There is no widely agreed upon list of the most important intellectual questions. Nor even a well-known attempted list, upon which people disagree. As far as I can tell there is hardly even such a list for any specific field. I don’t know of even a single person who has such a list. The closest things I know of are Hilbert’s list of important mathematical problems, published in 1900, a few less well knows lists by later mathematicians, some of Edge’s Question Center lists, and a recently compiled list by of problems in social sciences.
Perhaps you can find (and please send me) examples to prove there are such things, but my point remains that such lists are not common or popular. It seems that we hardly even discuss what the most important questions are. I don’t know off the top of my head what I think they are, even for the fields I am especially interested in. I could probably come up with a list if I thought about it, but it is surprising that I have not sufficiently done so already. I have even less idea how other people would answer. This seems strange. The idealistic intellectual’s supposed self-imposed quest is to work out these big important problems, or chip tiny bits off the sides of them. It seems it would be useful to keep in mind what we think these problems are.
I’m tired, so instead of compiling such a list, I’ll just give you one question. Why are such lists not more popular? I don’t know. But here are some ideas in no particular order:
- ‘Important questions’ is just too vague a category.
This seems false; there is generally public agreement about which additions to human knowledge are significant advances. If it is too vague, it could be narrowed to either questions of practical importance or those with theoretical interestingness.
. - ‘Questions’ are too vague an entity.
How important a question is just depends on how abstract you make it, and questions abstracted too far are useless. ‘How can we make the universe perfect?’ is presumably the question of most practical importance, and is not interesting at all. I don’t think this is really a barrier though. I’d be surprised if our intuitive notion of what is an optimally abstracted question did not serve. Or we could just pick a rough level of abstraction and stick to it.
. - Nobody cares about intellectual progress on big ideas. Intellectuals are all about signaling their academic ability, and asking questions doesn’t do that.
This seems false and immaterial. For someone to make a list it need not be that most people are motivated by intellectual progress on big ideas. Only a small fraction need be motivated. And they need not be motivated by intellectual progress on big ideas alone – there are other kinds of attention one could get from such an activity. A person could demonstrate confidence in his judgement and informedness, like having an opinion on the best wines or films can in other circles does. Knowing enough about enough things to write a decent list would be quite a feat I think. Many intellectuals write blogs, and I expect compiling such a list could get an amount and type of attention not unlike a period of blogging, even if the list was collected from the opinions others. I would expect some section of intellectuals to be motivated even if the majority are not.
. - Such a list would not actually be useful, since whoever had a say would use their answer to look good, or advertise a problem that they are already working on.
This is arguably illustrated within some of the near-examples I listed. However it should be possible to get around this, for instance by each person having to nominate a number of questions, or by the authors being sensible to the effects on their credibility if they so blatantly self-promote.
. - Most intellectuals are already working on something, and prefer to think that it is one of the most important things. So they would be actively opposed in the same way that doctors are opposed to finding out and publicising which hospitals are least likely to kill you.
This is supported by the observation that whenever you begin a new subject at college you are introduced with the assurance that anthropology for instance really is the bedrock upon which all other puny scientific pursuits are built. But if this is a force against scrutiny of importance, it is not so obviously so that it should have put off anyone from trying to make such a list.
Why do you think we don’t keep lists of the big questions?
Meteuphoric 
Asking questions also doesn’t let you as easily signal loyalty by taking sides, or signal your connections by showing knowledge of current fashion. Blogs do both those things well.
From Richard Hamming’s really great talk (http://www.cs.virginia.edu/~robins/YouAndYourResearch.html)
> “If you do not work on an important problem, it’s unlikely you’ll do important work. It’s perfectly obvious. Great scientists have thought through, in a careful way, a number of important problems in their field, and they keep an eye on wondering how to attack them. Let me warn you, ‘important problem’ must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn’t work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important.”
(Application of this quote is left as an exercise to the reader.)
I don’t think this article is correct at least as far as mathematics and theoretical computer science goes -= because the Clay Millennium Problems are obvious a worthy descendent’s of Hilbert’s Problems for mathematics and I doubt there is a mathematician alive who isn’t familiar with them. There is even, for example a very nice popular math book by Keith Devlin on them that I commend to you.
(The Poincare conjecture of course has been solved..)
A Google Scholar search on “important open problems” returns about 2000 hits.
Here is a definitive list of the absolutely most important open questions:
1) What are the important open questions?
Or to put it in a more helpful way, I think your problem is at your point numbered 1, specifically,
“This seems false; there is generally public agreement about which additions to human knowledge are significant advances. ”
I think this is wrong. If there is such public agreement, surely that implies your question list already exists, or is trivial to compose? And yet you haven’t done so already?
There is generally after the fact agreement about which advances turned out to be significant. But to take one particularly celebrated advance, consider the once open question
Why did the Michelson–Morley experiment fail to detect the Aether?
