*University of Colorado.  This paper is based on a combination of my thoughts over the years, but also on an excellent paper, "An Experimental Graduate Course in Economic Research," by Thomas Mayer, University of California, Davis.
 
 

The motivation in writing this paper is to help University of Colorado graduate students in what is always a very competitive job market.  The number of new Ph.D.'s each year fell from roughly 900 peak in 1973 to about 800 per year, but has been again rising being currently a bit over 1,000 per year.  However, many of these go to foreign countries, so the effective number of students on the market seeking academic jobs hasn't changed very much over the years.  Currently, less than 60% of economics Ph.D.'s get academic jobs. This latter figure is down from two-thirds, and those jobs taken in academia are often  less prestigious and harder to retain.  I have observed two facts relevant in the present context:

1. Even good students have problems developing and completing a doctoral dissertation, and

2. Research productivity is quite low for most academic economists.

Why is this?  First, let us discuss reasons sometimes advanced for failing to publish--reasons which are bogus in my opinion. It is not lack of technical ability (e.g., econometrics, math econ., etc.) which prevents people from publishing.  Virtually anyone with even minimal training in economics is prepared to publish (not necessarily in JET or Econometrica but a good idea is always publishable in a good place).  Nor is it the status of the profession as a collection of exhaustive, non-refutable truths; there are very good incremental (and even completely novel) contributions to be made.

Indeed, the profession is rapidly expanding its bounds into areas traditionally regarded as non-economic with many errors of omission or commission and even the traditional areas are far from settled.  It is not that most students are dumb.  Students are better every year in training and ability.  It is not even that economics is an "Art" which can't be taught (After all, there exist art schools for the very purpose of teaching things which are "unteachable").  It is not lack of time, either...

What is it then which prevents most people from diving into a successful dissertation and, later, into diverse research efforts?  I very strongly believe the reason is that the educational system, right up to the time of writing a dissertation, discourages independent thinking.  Independent ideas are not encouraged nor is the critical mindset necessary to generate ideas.  These thoughts first became evident to me on a post-doc at the University of Chicago where, from the moment of matriculation, students are trained to be critical of what they read--indeed, the most successful of those students have the attitude that, whatever it is that they are reading, it is probably wrong or, at the very least, could be greatly improved.⁽¹⁾

The preceding has, at least in bits and pieces, probably occurred to most students. The question becomes "What can be done to change this state of affairs?" Rather than engage in a host of empty platitudes, I will suggest two general things which can be done and will then go on to list a number of "work habit changes" which should, if pursued, greatly increase student productivity.

The first general point: collaborate with an experienced researcher!  There are those among you who will argue that this is exploitation--that you will not be paid your marginal product. There are two arguments to the contrary.  First, in every occupation, "apprentices" get paid less than their more experienced counterparts--this does not represent low payment, but rather represents a joint package of higher payment combined with the return purchase of education! That is, you are investing in research ability. The second argument involves loss of productivity for the senior researcher--it turns out that employing RAs may have costs greater than benefits (in terms of pages per faculty member in the top 24 journals over the 1974-78 period, a dummy variable for "presence of research assistance" had a negative coefficient indicating less publications for those having such "help"⁽²⁾).

The second general point: begin generating ideas by reading things critically.⁽³⁾ Since grade school we have been trained to merely regurgitate that which is taught us.  This is fine for ideas that have been tested so many times successfully that there is considerable confidence that they are right.  But, one never "proves something is right;" rather one tentatively accepts hypotheses until they are proven wrong.  Science advances by finding flaws in the orthodox views.

Changes in work habits. The following suggestions have worked for me, but you will no doubt arrive at a related set of hints that work for you:

1. Read critically--assume the author is wrong.

2. Don't be too narrowly "economic" when originally formulating ideas (that detracts from your innovativeness--it is not so much whether you are right or wrong but whether you are interesting in your thought process that matters).

3. Establish an "idea file." (I used to have a folder at home and one at the office (now I use computer files) to put rough ideas in--just jot down enough, a couple of sentences, to be able to recall the idea; don't think about it too much at first; if it's good, it will keep re-emerging). It is surprising how seldom you will actually go to the idea file to hunt for something to write about--its value lies in its existence not in the frequency in which you use it.

4. Scribble (even in "tried-and-true" textbooks) as you read them what you think to be wrong or unexplored or untested in the front flaps, perhaps with page references--add them to the idea file after you are done with the book (put page references in the file if that enables you to briefly get the idea down).

5. If a published empirical article has a result which appears to be implausible to you, rerun the original study. You will be amazed at how often a study using econometric methods cannot be duplicated!⁽⁴⁾

6. Write a comment if an error is found--it will give you professional confidence that you can do good work (besides when you write the idea or correction down it looks better, when it is typed it looks better still, when it is published it looks amazingly scholarly!).

