Principles of professional advancement.

Alchian, Armen A.

You've finished your Ph.D. ordeal, and luckily you're now in your first year as a real member of the faculty. The expected relief from the burden of completing the dissertation is quickly replaced by the burden of publishing. But then you realize it's the same pressure again. You've already extracted what little there might have been in the dissertation. What can you do next, something really on your own?

You may not know now, but in a few decades, predictably, you'll have more than you can complete. Unfortunately, by then you'll have less desire to publish. The capital value of another publication will have become pretty small. So you'll find yourself passing ideas to, and encouraging, the younger members of the department, wondering if they'll be so fortunate as you were in early publishing a article that really helped your career.

These reflections by an older, retired, out-of-date person - one who has succeeded far above the "expected value" of entrants to the profession - are a sort of confession of "How I did it." Or more honestly, maybe, "How it was done to me!" Perhaps it will inspire hope in new entrants, particularly with respect to publications.

I emphasize that the opening part of this essay is not entirely a conjectural story. It's mine, with a couple of minor exceptions. I'll confine my major comments to three papers I wrote some time ago, and with which I remain pleased today (for reasons I'll explain). I hope the comments will be of some interest to economists, especially in those moments when everything seems a bit confused, though not hopeless. I won't resist the temptation to reminisce and pontificate, the privilege of the emeriti.

BACKGROUND

Although I was officially awarded the Ph.D. in 1944, while in the United States Air Force, I actually had finished my doctoral work by 1942, just before entry into the military. My dissertation was on the presumed effects of a general cut in wage rates across the economy. Like most dissertations, it should have been addressed to my supervisors with the label, "For Your Eyes Only," and then forgotten - as mine properly has been. It had nothing to do with my subsequent work, happily. But the USAF engagement meant that between the dissertation and the first academic job there were several years in the military, with time to wonder what the point was in being what is called an "economist."

Fortunately, I had a major sub-discipline as required in the 1930s: statistics. I had learned a few things about inference, probability, random walks, and stochastic, evolutionary processes. I learned them from a few extraordinary teachers, among them Allen Wallis, Edward Shaw and Holbrook Working. And during military service I got to use what I had learned. At the USAF Training Command from 1942 to 1945, I did statistical evaluation of the validity of entry-level test scores of Air Force cadets, for their training as pilots, navigators or bombardiers.

Principle of Professional Advancement No. 1

Upon return to civilian life in 1946 in my new teaching job at UCLA, I again started to read the journals in economics with my superb graduate students (the majority of them relatively mature ex-military men in their mid-twenties). In that way I began to relearn economics. For economists, Principle of Professional Advancement No. 1 is, "Have super students!" The value of good students is evidenced by publications. All three of the articles I will discuss below were developed during classroom exposition and discussion with my students.

"Uncertainty, Evolution and Economic Theory" [1950]. In my early years of teaching, a pair of confrontational articles by a Professor Richard Lester and a Professor Fritz Machlup, published in the leading journal, the American Economic Review, were dutifully studied with disappointment and distress. Current readers will be astonished to know that the debate was about whether business people "really" used marginal productivity and profit-maximization analysis in making decisions! Lester said "no;" Machlup said "yes." Of course, both were right and both were wrong, but their reasoning and defenses were easily demolished by each other.

If that was the quality of analysis passing for economics, I should have stayed in the military I thought. So, one day in class I explained what I had read. Then a bit testily, I complained about the quality of the articles, all in the privacy of the classroom. I then explained what I thought the two economists should have said. They should have said, "Read Darwin! It's not what you think you are doing or how you rationalize your choice of that action. It's whether the action has survival value. And if outside analysts can identify the reasons the chosen action had survival value, and in what direction changes in the environment (constraints) affect survival conditions, economists don't have to worry about how people discover by thought or luck what are the new best conditions. Competitive trial and error will evolve toward the fittest - whom economists characterize as profit maximizers."

