Since I am teaching in the second-year macroeconomic field sequence this year, I have been thinking about the objectives for my teaching. I see three goals for a Ph.D. course:

1. to teach some of the skills directly necessary to fill out the body of an economics paper, including the computations from data and from simulations (to be laid out in tables or figures), and how to write down the details of proofs.
2. to give enough of a picture of how the world works to make it possible to begin to judge how important a potential research result might be: for one’s career, for the discipline of economics, and ultimately, in the potential contribution to overall social welfare. (On how the world works, see the recurring refrain in one of my most popular posts ever: “Dr. Smith and the Asset Bubble.”)
3. to teach analytical tools that–with a few hours or a few days effort–can help one to predict the likely distribution of results one might get from a potential research project that might take months or even years.

a. For straight theory, the development of mathematical intuition is the key for predicting what a project might lead to.

b. For empirical work, key skills for predicting what a project might lead to are

• understanding identification,
• understanding the sources and characteristics of measurement errors, 
• understanding at least rudimentary power analysis in the sense of knowing something about what goes into the standard errors one is likely to get, and
• understanding that the data are endogenous in two very different senses: (i) data from naturally occurring situations come from a complex web of causal relationships and forces and (ii) economists can cause data to come into existence through surveys, field experiments and lab experiments to help fulfill their research objectives.

c. For computational work, such as a project using a Dynamic Stochastic General Equilibrium model, or a project simulating life-cycle consumption, labor supply and portfolio behavior, some key skills for predicting the likely behavior of a model are

• understanding general comparative statics and comparative dynamics results;
• understanding general principles about how models behave, such as key neutrality results that cut across large classes of models and often require intentional modeling devices in order to break (monetary neutrality, Ricardian neutrality, Modigliani-Miller, Wallace neutrality, etc.)
• knowing how to design a set of graphs to get to the heart of what is going on in a model: graphs that serve the purpose for that advanced model that supply and demand serve for Economics 101 (see for example the graphs in my paper “Q-Theory and Real Business Cycle Analytics”); and
• knowing how to compute quantitative results for a few simple models by hand in order to get a sense of the likely size of various effects. (You can see an example of what I mean in some of the chapters of my draft textbook “Business Cycle Analytics.”) 

Of course, in all of these areas, research experience and seeing what other people have done–both in published articles and in work presented in seminars–will also help one predict what a project will lead to. Unfortunately, seeing what other people have done is most helpful in understanding paths that are already well-trodden. But sound criticism of what other people have done is immensely helpful in teaching what to avoid. (Helpful hint: when reading papers, be very suspicious of what is claimed in abstracts. At least half the time, abstracts misrepresent what a paper has really accomplished.) Whether one’s own research experience ultimately leads to unique insight into the likely outcomes of various potential projects depends on the directions one strikes out in during the early days of one’s research career.