这本书经典，对城市经济学感谢兴趣的研究生，必读、精读！请看城市经济学著名教授的书评吧。

Most research books I receive end up on my shelf and quietly gather dust until eventually disposed of. I also have a few good books and dust does not pile on them. They are full of useful information and I often return to them. My bookshelf also contains a tiny number of great books. They gave me something else. They changed the way I think; they changed the way I work; they make me better.

By this personal definition of what it means to be good, Ed Glaeser’s recent book on cities, agglomeration, and spatial equilibrium is certainly a “good” book. Anyone who needs a quick reminder about some aspect of urban economic theory or some fact about the evolution of U.S. cities is likely to find it there. In only 244 pages of text—about a third the length of a normal textbook—Glaeser explores more than 50 models. Chapter 3 alone contains 16 plots reporting partial correlations for U.S. cities. For these reasons alone, this book will not gather dust on my shelf. I will return to it often.

However, for many readers, the huge amount of information that is packed in the book in a way that is easy to access will not be its main attraction. This book is actually great and will join a very select club on my bookshelf. It offers a fantastic lesson about how to do research. It gives us a unique peek into the thought and work process of the premier producer of knowledge in urban economics over the last 20 years. Since his first breakthrough, “Growth in Cities” (Glaeser et al., 1992), Ed Glaeser has written an amazing array of journal articles, book chapters, and other pieces. Many of these pieces are “hits” that have been published in prestigious journals, which are taught in graduate or undergraduate courses, and have gathered an extraordinary amount of citations and attention. This book reveals his secrets about how he did it.

Before reading this book, I was convinced that his achievements were out of reach for nearly everyone, myself included. His brand of empirical work seemed to rely so much on some inspiration and a creativity that most of us lack. I was wrong. This book made it clear to me. The extraordinary output of Ed Glaeser in the last 20 years is largely due to the systematic and relentless use of a small set of theoretical ideas to conduct empirical work. No more. No less. Of course, some of his characteristics such as boundless energy and great communication skills are harder to replicate and there may not be any recipe for that. However, this book makes the case that empirical work is so much better when it relies on the disciplined use of robust insights from simple theory.

It is not an accident that Glaser’s work has been predominantly empirical while this book tilts heavily toward theory. The book shows what the process is. Put theory first, bring it to the data, take a second look at the theory, extend it in the most obvious direction or amend it, go back to the data, etc. Glaeser’s journal articles only give us the end product that is very data intensive. This book allows the reader to see what is behind the set. There is a lot of economic theory. As a recipe for producing new knowledge, this systematic movement to and fro between theory and empirics may not be as glamorous as relying on pure creativity or divine inspiration, but it is I believe what has made Ed Glaeser so extraordinarily effective.

Let me dwell further on this idea by going into the details of the book. After an introductory chapter, chapter 2 is concerned with the internal structure of cities. As could be expected, it starts with an exposition of the Alonso–Muth–Mills model (AMM), “the” classic piece of urban theory that launched the field. Glaeser does not try to give the most general and comprehensive version of the AMM model first. Instead, he starts with a simple version of it, full of restrictive assumptions. It is a useful didactic device. However, it is much more than that. First, it helps the author hammer home the point that the core of the model is really the notion of spatial equilibrium where consumers choose one location among many. The second reason for starting with the simplest model is that the simplest model is enough to generate a key empirical prediction. There should be a price gradient as one moves away from the city center. Of course, economists have tried for a long time to measure those price gradients.

The data indeed support the existence of a price gradient but it is quite weak. The typical reaction of an urban economist is then to discard the mono centric model as a useful piece of theory and turn to a-theoretic empirical work with the additional justification that the theory of multi centric cities is messy. Not Ed Glaeser. He indeed acknowledges the weak gradient, and he also emphasizes differences in gradients across U.S. cities. Then he wonders about what could be at the root of these empirical findings. The most natural explanation within the AMM framework regards the existence of different transport modes. After this, he extends the AMM model further to consider an endogenous amount of land consumption, which leads to the prediction of a density gradient, a prediction he also examines. Then he introduces housing into the model and derives some interesting implication regarding how changes in building technology will affect cities. A beauty of the chapter is that the nice insight that urban sprawl might be due in part to more efficient building technologies is not the result of supernatural creativity. Instead, it is an outcome of being disciplined, going for the most natural and straightforward explanation, and amending it in the simplest way when it is contradicted by the data.

At this point, the chapter has laid the ground for an exploration of the location of urban dwellers by income. A simple extension of the AMM model shows that under some condition regarding the income elasticity of the demand for land, the rich will live in the periphery of cities while the poor will live downtown. Even though this prediction about patterns of urban location by income is broadly confirmed in U.S. cities, it cannot be explained by a simple AMM extension to heterogeneous residents. The income elasticity of the demand for land is nowhere large enough. The second most appealing explanation of location patterns by income has to do with amenities. Glaeser naturally, and unsurprisingly, turns to it. At the end of the chapter, all these elements are put together to offer a very insightful story about job decentralization and the evolution of cities. Job decentralization and urban sprawl are of course the big story for U.S. cities. Nonetheless, what the chapter makes clear is that the convincing argument about the evolution of cities that comes at the end is neither the product of genius nor some quickly made-up conjecture. It is instead the conclusion of the patient and systematic exploration that started with the simplest form of the AMM model. Glaeser proceeds in the same way in the other chapters. In chapter 3 he looks at cross-city differences. The starting point this time is the Rosen–Roback framework instead of theAMMmodel.However, at the core of the Rosen–Roback framework there is the same notion of spatial equilibrium. Themain difference is that residents now choose their location from among cities endowed with different amenities instead of choosing one residential lot within a single city. As in chapter 2, Glaeser distils some great insights. The reading of the chapter highlights that these insights are not accidental but come instead from the systematic and critical exploration of the Rosen Roback framework.

