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.
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