the bowels of the machine. I would have thought that all sensible people regarded these two approaches as complementary.
Mirrlees likewise criticized Richardson’s comparison with Forrester’s model:
Greater details brings with it greater precision, greater dependence on the particularities of specification. Particularly in a simulation (of the Forrester type, say) it is very hard to assess critically the conclusions of particular runs of the model, because we cannot perceive the way in which the particular specification determines the results. Changing a few parameters does not help, for it is deeper aspects of the specification that are likely to be in question. Surely it is a principle of very general application that more information. If Mr Richardson wants urban economics to be ‘policy-orientated,’ he should welcome the simple models, and the invasion by theoretical welfare economics.
In a rejoinder, Richardson conceded that “there is no dispute … about the role and need for economic theory,” but he did not relent on his idea that the choice of models should be informed by policy tractability rather than formal beauty :
“All I ask of the theorists is that they exercise some discrimination in their selection of problems for analysis, be guided less ‘by logical curiosity than by taste for relevance’ (professor Sen), and frame their researches in a way that does not lead to the divorce between formal theory and policy applications which had held back progress in some other branches of economics. The progeny of aggregate growth analysis is a terrible warning of what can happen when the theorists become too incestuous.”
In January 2015, Paul Romer launched an all-out attack of what he saw as degenerated uses of mathematical models in growth economics, some he called “mathiness.” His ire was directed at two price-taking growth models by Lucas, and McGrattan and Prescott. If economists’ lack of interest in their own history condemns them to perpetually reenact old controversies, this is not without irony. Richardson would have probably not endorsed Romer’s own brand of math, and Romer would have unreservedly sided with Mirrlees and Solow. Yet both Romer now and Richardson then accused their opponents of using math as a smokescreen, though Richardson targeted abstraction, while Romer instead focuses on the inconsistency between models and conclusions. Other lessons drawn from the re-enactment of this old debate are:
- It’s not so much about the uses of math, it’s about the uses of theory and about modeling strategies
Note how quickly the debate switched from “which math” to “which theory” in 1973. The key issues are 1) how much simplification should theoretical models exhibit and 2) how to identify causality. Solow and Mirrlees believed that simple models are necessary to understand causal relationships. Richardson prioritized models that reproduce complex interactions. Similar debates had been carried on in the following decades, with the development of calibration, reduced-form econometrics and RCTs. The 2015 mathiness debate has likewise quickly evolved into an assessment of theoretical models, and their relevance to real world issues.
2. When it’s about the use of theory, it’s about the status of the field/science
The early 1970s was a time of transition for economics. A theoretical “core” (optimization and general equilibrium) had stabilized, and only those applied field endorsing the core were considered as legit science. The 1973 debate reflects urban economics’s difficult normalization, a struggle also found in development economics at that time.
Urban economics was then the hottest field – it was almost given an independent JEL code during the 1966 revision of the classification, and the Journal of Urban Economics had just been created. Yet, the many efforts to provide a unified theoretical foundation to the development of cities, location decisions or housing prices had hitherto failed, and new questions were constantly emerging: racial segregation, congestion, urban decay, or local finance. At the turn of the 1970s, the field embodied a collection of seemingly irreconciliable questions, models, methods and research traditions. It spanned Walter Isard’s “regional science” at Penn, the application of standard microeconomic tools to study location decisions (Alonso-Muth-Wingo in the 60s), a wealth of metropolitan studies involving simulation models (Lowry’s model of Pittsburg, Forrester), system analysis or cost-benefit (Kain-Meyer-Wohl study of LA transportation at RAND), General Equilibrium-based large scale model (Rothenberg-Harris on the Boston area), or marxist explanations of racial segregation (Edel).
None of these frameworks had yet come to dominate urban economics. Data-based simulations were extremely sensitive to small changes in the parameters and hypotheses, which, it was believed, could be fixed with better theoretical foundations. Yet theoretical models of the Alonso-Muth or Solow-Mirrlees type were perceived as too simplistic. Disappointment with large scale models of cities loomed even larger. Richard Muth found the Rothenberg model too ambitious and of little help for Boston planners, and Perloff confessed, in a 1973 survey, that all these models “had little impact on the world with which they were concerned.”
3. It’s not only about theory vs empirical work, it’s also about policy relevance, the current policy regime and policy-makers’ demands for expertise
Policy-relevance was Richardson’s main criterion to judge the quality of a model. Though Solow and Mirrlees countered with a defense of simple models as “reconnaissance exercices,” policy was clearly on their mind too. The social context made the pressing demands of the civil society impossible to forget. But this policy orientation was also built-in the field’s history: urban economics was a field thoroughly engineered by policy-makers and foundations rather than economists themselves.
Crucial to urban economics’ takeoff was a 1959 grant the Ford Foundation awarded to Resource for the Future’s alumni Lowdon Wingo and Harvey Perloff for the establishment of a Committee on Urban Education. The two researchers aimed at the “conscious development of a new academic field” and by 1969, the program was an institutional success, with 50 graduate programs created and several textbooks published. The Ford’s instance that an “analytical framework” be developed was in line with Johnson’s War on Poverty, its legal activism and the “research-intensive structure” of the Great Society.
Ford’s focus however quickly shifted after the Watts riots. In 1967, the foundation awarded $10 millions to Columbia, Chicago, Harvard and MIT (these “urban grants” were renewed in 1970). This time, Ford’s director McGeorges Bundy explicitly required that the research funded provide “a direction for effective action on its problems.”
The “urban policy seminar” MIT economists set up in the Fall of 1970 thanks to MIT urban grant did not met Ford’s requirements. At the inaugural seminar, “it was agreed that the emphasis of the seminar will be analytic and methodological, rather than policy-oriented,” the minutes read. Solow, Mirrlees, and Rothenberg’s models grew out of these meetings. Yet, by 1973, the initial optimism had waned. It had become clear that the grant would not be renewed. Nixon had appointed Havard political scientist Edward Banfield, author of The Unheavently City, to review Johnson’s Model Cities program, which unsurprisingly had led to its dismantlement. Urban economists were worried; the need to demonstrate theoretical viability and policy relevance was pressing, creating discussions, tensions, debates.
Similar tensions and debates have been reported lately. Dissecting the 1973 debate suggests directions to move beyond the simplistic “it’s the 2008 crisis” explanation. The mathiness debate might be a sign that there is a paradigm shift under way in economics, a shift from a theory-driven to a tool-driven framework, or that the “core” is fragmenting. It may also signal a change in US’s policy regime, or citizens’ perception of economists.