Word of my comments passed to my colleague, Professor Stephen Enke, as sensible and practical an economist as you would ever want to know. He remarked that the comments would make a publishable article. I scoffed that it was all too obvious and trivial, and appropriate only for a class lecture, not as a publishable article. He nevertheless urged me to write it at least for future classroom handouts.

I did. He read it, and liked it enough to demand that I send it to a journal. I didn't know of one minor enough to warrant a chance for publication. He persevered, saying I should not send it to the AER, where the original two had been published. Instead, he brazenly suggested and insisted that I send it to the Journal of Political Economy.

To my genuine surprise, a very encouraging letter was quickly (by current standards) received from a Professor Milton Friedman, of whom I had heard. The paper would be published if a few suggested extrapolations and minor modifications were made. The article quickly appeared. It was my first article.(1) I proudly fondled the issue and sent reprints to close friends, expecting they might respond by saying "Thanks, I'll read it sometime soon." I could not at that time believe that evolutionary competitive principles were so forgotten or ignored.

Principle of Professional Advancement No. 2

I have since begun to realize that I was exceptionally fortunate to have had a father who thrust my nose into Darwin's Origins when I was in high school. Then, in college, I had a course in biology which was all Darwin and evolution. Finally, at the graduate level, I was fortunate to have worked with Professor Wallis, who introduced me to R. A. Fisher's Statistical Methods for Biological Research, and to have studied with Professor Working, whose chief interest was random walks in wheat futures prices. With that training, evolutionary interpretations were virtually genetic. So Principle No. 2 is: "To advance your career, you have to be smart enough to have had the right teachers."

Principle of Professional Advancement No. 3

That's also how, by great foresight and research, you can be at the right place at the right time. The article on evolution and economics happened to appear at a time of reviving interest in and a more rigorous formulation of the evolutionary processes. That the approach helps relieve economists from squirming and hedging in futile attempts to assess what business people were "really doing" was probably a reason why the article was so well received and why it has remained a relatively well-cited paper. Principle of Professional Advancement No. 3 is "Plan to be at the place where your training happens to be useful - at the right time.

I'm still astonished at the success of the article on evolution and economics. As I look back - the privilege granted to those who survive for a long time - I see that the idea had an enormous effect. But not because of the article I wrote. It was because of the idea itself, taken from Darwin. I just happened to be the person who brought the news to economics, as a middleman brings goods from manufacturers to consumers. If I hadn't done it, many others would have.

I would regard the article as having contributed to a major revision in the science if there had followed a strong interest and research in the genetics of economic behavior. For example, whileeconomists treat the "individual" as the unit of analysis, a more general and (I conjecture) more powerful analysis of economic behavior can be founded on "genes" as the unit of analysis or, more exactly, as the competing units. Certainly the convex preference map is a convex survival map, mapping points of equal survival probability. Is it not true that all forms of life have indifference survival curves that are convex, etc.? Using a biological approach - economics is a life science! - economists would look at competition beyond the benevolent type.

Jack Hirshleifer's recent work is an example of this thrust into ignored economic behavior. Someplace in my 1950 article on evolution (or perhaps elsewhere), I argued that biology and economics ultimately would merge. My colleague Professor Hirshleifer now appears to be manipulating a takeover of the one by the other.

"Costs and Outputs" [1959]. My ability to apply Principle of Professional Advancement No. 3 - being at the right place at the right time - was illustrated by my decision to join UCLA, close to where the AND Corporation would later be created. RAND would (at the instigation of Allen Wallis) invite me to be their first resident consulting economist. I happened to join the UCLA faculty in 1946; it happened that RAND was set up in Santa Monica in 1945. Allen happened to know General "Hap" Arnold well. So it was all happenstance - like the birdies I make in golf.

RAND was not sure what an economist would do. I certainly didn't know either. But I learned a lot about "big real world problems' - too big to comprehend, usually. Since it wasn't clear at first what an economist could do that was pertinent, the task was to snoop around, look at the problems being analyzed (defense problems, usually) and try to see how economics could help.

