A brief intellectual biography
But a very long blog post. I hope this will be of some value to younger researchers.
In the summer of 1986, my personal life had hit rock bottom and I decided to immerse myself in economic research, as a form of therapy. That year I came up with most of the ideas that I’ve used throughout my career. Here’s how I did it.
1. As a teenager, I had greatly enjoyed reading Friedman and Schwartz’s Monetary History of the United States, and this led me to spend a lot of time looking at old macro data sets once I got out of grad school. Fortunately, I have a very good memory for numbers, or more precisely data (not phone numbers). I also spent a lot of time reading theoretical papers, and considering whether the theories seemed to match my understanding of the “stylized facts”, which means the broad trends in the data.
One set of articles discussed how sticky-wage theories of the business cycle were not very useful, because the real wage did not move countercyclically, as predicted by these theories. The sticky-wage theory predicted that wages would fall more slowly than prices during a depression, which would make the real wage go up (i.e. countercyclical.) The false assumption that real wages are not countercyclical still underlies New Keynesian economics.
I knew that real wages were highly countercyclical during the period before WWII, and wondered why modern researchers had reached different conclusions. When I looked at the modern studies, I found they were strong influenced by real wages being highly procyclical during “supply shocks” like 1974 and 1980. I then realized that the original sticky-wage theory of cycles was based on the idea that recessions were caused by demand shocks, which caused both prices and output to fall at the same time. In contrast, if prices rose as output fell then sticky nominal wages would make for procyclical real wages. Real wages would fall during (inflationary) recessions.
Steve Silver and I then wrote a paper showing that real wages tended to be strongly countercyclical when the economy was hit by a demand shock and highly procyclical when the economy was hit by a supply shock. The overall pattern was ambiguous. The paper eventually got published in the JPE in 1989, and I vaguely recall that a couple of intermediate macro texts cited the paper (Mankiw’s and Bernanke’s?)
This study is what eventually led me to my “never reason from a price change” obsession, although I didn’t really understand the broader implications of that problem until the Great Recession, when I also applied the idea to interest rates. Elsewhere I’ve argued that the Great Recession was caused by two types of reasoning from a price change. First, the Fed wrongly assumed that the high inflation of mid-2008 was evidence of possible excess demand, and second they assumed that the low interest rates of 2008 reflected easy money.
My 1986 research also made me realize that NGDP was a better indicator of economic overheating than price inflation.
Punch line: Always think about whether the stylized facts are consistent with the models you examine. And put the greatest weight on the stylized facts from the interwar period, when the shocks were the biggest and most easily identified. If you are a young macroeconomist, you should memorize all the important interwar macro data.
2. During 1986, there was increasing disenchantment with traditional monetarism, and a search for alternative approaches. The “New Monetary Economists” discussed a price of money approach—as opposed to the monetarists’ quantity of money approach (M) and the Keynesian rental cost of money approach (i). Ideas being discussed included Mundell’s fixed exchange rates, gold price pegging, as well as targeting the price of a basket of actively traded commodities.
I understood that a commodity basket had advantages over a single good like gold, and wondered why we couldn’t just target the entire CPI. The problem, of course, was sticky prices and policy lags, which make it harder to target the overall CPI basket than a few simple commodities with flexible prices.
The solution was immediately obvious; target a CPI futures contract. This overcomes the policy lag issue that Friedman worried about, and also incorporates some of the rational expectations/efficient markets ideas that I had recently studied at Chicago. By the time I published the paper in 1989 (Bulletin of Economic Research), the CPI futures market had become a NGDP futures market.
Punch Line: An optimal policy is a policy that the market expects to succeed.
3. I was very interested in economic history, and read a paper by McCloskey and Zecher that was critical of the Friedman and Schwartz interpretation of the Great Depression. McCloskey and Zecher argued that national monetary policy is endogenous under an international gold standard, and individual central banks have little impact on the local price level (i.e. value of gold.) I found their paper to be quite impressive, which annoyed me because I was a big fan of Friedman and Schwartz.
So in 1986, I set out to revisit this issue from the ground up. I realized that traditional models featuring things like gold flows were not adequate, as a gold flow would have no first order effect on the global price level, and the fundamental problem during the Great Depression was worldwide deflation.
I began by getting all the accounting data, to better understand the problem. Almost immediately it became apparent that the Great Deflation of 1929-33 was a gold demand problem, as global gold supplies rise by a couple percent each year. I then collected data trying to figure out if it was central banks or private individuals that were demanding too much gold, and found that central bank demand was the big problem (except during brief bouts of private gold hoarding). Then I considered whether the extra central bank demand reflected extra demand for currency (which had to be backed with gold), or central banks choosing to hold more gold for each unit of currency. I found that both factors played a big role in the 1929-33 deflation. Eventually, my accounting data allowed me to isolate the role of individual countries such as the US and France–which helped me to evaluate the dispute between McCloskey/Zecher and Friedman/Schwartz.
There’s much more in my recent book on the role of gold in the Depression, but the basic ideas came to me when I realized that I needed to go back to first principles, even if the initial model was “too simple”. Gold was the global medium of account, so we need a global supply and demand for gold model of the world price level. Simple models help you get to the essence of things. (Paul Krugman’s very good at this sort of thing.)
My Great Depression research also involved a heavy use of rational expectations and efficient markets. I read almost all the New York Times from 1928-38 and looked at how various asset prices reacted to various types of policy shocks that would directly or indirectly impact gold demand. Doing so vastly increased my respect for the efficiency of asset markets, as I saw numerous examples of where market participants correctly saw things that even the great Friedman and Schwartz had missed.
By the time the Great Recession rolled around, I was already primed to look at asset market prices as an indicator of policy shocks, and when I saw TIPS spreads plunging along with all sorts of other asset prices, I immediately knew that money was too tight.
4. A few years later, I became interested in some papers that looked at episodes of rapid Colonial American currency issuance, which led to comparatively little price inflation. Several authors argued that this provided evidence for a “backing” theory of money and the price level, and against the traditional quantity of money approach. I argued (in a 1993 paper) that backing wasn’t really the issue, rather that the Colonial currency issuance was not inflationary because it was seen as being temporary. This work also made me skeptical of “fiscal theories of the price level”, which are not well supported by the data.
In 1998, Krugman argued that Japanese currency expansion was not inflationary because it was expected to be temporary, which is a very useful way of thinking about liquidity traps. His 1998 paper provides a good way of understanding what’s gone wrong over the past decade, and especially why monetary policy doesn’t seem to have its expected impact.
5. In the late 1990s, near-zero interest rates led to a revival of interest in liquidity traps. I did a paper arguing that the case for monetary stimulus is actually stronger at the zero bound, as you can print more money to achieve any given nominal target. Since printing money is profitable, governments should be thrilled to find themselves at the zero bound, as I explained in this recent MoneyIllusion paper.
This liquidity trap research made me very hostile to the broader profession in 2009, when pessimism about the effectiveness of monetary policy became widespread. In addition, my research on the Great Depression primed me to expect people to wrongly view a depression as a failure of capitalism, not excessively tight money, because that’s exactly how they initially misdiagnosed things in the 1930s. And yup, they made the exact same mistake in 2009.
My career path was very “eccentric”, and a failure by traditional career metrics. But it did give me a useful vantage point as things were falling apart in 2008.