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For instance, there's currently a great deal of attention towards the theory of "spin glasses" in probability theory. But how does a research direction gain its importance so quickly? Does it simply start with one researcher who declares that this research direction should be given a lot of attention?

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    Spin glasses are new?? – JeffE Feb 20 '17 at 2:52
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    Extra funny, since I thought of spin glasses as having a huge fad peak in the 1980s or so... but maybe there's a resurgence! – AJK Feb 20 '17 at 3:41
  • As the OP writes, spin glasses are a relatively recent subject of interest in probability theory, in the sense of "among people who describe themselves as probability theorists, and publish in probability journals". Physicists started thinking about them much longer ago. – Mark Meckes Feb 20 '17 at 16:47
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The current answers are both good answers to the general question, but neither really applies in the particular case singled out by the OP or other situations like it. Spin glasses have been studied by physicists for decades, but until relatively recently the most popular mathematical models of spin glasses appeared to be beyond the reach of rigorous mathematical analysis. Following some breakthroughs circa 2000 (due particularly to Talagrand), probability theorists now recognize that this is a fruitful area to research, full of problems that are hard enough for progress to be interesting, but possibly within reach of current mathematical techniques.

This kind of thing happens a lot in mathematics. Many so-called pure mathematicians are much more interested in real-world phenomena than they are made out to be, and are always on the look-out for interesting problems inspired by real-world phenomena. But most real-world phenomena are simply too complicated to be amenable to proving theorems about them. So if someone shows that some physical model --- possibly a highly simplified toy model, but complicated enough to reflect something of what might go on in the real world --- is within the reach of rigorous mathematical analysis, then mathematicians often flock to work on it. If it's just the right level of difficulty, so that new theorems keep getting proved, but it's hard work, then it can hold mathematicians' interest for a long time.

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In my (limited) experience in academia, I've noticed that the research topics that gain the most importance & attention tend to be the ones that impact the most people.

Sometimes (often) it takes a while for new research to become important. For example, in my field of computer engineering, machine learning has been researched for decades. But only in the last 5-10 years has it truly caught fire, as computational power, software libraries, etc. finally reached the point where the average researcher could quickly and easily make use of machine learning techniques. Now, you see its use in everything from engineering to the social sciences because of its power in extracting useful information from large datasets.

Sometimes new research topics become important because they disrupt a large amount of research. Einstein's theory of special relativity (eventually) opened up vast new fields of research -- but not before facing criticism from classical physicists who saw their life work as being under attack.

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One somewhat counterintuitive thing in mathematics seems to be that a topic A attracts new attention whenever someone finds an application of A to a topic B (this is, of course, understandable), but also whenever someone finds an application of a topic B to A (this is the counterintuitive part). The reason, I guess, is that applications are rarely one-way roads in mathematics, and usually point to deeper connections which can then be walked down both ways (although one of the directions is often easier). The other reason is that people want to be useful and thus like to explore fields where their experience could help, even if they don't care that much about these fields on their own.

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