What we economists did first was detect how economics was being ignored, in particular how costs and interest rates were ignored in making military-strategy decisions. Another "complicated, surprising" proposition was that for assigning nuclear material to the Air Force versus the Navy, it was not deemed necessary to know whether it was more important for the Navy or the Air Force to have more fissile material. But of course, that would be very desirable to know. With the idea of indifference curves between nuclear material and labor (as inputs), marginal rates of substitution between the two in the Navy and also in the Air Force would indicate directions in which to revise the allocations. That "revelation" gave the economics group some extra clout.

I cite these as two examples of how the simplest concepts and propositions in economics have mega-ton power. In that vein, I like to brag that I did the first "event study" in corporate finance, back in the 1950s and 1960s. The year before the H-bomb was successfully created, we in the economics division at RAND were curious as to what the essential metal was - lithium, beryllium, thorium, or some other. The engineers and physicists wouldn't tell us economists, quite properly, given the security restrictions. So I told them I would find out. I read the U.S. Department of Commerce Year Book to see which firms made which of the possible ingredients. For the last six months of the year prior to the successful test of the bomb, I traced the stock prices of those firms. I used no inside information. Lo and behold! One firm's stock prices rose, as best I can recall, from about $2 or $3 per share in August to about $13 per share in December. It was the Lithium Corp. of America. In January, I wrote and circulated within RAND a memorandum titled "The Stock Market Speaks." Two days later I was told to withdraw it. The bomb was tested successfully in February, and thereafter the stock price stabilized.

In the economics division I was working with Stephen Enke, under the strong support and leadership of Charles Hitch.(2) One thing we discovered was that engineers didn't quite understand why "cost" had something to do with a choice of armaments. To help them learn how and why costs and things like interest rates weren't just financial shenanigans, we collected cost data on production and operations of airplanes. I quickly noticed that the production engineers kept saying marginal costs decreased and continued to decease, lower and lower. To the contrary, as every economist knew, marginal costs begin to rise at some stage. And our textbook diagrams and cost theory proved it.

So what mistake were the engineers making? After too long a time, with embarrassment, I discovered that "output" meant something entirely different to production engineers than it appeared to mean to economists. Output to engineers was measured in units of accumulated total output, not in rate of output. Simple, but spectacularly different. Yet, not a single economics textbook, advanced or elementary, mentioned that. In fact most of the time the texts left unclear what was meant by "amount of output." The engineers were explicitly clear - it was the accumulated number of units produced, with nothing whatever about the rate of production of that aggregated volume of output. Economists, judging by the relations posited to exist with "output," had if anything the "rate of output" in mind, unconscious of the importance of the difference between rate and volume of produced output.

Which group was correct? It was a draw. The engineers were right in that marginal costs of volume decreased with volume; economists still could be allowed to presume marginal costs of increased speed of output were rising. But the economists were obviously right more generally in emphasizing costs in the choice of alternative weaponry. And in measuring cost it was capital value, the present value of a stream of future activities, that was pertinent, not just the initial year's flow of "cost."

The important points were, first, that investment decisions for output involved contemplated total amount, or volume, as well as the rate. Second, the cost had to be in terms of capital values - the present value of the contemplated outlay in the future. By confining one's thoughts to rates of output the capital value measure was hidden, resulting in overly narrow attention on variable, fixed and marginal costs of changes in the rate of output. I thought that was important. At least it matched the procedure being initiated in the Kennedy administration's five-year military costing conception.

I was allowed to summarize the situation in some memoranda on learning and "progress curves," as the engineers dubbed the cost-output relations.(3) A summary of implications was written, called "Costs and Outputs," which was accepted for publication in the American Economic Review. But then I was asked instead to include it in a collection of papers being prepared by Moses Abramovitz and others in honor of their Stanford colleague - and my old teacher - Professor Bernard Haley. I declined the invitation to publish "Costs and Outputs" in the AER in favor of the Haley festschrift. I regret that it did not get into the AER where more people would have seen it. But I don't regret having had that opportunity to express appreciation for the help Professor Haley gave me while I was a student at Stanford.

