“What are you gonna do with your life?”
College freshmen (and many graduates… and many adults) all grapple with this question. If you’ve been naive enough to answer “science!” then you’re faced with the follow-up: “Well, what are you gonna study?”
Most young knowledge warriors charge straight at whichever field their best teacher from high school or college was from, certain that their initial passion will never wane. Yet talk to these firecrackers seven years later and notice how many grad students have lost that spark. What once was a tantalizing realm of puzzles and mysteries becomes a never-ending cycle of mundane tasks.
Science can certainly be a cruel succubus, but considering one important feature of a field before hopping on the bandwagon can help avoid this.
Ripeness & Saturation: The Potential of a Science
The key is to compare the current set of ideas with the potential for developing new ones given available data, tools for acquiring data, and culture. Too little new available data, too few tools for acquiring data, or cultural norms that enforce old paradigms can all hinder the potential for interesting projects. Quantum gravity might be an instance of the first two shortages whereas 16th century astronomy (influenced by the church doctrine of a geocentric universe) is a good example of the last. Let’s call these saturated fields.
On the flip side, an abundance of data, the invention of tools for acquiring new data, or changing cultural norms can all provide opportunities for great projects. Genomics is experiencing the first two surpluses whereas complex systems research in the early years of the internet (and the metaphors about networks that accompanied it) probably benefited greatly from cultural shifts. Let’s call these ripe fields.
Your mission, young sailor of the scientific seas, is to find one of these gems.
Now, how can you tell? You can’t be sure, but here are some good signs:
- Researchers still identify themselves with another more traditional field and just list this one as an “interest.”
- It attracts researchers from many different backgrounds and much of the work done is considered “interdisciplinary.”
- A new institute pops up every week or so.
- A large percentage of new papers all reference one or a few papers written in the last five years.
- The introductory textbooks were all written in the last few years and there is no consensus on which is best.
Some signs of a saturated field include:
- Systematized jargon (new ideas and discoveries get ID numbers rather than names)
- A large percentage of new papers are written to make small corrections on old ones (the field has become recursive).
- There are introductory textbooks in their twelfth edition and most professors use the same text to teach as they did to learn.
I’d wager quantum computing and neuroscience are ripe for the picking.
Which fields would you add? And which criteria for identifying ripe and saturated fields would you use?
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6 responses so far ↓
Excellent post. This one really spoke to me. It’s definitely why I’ve become more interested in web development than physics recently. Hopefully computational physics isn’t too full…
Two comments on that.
One, I think it depends on what set of problems you’re interested in. Computational physics is just as broad a category as are experimental and theoretical physics. The trick is to apply those methods fruitfully to some unique area, be that of “physics” proper or another field (*cough* brains!).
Two, science in the age of massive data sets is still wide open. Check out that Fourth Paradigm e-book I sent to you a while back. We’re learning to acquire data faster than we’re learning how to deal with it and new things are becoming “datafied” and placed into the realm of analysis (i.e. the process of science itself via projects like CoLab).
Perhaps what I’m saying is that computational science is ripe with open problems.
My category theory lecturer, a font of anecdotes and dry wisdom, said exactly the same thing to me. And then was somehow surprised when I failed to take up the baton of category theory — a 50 year old branch of pure mathematics!
I’m tempted to think that Wolfram’s self-styled “NKS” presents one of these new fields: the universe of simple computational systems and their behavior. Two things make it ripe:
1) for a couple of reasons to do with undecidability, there isn’t very much that traditional analysis can say about these systems, and so people haven’t thought them worth studying. However, consumer computing is just now hitting the point where one can perform large-scale data mining on the space of possible simple computational systems
2) Heavily-architected systems like CPUs are all well and good at the micron scale, but get small enough and traditional engineering stops working. At some point we’re going to have to exploit emergence, self-assembly and all the other sexy buzzwords, and NKS-y type science is suited for exactly this.
Disclosure: I’m a Wolfram employee who works on Wolfram|Alpha.
Re: 1) You hint at a good point here – the age of a field might not be a good indication of its ripeness or saturation because often, interesting or suggestive results are ignored if the path forward is not amenable to currently available tools. So potentially profound implications are unexplored in favor of lower hanging fruit. It’s possible for ideas to precede tools necessary for their further analysis (in which case I would say the field is neither ripe nor saturated but perhaps ‘green’). It’s also possible however, as you point out, that a field may be ripe but not recognized as such because the appropriate tools of analysis are new or frowned upon by the scientific establishment. I’m still appalled at the number of mathematicians and physicists who balk at the ideas of data mining and numerical explanation as research tools, favoring instead their perhaps brilliant yet limited and fallible minds.
Re: 2) Interesting. This suggests another way to look at saturated fields – as disciplines flirting with the edge of human analytical intelligence. That is, there may be plenty more ideas to be discovered, but that they are far more amenable to numerical exploration, data mining, or other tools that do not rely as much on foresight.
Re: Re: 1) Green, I like that
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Re: Re: 2) I’m being a bit pedantic, but I think there’s still a morself of historical bias hiding in your last sentence. You characterized experimental mathematics as trading off the use of powerful new tools for a decrease in foresight. Why? Just because one plays Advanced Chess, where all the moves one makes are vetted by a supercomputer, doesn’t mean one stops thinking as much. It’s just that you can now think about different things. You can ask different, higher-level questions that for their details require computations of mind boggling complexity that no human could ever perform.
Re:^3 2) I did not mean to imply the human role played in such science was trivial or didn’t require foresight. Perhaps the better way to word what I meant is:
A field can be in a state such that unassisted human reasoning has reached a saturation point but that human reasoning assisted with sufficient additional computational power can still provide new insights.
It’s unclear to me whether the role of the scientist is actually different in such a scenario, or if computers simply play a role analogous to that of pen & paper, telescopes, and the rest of the paraphernalia of science.