There's a very useful idea for thinking about the history of research and discovery that I call "the velocity of discovery".
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It begins with an analogy - actually, more than an analogy - to the motion of waves (e.g. water waves).
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A very interesting thing about wave motion is that waves can move faster than the individual particles making up the waves.
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Indeed, if you set things up just right the constituent particles may just move up and down, or even backward (compared to the wave), while the wave itself moves quickly forward.
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Something very similar happens in research and discovery. You think of individual researchers as individual particles. It's possible for the most exciting research frontiers to move very rapidly round the research ecosystem - far faster than any researcher can move.
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An example: suppose in 2004 you happened, by coincidence, to take university classes in linear algebra, AI (including neural nets), and GPUs. You didn't do this with any aforethought - at the time, these weren't necessarily even thought to be so closely connected.
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No offense at all meant to my brilliant deep learning friends! Just pointing out that there is a lot of luck in these things.
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Another example: someone may become famous doing some type of research. They look like a visionary, way ahead of the curve. But later they continue pursuing what others consider dead end ideas. But perhaps it just shows that they move slower than the general velocity of discovery
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Furthermore, that can be a good thing! We need at least a few people who continue pursuing what are now unfashionable ideas.
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I find this line of thought extremely helpful when I'm finding it tough to find a research problem I'm really excited about. I can't move as fast as the overall frontier of opportunity moves, and shouldn't try to. It's better to figure out where the wave really ought to be.
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That is, work on discovering really important problems that rely on my strengths & interests, a long time before others do, & doing something about it. I'll be unfashionable, even incomprehensible, much of the time. But also more likely to work on what matters than chsing fashion
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And, sometimes, it means just being patient, not trying to force it, and jumping on an unimportant problem out of some mistaken desire to be busy or to do what is fashionable.
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A missed tweet, just before "No offense": 10 years later you look like a genius who foresaw deep learning becoming huge. But maybe you were a product of good luck: lots of people take many combinations of classes, & a few will by chance take combinations that later look prescient
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End of conversation
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