The manuscripts of Edsger W. Dijkstra [Link] contain his ten pieces of advice for doing academic research:
- Raise your standards as high as you can live with, avoid wasting your time on routine problems, and always try to work as closely as possible at the boundary of your abilities. Do this because it is the only way of discovering how that boundary should be moved forward
- We all like our work to be socially relevant and scientifically sound. If we can find a topic satisfying both desires, we are lucky; if the two targets are in conflict with each other, let the requirement of scientific soundness prevail.
- Never tackle a problem of which you can be pretty sure that (now or in the near future) it will be tackled by others who are, in relation to that problem, at least as competent and well-equipped as you are.
- Write as if your work is going to be studied by a thousand people.
- Don’t get enamored with the complexities you have learned to live with (be they of your own making or imported). The lurking suspicion that something could be simplified is the world’s richest source of rewarding challenges.
- Before embarking on an ambitious project, try to kill it.
- Remember that research with a big R is rarely mission-oriented and plan in terms of decades, not years. Resist all pressure —be it financial or cultural— to do work that is of ephemeral significance at best.
- Don’t strive for recognition (in whatever form): recognition should not be your goal, but a symptom that your work has been worthwhile.
- Avoid involvement in projects so vague that their failure could remain invisible: such involvement tends to corrupt one’s scientific integrity.
- Striving for perfection is ultimately the only justification for the academic enterprise; if you don’t feel comfortable with this goal —e.g. because you think it too presumptuous—stay out!
I like some of these more than others: #1 and #6 are great, but I’m not so crazy about perfectionism #10 (“Done is better than perfect“). I wish this list of commandments was more actionable, but I won’t criticize because his other manuscripts may contain other advice. Please leave your thoughts in the comments (or better yet – links to other Dijkstra manuscripts!)
HT: @ncgds
Punk Rock Operations Research 
January 1st, 2014 at 2:08 pm
Alright I tweeted before actually finishing the whole thing. I agree with what you said about #10, but also I can’t get #3 to sink in. Why should I avoid working on something if I know that someone else might work on it?
January 1st, 2014 at 3:17 pm
I like the commandments more in retirement than I would have as an assistant professor. Sadly, #1, #7 and possibly #10 run contrary to the path to tenure at many (most?) universities. I tend to think that #2 might prove counterproductive at many (most?) business schools. I don’t question their correctness, just their practicality.
January 2nd, 2014 at 1:06 pm
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January 7th, 2014 at 4:55 pm
Really like most of these, but especially like #4 and #9. And of course, #1. Not so sure of #3 though; I think there will always be someone as capable as me for every problem out there.
January 8th, 2014 at 4:19 pm
I agree that #3 seems a little strange. It suggests that there can only be one way forward in a problem area. In many areas, progress is made incrementally, so if I progress the subject a little, it will help another (more competent?) person later who can use my results. Newton’s comment about standing on the shoulders of giants seems relevant. And Dijkstra is known for his shortest path algorithm, and since his groundwork on that, other people have developed incremental improvements on it.
#4 is interesting. How many academic articles are read by 1000 people? But if research was written so that it could be _understood_ by 1000 people outside the narrow discipline, without being trivial, then it would be very good for the clarity of academic journals!
As Paul says, #7 (sadly) goes against the norms of the academic ratrace. The pressure to publish and apply for the next grant means that one can easily work at problems which give quick results. However, practical O.R. often wants quick results, even if those results are not so rigorously established as an academic might like. So, although some research work may take decades to complete, (the experiment at http://en.wikipedia.org/wiki/Pitch_drop_experiment is an extreme case) most of us will spend most of our time on matters which have time horizons of months. At least we have the luxury of horizons of months, while those in industry may have horizons of days or hours.
January 9th, 2014 at 9:29 am
Had I adhered to #3, my tenure decision would have been much simpler (as the result of zero papers submitted, let alone published). I wonder if Dijkstra was implicitly assuming the recipient of the advice would be sufficiently gifted that s/he could always move on to a more important or more challenging problem (and would always be able to identify such a problem — not entirely trivial if we set aside P=NP and other tilts against windmills)?
I’m not sure if #4 was intended to mean “write clearly enough that a 1,000 disparate scholars can read it” (David’s point on clarity) or “write carefully enough that 1,000 informed and persnickety readers will find no cause for complaint”. I think both are worthy goals.
January 13th, 2014 at 1:43 pm
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