SimpleSimon

This borrows heavily from Simon - Scientist as Problem Solver, Langley - Heuristics for Scientific Discovery, and Valdes-Perez - Personal Recollections from 15 years of Monthly Meetings.

What to work on (Tension between 2nd and third points)

  • Start with questions/problems (not topics) and concentrate on the surprises
    • As you work on problems (as you develop expertise?), you’ll find new questions.
      • Confirming or rejecting a hypothesis is good, but the things that really push the boundaries of your knowledge are the things you didn’t foresee. Surprises can guide you to new directions in your research.
      • Surprises make for good questions.
    • What would an answer to the question look like? How would you begin work on the problem? (Valdes-Perez)
      • "When you are famous it is hard to work on small problems. This is what did Shannon in. After information theory, what do you do for an encore? The great scientists often make this error. They fail to continue to plant the little acorns from which the mighty oak trees grow. They try to get the big thing right off. And that isn't the way things go." Richard Hamming - You and Your Research
  • Be audacious Sometimes things may be “hard”, but you have a perspective or tools (secret weapon) that makes it doable. Don’t be afraid to take on hard problems, perhaps you can contribute.
  • Is it feasible, given the current state of the art? You don’t want to work on something that you’ll invest a lot of time into without any returns. Some problems you just don’t have much hope of making real progress on given current state of the art.
    • Perhaps knowledge from other fields or a secret weapon will make it possible. This might be where audaciousness comes in.
  • Will at least two people ask for a reprint? Solve problems people care about This is a heuristic. It may be that the problem you are working is important, but no one cares about it now. While that could be the case, you may not have the ability to pick those problems early in your career.
  • Multiple problems/tasks at once to avoid ruts Multitasking is usually bad, but that isn’t really what this means. It is more along the lines of Richard Feynman’s approach to looking like a genius (also recommended by Richard Hamming in You and Your Research), "Richard Feynman was fond of giving the following advice on how to be a genius. You have to keep a dozen of your favorite problems constantly present in your mind, although by and large they will lay in a dormant state. Every time you hear or read a new trick or a new result, test it against each of your twelve problems to see whether it helps. Every once in awhile there will be a hit, and people will say: 'How did he do it? He must be a genius!'" Note that some problems will probably be in a dormant state. I suppose this is slightly different advice, in that Feynman recommends this as a way of trying new techniques (secret weapons) on problems, and Simon advocates multiple problems as a way to increase your utilization. Sometimes you just get stuck on a problem. Rather than beating your head against a wall, try something else for a while. Other times, you start to get bored with the work, or stuck in a line of thinking. Multiple problems keep you fresh and enable some cross-fertilization. Sometimes just stepping away from a problem and getting rest is good too...

How to work on it (tension between first and last points)

  • Persevere: Outstanding discoveries happen by luck, but only to prepared minds and with sufficient effort
    • This is another point where the advice for starting with questions/problems comes into play. Before you find interesting questions, you’ll probably have to spend some time on uninteresting ones.
    • Have to have expectations for something unexpected to happen
    • Deliberate practice
  • Use knowledge from other fields Simon discusses problem isomorphs in his work, problems that look different on the surface, but are equivalent given the right mapping. Perhaps knowledge from other fields can act as an isomorph, or provide metaphors and analogies that will improve understanding.
  • Cultivate productive working relationships In some ways this is like knowledge from other fields and perseverance combined. One person can only master so much, other people are likely to have different experience than you or have knowledge from other fields. If your friends work to acquire expertise, they’ll probably be able to fill in gaps in your knowledge and abilities. You can do the same.
    • "Acquire as many good friends as possible, who are energetic, intelligent, and knowledgeable as they can be. " Simon - The Scientist as Problem Solver
    • Form partnerships whenever you can
  • Use a secret weapon Again, deliberate practice can come into play here. A secret weapon may simply be some expertise or mastery of some technique that others haven’t cultivated. It could also be equipment, your friends, a metaphor, etc.
  • Balance theory and data There is an important interplay between hypotheses and tests. Form theory in response to data, design experiment to test theory, surprise from experiment, refine model, ….
    • Model or formulate your data/observations
    • Experiment: Design experiments to test your model
    • Look for surprises (Where does the model fail)
      • "In that brief interval between surprise and successful normalizing lies one of your few opportunities to discover what you don’t know. This is one of those rare moments when you can significantly improve your understanding. If you wait too long, normalizing will take over, and you’ll be convinced that there is nothing to learn. Most opportunities for learning come in the form of brief moments. And one of the best moments for learning, a moment of the unexpected, is also one of the shortest-lived moments." Karl Weick - Managing the Unexpected: Resilient Performance in an Age of Uncertainty
  • Satisfice Pareto principle. You’ll always have something left undone, you’ll have to determine when to move on. At some level, you’ll get diminishing returns.