mediocrity. It gives the illusion that research is about making small increments to someone else’s work. But worse, it almost guarantees that after a while, the work is driven by what can be solved, rather than what needs to be solved. People write papers, and the papers get accepted because they are reviewed by the people who wrote the papers being improved incrementally, but the influence beyond the world of paper-writing is minimal.
In the first years of computer science as an academic discipline, many theses were “theoretical,” in the sense that the contribution was mostly pencil-and-paper: theorems, algorithms and the like, rather than software. While much of this work was vulnerable to the problem just described—paper building on paper—it is quite possible for a theoretical thesis to offer a real contribution. For example, even before I joined the Princeton faculty, I had a summer intern at Bell Labs, Ravi Sethi. At that time Ken Thompson and Dennis Ritchie were involved in the Mul-tics project, an operating system for the GE635 computer. This beast was the first to have more than one register in which arithmetic could be done, and the word passed to Ravi and me that they needed techniques to compile code in a way that made best use of several registers. Ravi’s thesis was an algorithm for compiling arithmetic expressions using any given number of registers, in the fewest possible steps. This algorithm actually was put into the C compiler for the PDP- 11, a few years later.
While Ravi’s thesis was “ theoretical”—neither of us wrote any code— the work illustrates how I believe any thesis should develop. The work was not based on what some paper left open, but rather on an expressed need: a way to compile expressions using several registers. The big advantage we had was that we were part of an environment that was pushing the frontiers. Had we not been at Bell Labs, it is doubtful we would have realized the problem was worth addressing. We surely could not have read about it in a paper. Even Andrei Ershov, who had previously published the node-num-
bering scheme we used, only saw it as a way to compile for a one-register machine, and did not suggest in his paper that someone else should look at machines with multiple registers.
The best scenario is that the student tells me what their thesis should be, and carries it out independently. Moreover, their thesis topic is selected because they perceive a need on the part of some “customer.” Sergey Brin came closest to this ideal, since he and Larry Page, with no help from me, saw both the need for a better search engine and the key ways that goal could be reached, while students at Stanford. The one missing element: neither of them got their degree; but more about that later.
A close approximation was George Lueker, who came to visit me one day to ask if I had any ideas for a thesis topic. George was not then my student, being enrolled in the Applied Math Program at Princeton. I happened to be reading about chordal graphs that morning, and suggested an algorithm to detect chordality. A year later, he came back and showed me a thesis he had written on pq-trees, a data structure that even today has several important applications beyond chordality testing. Several other students have dragged me kicking and screaming to learn a new area, even if I then got involved in selection of their thesis topic. Matt Hecht had me learn about data-flow analysis; Allen Van Gelder did the same with logic programming.
Why does it matter who suggests the thesis topic? We’re trying to get young scientists to the point where they can make independent judgments about what is worth working on. There are several decisions to be made: what is worth doing, what is feasible to do, and how do you do it? While an advisor can help with all these things, it is wonderful to meet a student to whom this comes naturally. Another point that I tried not to forget as I grew older was that young people can often see things that those of us who have become set in our ways cannot. Trusting the technical judgment of the young is not a bad strategy.
To make students successful, we need to be ready to provide many services.
Finding customers. As mentioned at the beginning of this Viewpoint, there needs to be an exposure to problems that are at the frontier, and that are needed by a “customer.” Sometimes, they can find a customer in industry, as Ravi Sethi did at Bell Labs. Summer internships can be a great opportunity. However, advisors should encourage students to intern at a strong industrial research group, one where the goals are more than minor tweaks to what exists.
Whether the thesis is theoretical or an implemented solution, students need to be guided to understand who will consume their contribution if they are successful. And the answer cannot be “people will read the paper I will write, and they will use the open problems in it to help form their own theses.” Especially when dealing with theoretical theses, the chain of consumption may be long, with idea feeding idea, until the payload is delivered. Yet if we let students ignore the question of whether such a chain and payload plausibly exist, we are doing them a disservice.
Walking before you run. Exposure to problems is not enough. Some, although surely not all, Ph.D. students need to convince themselves that they can do something original. Here are a few ideas that have worked:
˲ One way to give a beginning student practice with the mechanics of research is to think through a small problem yourself, and then propose
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