The paper - henceforth a festschrift book chapter - has been reprinted several times (e.g., Breit and Hochman [1971]). Still, the paper seems to have had no effect on anything. After all, who bothers to read festschrifts? No texts, so far as I could discover, were changed in any way to avoid the confusions in the meanings and measures of output and of the pertinent measure of cost. I was disappointed. Why were the implications ignored?

A possible answer soon dawned. If capital value concepts of cost and aggregate output were on the supply side, should something not appear on the demand side to make the analysis compatible? Demand was conventionally viewed as a rate of demand, not as an aggregated total volume. Until modified, the demand and supply analysis would continue to limp along on one foot.

But an article appearing recently in Economic Inquiry asked and answered the question why firms persist in intentional mispricing, that is, in keeping prices too low when demand increases transiently.(4) Why are shortages and rationing deliberately chosen over a more profitable, higher, market-clearing price? And which customers are favored? The basis of the answer, when stripped of all surrounding detail, is, I believe, that demand and price must be viewed not simply one-dimensionally as the current rate, but as the anticipated aggregated volume. More precisely, price is not just the current dollar price for a unit now, but is the anticipated capital value of all future business from the customer. For example, which is a greater demand: (a) a rate of 1000 a day lasting one week, or (b) a rate of 100 a day lasting a year? The rate over time is certainly an important dimension of the demand vector. More attention is paid to that vector of "demand price" than to the current flow price. This is especially important for items like CD disks, computers, computer programs, and drugs where marginal costs of extra units of volume are very small compared to the total cost of development.

If I were a young assistant professor today, there's no doubt as to what puzzles and issues I'd tackle. There is much more work to be done in tying the volume-demand effect to the stochastic nature of demand. Applications of such models to a wide range of pricing problems will be very fruitful, I believe; Art De Vany is doing such work with theatrical exhibitions and pricing. The "zero" marginal cost of extra units of things like software, drugs, and patented ideas likewise poses interesting pricing and contractual problems.(5)

"Information Costs, Pricing and Resource Unemployment" [1969]. Perhaps mistakenly, I like to regard this paper as my best. It posed the simple question, why is there unemployment? In attempting to answer the question, the article owes its genesis to a casual comment by George Stigler one day during a round of golf.(6) That particular day, I inquired of George, "Economists don't have an explanation of unemployment. Why does it occur?" Stigler, a man who could recognize a serious question even when trying to extricate himself from a bunker, responded "Did you ever think of the reasons for, and costs of, search?"

That showed I knew how to apply Principle No. 2: have the right teachers. As with the article on evolution and economics, the paper sparked by George's comment was at first intended as an exposition just for my own information and understanding. It ultimately appeared in Economic Inquiry (then the Western Economic Journal) while Professor Harold Somers was editor.(7)

I stated above that I think this paper my best. It tackles a clearly important problem, one on which I had seen much nonsense - and still do. It was an attempt to put in plain English what economists know about things like search, and to dispose of explanations based on "monopoly," "price rigidities," "unions," and so forth. Because the exposition was simple but the ideas themselves powerful, the paper has had wide readership.

Principles of Professional Advancement Nos. 4 and 5

Two more Principles of Professional Advancement remain. Principle No. 4 is: make frequent use of coauthors. They keep you on the "straight and narrow." If you can survive as friends after a joint paper, you are doubly lucky. It has been a boon to me to have co-authors like Robert Crawford, Harold Demsetz, Reuben Kessel, Benjamin Klein, Roland McKean, William Meckling, and Susan Woodward. (I hope I have not forgotten any.) Oh, I also have a William Allen as co-author of a text book [1972] that was forty years ahead of its time, in which he claims I wrote all the odd words while he wrote the even ones.