Chapter 4 covers agglomeration economies. Again, the set is at first unsurprising. The chapter starts with the fact that nominal incomes are higher in cities. Trying to understand why this is so leads the author to lay down a simple model of location choice with agglomeration effects and natural advantage. The key result is that we cannot take it for granted that higher nominal wages must be the outcome of agglomeration economies. As Glaeser shows in this chapter, making a rigorous case for agglomeration economies is actually hard. The chapter also offers a quick exposition of Krugman’s new economic geography before turning to the microeconomic foundations of agglomeration economies. Following the Marshallian tradition, Glaeser looks at the

division of labor, labor market pooling and matching, and learning. The next logical step is then to

wonder which of these mechanisms is actually the most relevant. A very hard question. The chapter again ends up by using many of the elements explored prior to the conclusion to come up with an insightful story about the effect of modern communication technologies on cities. Yet again, the sexy stuff comes at the end and is the outcome of patient reflection and the systematic exploration of many aspects that are all too often dismissed by many researchers as mundane.

    Chapter 5 is another example of the same “method,” applied this time to urban social problems in the United States. Only chapter 6 differs. It is about urban policies and it is much more normative in its focus. This chapter, despite the importance of the topic, is less satisfactory and does not rely on prior research as much as the other chapters. This weakness leads me to my next point. One may argue that, despite being great, this book is nonetheless imperfect. Instead, I would like to make the case that its greatness and usefulness comes in part from the imperfections.

More precisely, the book is imperfect in three ways. As already noted, the first issue is that some chapters are more satisfactory than others. While the reader may feel overwhelmed by facts and empirical results in chapter 3 while trying to understand cross-city differences, the same facts and empirical results are conspicuously lacking from chapter 6 about urban policy. This is a reflection of the state of the literature. These gaps in the book are not Glaeser’s fault unless one wants to blame him for not having advanced the frontiers of knowledge to the same point on all fronts. The gaps are clear opportunities for readers to seize and advance knowledge themselves. From chapter 6, I actually take away the idea that we need the same sort of systematic data about urban policies as we have about other aspects of cities. A group at the Wharton School of the University of Pennsylvania has started to collect systematic information about zoning regulations. The effort is very useful but it will not be enough. The theories highlighted in chapter 6 make clear that much more is needed. A lot of new interesting research could be done with some information about local redistributive policies and many other aspects of municipal public finance.

The second criticism that can be made is that the theory is not really exposed in the same way as advanced microeconomics courses teach theory in graduate school. For instance, the domain of functions is usually ignored. When solving for the equilibrium, second-order conditions are not mentioned unless they actually play a role. Notations are not always defined elegantly. There are sometimes denominators like “d d” to denote a derivative with respect to a variable d. While some may moan that such modeling is not rigorous enough and “too quick,” I think there are some useful lessons here. First, I interpret Glaeser as saying that although theory is the senior partner to empirics, the objective is not to do theory for the sake of theory. Someone interested in theoretical perfection should go elsewhere. Second, spending more time on the details of the model would be a distraction. It would obscure what I think is the great strength of the book. Its fast pace is what allows the reader to see what goes on inside the author’s mind.

The third criticism one can make is that it makes no attempt to be exhaustive in its coverage. For instance, New Economic Geography only gets a couple of pages to expose Krugman’s 1991 model and that is it. The book is highly personal and makes no apology for that. However, provided one does not misinterpret Glaeser’s objective, this is a plus rather than a minus. Trying to be more exhaustive would dilute the possibility for the reader to observe the author’s thought process in its raw form. Leaving those other models completely aside makes it clear where the gaps are. Alternatively, progress will also be achieved by reexamining the weakest parts of the various frameworks that Glaeser uses. The notion of spatial equilibrium is indeed fundamental. However, Glaeser nearly always considers it in its simplest form of static utility equalization across locations. Although it might be a reasonable long-run first-order approximation for the United States, I expect the world to be full of frictions. Trying to understand which ones really matter and what their implications are strikes me as a great avenue for future research. Hence, there is much to gain for young ambitious researchers in applying Glaeser’s method to other models or remedying weaknesses in the frameworks he is using rather than attempt to superficially copy his style.

To sum up, this is a book that everyone should read. The best time to read it is before starting new research. As such it should be compulsory reading for any starting Ph.D. student thinking about doing applied work in urban economics. Although it is filled with facts and models, the book is not a textbook and people should not think about it as such. It is a book about “methods.” It shows how the author could produce so much pioneering research by working very hard and following simple theory with ruthless discipline. It is a great lecture and a great lesson. Beyond the results, it teaches us how to do research. There might be other ways to do urban economics, of course, but Ed Glaeser’s method has passed the market test. At the core of this book, there is a fundamental message. Theory matters. Existing empirical work all too often forgets that.

Gilles Duranton

Department of Economics

University of Toronto