Now clearly there was a sense amongst physicists at the time that this was an important question. But there was no public consensus about exactly how important until 18 years later (well more really, given the answer didn’t gain either instantaneous acceptance or comprehension.) And it might have turned out to have been just some boring methodological error.
Likewise, to take a current open problem widely considered important in Computer Science, P = NP. There’s agreement its important, but a lot of argument about exactly how much, which only the actual answer will settle. If the answer turns out to be a moderately efficient polynomial algorithm for every problem in NP, the consequences will be utterly profound. If it turns out to be just a long, technically difficult proof that P /= NP, theoretical computer scientists will still celebrate that, but it might not end up mattering much to everyone else. If the answer is something a bit more out of left field, e.g. P = NP is independent of ZFC, well the consequences are equally hard to see coming.
Fundamentally, perfect information about the relative importance of questions is probably a more difficult thing to learn, in many cases, than the answer itself, as it implies knowledge not just of the content of the question itself, but of all the other questions.
Is P = NP more important than the existence of the Higgs Boson? Only an extreme expert in both Computer Science and Particle Physics who can see the future could give a decent answer.
I think it’s a mixture of 2, questions being too vague, and then once they are no longer too vague, that they tend to be solved pretty quickly.
One could ask the general question “how does gene regulation work?”, and that is a big open important question, but it’s vague as there are a bunch of ways gene reg could work, so you have to divide it into subproblems, but you don’t really have any idea what those are, until you find some type of experimental evidence, at which point it becomes much more clear. But then you are really just asking what % of variance each component of gene regulation you discover can explain.
So really I think the problem with these questions is that they are often too vague, so people don’t really collect them because they don’t tend to be that useful.
Basic research is a lot like venture capital. You invest in 1000 different things, hoping that one of them pays off. I don’t think it’s possible to predict which problem will be the most important ahead of time. That’s one of the big problems with the current crop of tech billionaire philanthropists who think they can “bring business discipline to research”. It’s a bit of a counterproductive fantasy to think that we can orchestrate and direct scientists’ efforts in a way that will make the big discoveries more likely.
Having said that, we know what some of the big problems are. Energy and mortality seem to be big ones. Perhaps people don’t make lists because the really big problems loom so large. When you’re about to get hit by a train, you’re not making lists.
Conquest, war, famine, and death are all issues relating to human biology and psychology, and since the overall design-structure of those has arisen out of evolutionary forces — physical anthropology. Merged with psychology, you get evolutionary psychology. It is interesting just how much animosity has been directed over the last twenty years toward that field which has as it’s core mission the establishment of a science of human nature. Here’s the (now very old) Don Brown list proposing possible research programs into human nature: http://www.robotwisdom.com/ai/universals.html
A better link is, http://condor.depaul.edu/mfiddler/hyphen/humunivers.htm
Well, Wikipedia does have a list of unsolved problems in physics and several other fields.
Here’a list of “hard problems in the social sciences” that was recently produced through some sort of semi-participatory process:
http://socialscience.fas.harvard.edu/icb/icb.do?keyword=socialsciencedivision&pageid=icb.page336066
We don’t think about the big questions anymore because we are humbler than we used to be. We no longer strive for immortality, but at most to make a contribution. That’s also why there are so few heroes now, only more or less popular individuals, who we often suspect are chasing vainglory rather than true glory.
We are in the modern age, in which we are embedded in complex relations of interdependency on others for everything. That goes for academia too. The old philosophers had the courage and world-view to take anything; the modern philosopher (except for the naive undergraduate) reaches immediately for methodology and a niche in the scholarly conversation
1. Artificial Intelligence
In some fields asking big questions, especially lists of such questions, can actually be a very high status thing. The most famous example is probably David Hilbert’s presentation of his 23 problems.
There are lists in many fields, for example important psychology experiments. I would add:
1) What many of us humans feel are “meaningful questions” are either meaningless noise that don’t admit of much investigation which revealing themselves as such, a fact which most of us would prefer not to confront – or more charitably, that even if such questions are meaningful, we just have no way to approach them clearly, to paraphrase a previous commenter. Writing and discussion about these questions then is mostly art or entertainment, rather than problem-solving.
2) People who think about Important Questions usually self-identify as intellectuals and so like to signal this status (as Katja observed). But rather than arguing that their first concern isn’t solving these questions, the problem is that self-identified intellectuals shy away from things as rote and mundane as lists. It would support the idea that self-identified intellectuals do care about solving concrete problems but dislike lists if, in complex jobs where employees have a reputation for being very smart, those employees irrationally avoid lists, vs equally complex jobs where employees don’t have such a reputation. And indeed, in the U.S. it has been a struggle to get physicians and especially surgeons to start using checklists, despite clear evidence that they improve outcomes and save lives. Meanwhile, pilots (who have complex jobs but who don’t status-signal based on intellect to nearly the same degree) have no problem with checklists. The best explanation I’ve encountered is that using lists just makes surgeons afraid they’ll seem less cool. (If Hanson reads this comment he’ll like that).