I'm not going to comment on how the jointly-authored articles were initiated and co-authored. The co-authors would have to co-author any current recollections. But a common theme has been the structure and role of types of property rights. All the persons mentioned have remained good friends to this day, except that Kessel and McKean, most sadly, died far too early. I want to seize this rare opportunity to pay tribute to Reuben Kessel, whom I met at RAND, and with whom I worked most intensively. He was a natural born economist, and he was "homo economicus." My error rate in economics diminished rapidly after a few years of friendship with him, and my horizon of understandable events widened.

Finally, and in that vein, be sure you have helpful, smart colleagues, ones who are willing to spend hours trying to demolish your argument while trying to help you reach a better understanding, or in suggesting ideas for you. I followed that advice. Not only has fortune favored me with excellent graduate students and co-authors, but also with other colleagues who are superb economists. Of course, although it's not publicized, colleagues who aren't co-authors with you often contribute more to your career than co-authors. Being smart enough to have cooperative colleagues like that is not just luck. I was deeply involved in recruiting for the department. So in closing, I commend Principle No. 5: have superb and cooperative colleagues.

1. I had published a small, minor comment in the Journal of the American Statistics Association on someone else's paper.

2. As a Rhodes scholar, Charles Hitch had been a friend of John Williams, the chief of the division at RAND in which the mathematicians were located, and where I was placed for lack of knowing what an economist could do. Williams invited Hitch to Santa Monica for a month on the beach, which fortunately helped to persuade Hitch to be the head of an economics division. In addition to myself and Hitch, the economics division included my UCLA colleague Roland McKean, who co-authored a book with Hitch [1960] based on some of the work being done at RAND.

3. That work also led to my writing an article on the reliability of progress curves in airframe production [1963].

4. Haddock and McChesney [1994]. In essence, Haddock and McChesney argue that once demand is viewed more broadly, in more dimensions of "size," the implied market-clearing competitive pricing concept in altered. What appears to be irrational, inefficient pricing is seen to be economically efficient.

5. The biological-genetic work mentioned above is also of great interest, although this area is too technical for many people trained as economists.

6. George was an avid golfer. He lived next to Flossmoor Country Club, where I was lucky enough to play with him a couple of times. I also visited George at his summer home on Lake Muskoka in Canada, where we boated across the lake to alternate golf courses. And we played a few holes at Princeton (where I first met George at a conference), with Milton Friedman as our caddy.

It is unclear whether golf and economics are complements or substitutes. Bob Crawford and I used to talk a lot about economics as we were developing our ideas about opportunistic behavior (Klein, Crawford & Alchian [1978]), but bad golf was sometimes the resuit.

7. Somers, retired from the UCLA economics department and my current office-mate, is also the man who brought Ronald Coase from England to Buffalo.

REFERENCES

Alchian, Armen A. "Uncertainty, Evolution and Economic Theory." Journal of Political Economy, June 1950, 211-21.

-----. "Costs and Outputs," in The Allocation of Economic Resources, edited by M. Abramovitz et al. Palo Alto: Stanford University Press, 1959, 23-40.

-----. "The Reliability of Progress Curves in Airframe Production." Econometrica, October 1963, 679-93.

-----. "Information Costs, Pricing and Resource Unemployment. Western Economic Journal, June 1969, 109-28.

Alchian, Armen, and William R. Allen. University Economics: Elements of Inquiry, 3d ed. Belmont, Calif.: Wadsworth Publishing Co., 1972.

Breit, William, and Harold M. Hochman. Readings in Microeconomics, 2nd ed. New York: Holt, Rinehart and Winston, 1971.

Haddock, David D., and Fred S. McChesney. "Why Do Firms Contrive Shortages? The Economics of Intentional Mispricing." Economic Inquiry, October 1994, 562-81.

Hitch, Charles J., and Roland N. McKean. The Economics of Defense in the Nuclear Age. New York: Atheneum, 1960.

Klein, Benjamin, Robert G. Crawford, and Armen A. Alchian. "Vertical Integration, Appropriable Rents, and the Competitive Contracting Process." Journal of Law and Economics, October 1978, 297-326.

ARMEN A. ALCHIAN, Professor Emeritus, Department of Economics, UCLA.