Epistemic status: Reasonably confident, but I should probably try to back this up with numbers about how often elementary results actually do get missed.
Attention conservation notice: More than a little rambling.
Fairly regularly you see news articles about how some long-standing problem that has stumped experts for years has been solved, usually with some nice simple solution.
This might be a proof of some mathematical result, a translation of the Voynich algorithm, a theory of everything. Those are the main ones I see, but I’m sure there are many others that I don’t see.
These are almost always wrong, and I don’t even bother reading them any more.
The reason is this: If something is both novel and interesting, it requires an explanation: Why has nobody thought of this before?
Typically, these crackpot solutions (where they’re not entirely nonsensical) are so elementary that someone would surely have discovered it before now.
Even for non-crackpot ideas, I think this question is worth asking when you discover new. As well as being a useful validity check for finding errors and problems, if there is a good answer then it can often be enlightening about the problem space.
Potentially, it could also be used as a heuristic in the other direction: If you want to discover something new, look in places where you would have a good answer to this question.
There are a couple ways this can play out, but most of them boil down to numbers: If a lot of people have been working for a problem for a long time during which they could have discovered your solution, they probably would have. As nice as it would be to believe that we were uniquely clever compared to everyone else, that is rarely the case.
So an explanation basically needs to show some combination of:
The first is often a bad sign! If not many people work on the problem, it might not be very interesting.
This could also be a case of bad incentives. For example, I’ve discovered a bunch of new things about test case reduction, and I’m pretty sure most of that is because not many people work on test case reduction: It’s a useful tool (and I think the problem is interesting!), but it’s a very niche problem at a weird intersection of practical needs and academic research where neither side has much of a good incentive to work on it.
As a result, I wouldn’t be surprised an appreciable percentage of person-hours ever spent on test-case reduction were done by me! Probably not 10%, but maybe somewhere in the region of 1-5%. This makes it not very surprising for me to have discovered new things about it even though the end result is useful.
More often I find that I’m just interested in weird things that nobody else cares about, which can be quite frustrating and it can make it difficult to get other people excited about your novel thing. If that’s the case, you’re probably going to have a harder time marketing your novel idea than you are discovering it.
The more interesting category of problem is the second: Why have the people who are already working on this area not previously thought of this?
The easiest way out of this is simply incremental progress: If you’re building on some recent discovery then there just hasn’t been that much time for them to discover it, so you’ve got a reasonable chance of being the first to discover it!
Another way is by using knowledge that they were unlikely to have – for example, by applying techniques from another discipline with little overlap in practice with the one the problem is form. Academia is often surprisingly siloed (but if the problem is big enough and the cross-disciplinary material is elementary enough, this probably isn’t sufficient. It’s not that siloed).
An example of this seems to be Thomas Royen’s recentish proof of the Gaussian Correlation Inequality (disclaimer: I don’t actually understand this work). He applied some fairly hairy technical results that few people working on the problem were likely to be familiar with, and as a result was able to solve something people had been working on for more than 50 years.
A third category of solution is to argue that everyone else had a good chance of giving up before finding your solution: e.g. If the solution is very complicated or involved, it has a much higher chance of being novel (and also a much higher chance of being wrong of course)! Another way this can happen is the approach looks discouraging in some way.
Sometimes all of these combine. For example, I think the core design of Hypothesis is a very simple, elegant, idea, that just doesn’t seem to have been implemented before (I’ve had a few people dismissively tell me they’ve encountered the concept before, but they never could point me to a working implementation).
I think there are a couple reasons for this:
So there aren’t that many people working on this, they haven’t had that much time to work on it, and if they’d tried it it probably would have looked extremely discouraging.
In contrast I have spent a surprising amount of time on it (largely because I wanted to and didn’t care about money or academic publishing incentives), and I came at it the long way around so I was starting from a system I knew worked, so it’s not that surprising that I was able to find it when nobody else had (and does not require any “I’m so clever” explanations).
In general there is of course no reason that there has to be a good explanation of why something hasn’t been discovered before. There’s no hard cut off line where something goes from “logically must have been discovered” to “it’s completely plausible that you’re the first” (discontinuous functions don’t exist!), it’s just a matter of probabilities. Maybe it’s very likely that somebody hasn’t discovered it before, but maybe you just got lucky. There are enough novel things out there that somebody is going to get lucky on a fairly regular basis, it’s probably just best not to count on it being you.
PS. I think it very unlikely this point is novel, and I probably even explicitly got it from somewhere else and forgot where. Not everything has to be novel to be worthwhile.