7. Seek out co-authors (the law of comparative advantage in action) but not at the expense of establishing that you can conduct independent work.

8. Assume that what you are doing is different until proven otherwise! (This is, in my opinion, very important--many people look through the JEL or JSTOR and, from titles and abstracts, assume that their idea has been done before. It probably hasn't and if it has you are probably bringing some new theoretical or empirical wrinkle to the subject). Along the same lines, while a literature review is very nice, it can inhibit your range of thinking--you should at least have a very good idea of exactly what you want to do before examining what others have done in detail. The review of literature is to tell others how what you have done is an improvement--if you let yourself be intimidated by prior efforts a promising line of work may be dropped.  [Anecdote: while I don't recommend this as a general rule, I have never published a paper (with perhaps minor exceptions) on a topic that I had any formal training on!  That is, I have never had a course, at any level, in urban/regional or environmental economics, and the monetary ideas of my dissertation were largely unrelated to coursework at Northwestern.].

9. Get a location (library, home office, etc) where you can work and associate with work--if you feel like goofing off, leave the
"sacred spot".

10. Usually "look" at your data a bit (not just means, sds, etc., but matching observations with reality--sometimes you can get an interesting idea from a personal examination of the data).  Hardly any worthwhile scientific advance was actually accomplished by the "scientific method!"  (Scientific Method: reflecting analytically on a subject at a purely theoretical level, then turning to the data to conduct tests of the model).  There is, in fact, a constant interplay between the broadly-defined data (i.e. the sense of the way the world works) and the model building; constructing a new model is much more like writing a convincing novel than anything that might be called the scientific method.

11. Write clearly (use fewer commas than you'd ordinarily use and make sentences shorter) but don't get paranoid about matters of style to the extent that you get "writer's constipation" (a common post-Ph.D. phenomenon when the main readers have altered your sentences mercilessly).

12. Interpret reviewers' and editors' comments optimistically--show your "rejections" to a more experienced colleague.⁽⁵⁾ Also don't worry too much about rejections. To a certain extent it's a random draw and if you never get rejected you are shooting too low in your journal selection (there is an "optimal" rejection rate, depending on your life-cycle and the like). Watch out for phrases like "in its present form" since the revised form often need not be too different, usually shorter.

13. Make time for research effort! Surveys show that typical academicians spends less than 25% of their time doing research. It is very easy to let the minutiae of day-to-day trivia come to dominate your life. Never lose sight of how much time you are actually spending on research, as it is extremely easy to let six weeks go by doing nothing in this area on the grounds that you are "too busy!"  You really are not and once you get used to it you will find your self-esteem going way up and, in addition, some of the research is actually fun!

GOOD LUCK

P.S. I would welcome additional hints from students, colleagues, et. al. If this is found to be useful, I will keep updates coming...

Original: January 1991

Minor revisions and web upload: August 2001, September 2002

1. This is a very healthy research attitude, though it can lead to insidious personality changes. (Aside: How much of the difference in performance between men and women is due to the training of the latter to be "nice" and less critical in our society?).

2. See my "Economics Departmental Rankings: Research Incentives, Constraints and Efficiency." American Economic Review, Vol. 72, No. 5 (December 1982), pp. 1131-1141 (with J. Marchand and R. Thompson).  There are some additional competing explanations involving the nature of institutional funding.

3. By way of anecdotal support for this position, I found the Arrow Increasing Relative Risk Aversion Hypothesis to be quite implausible when reading in graduate school. Since Arrow based his hypothesis on Friedman's time series money findings which indicated that money was a superior good, I also felt those findings to be suspect. One's immediate reaction would be to accept the findings of two Nobel Laureates without question--never do this! Check 'em out.  I may not be correct in my assertions that both are wrong in this matter, but I have managed to convince enough people to publish five articles on the subject.  In fact, I have a very recent paper that suggests that they might be right!  I still believe that I'm right but there is a payoff to the publications in any event--right or wrong, it is always good to question....

4. Anecdote: I found implausible a result in the Journal of Regional Science that indicated that migrants responded to expected future growth in per capita income but not current income differentials (moreover the former variable appeared to explain 44 percent of migration)! This seemed so counterintuitive to me that I re-ran the regressions and found that the result stemmed from having copied the wrong column of numbers (growth of personal income, not personal per capita income, hence migration was essentially regressed on future migration!). This led to a published comment longer than the original article (some other results changed) and ultimately to a host of related works since then.

5. Anecdote: I showed one of my early rejection letters a colleague and he responded "Congratulations! They want a revision."