In present day academia, it seems much harder to make foundational breakthroughs than it was in the past. Most work now synthesizes previously discovered results to study something extremely specific. Although this extremely specific thing may be valuable to know, it generally does not have the potential to rewrite the field.

For example, in physics, the beginning of the 20th century saw the revolutionary development of general relativity and quantum mechanics. While there is still much to be learned in modern physics research, it is much more difficult for someone to make large, fundamental contributions to the field, simply based on the fact that the large, fundamental contributions were already made. Now, even an extremely productive researcher may only become well-known in their immediate subfield. Similar notions can be applied to art and a variety of other academic disciplines, in which it is more difficult for one single artist's work to be foundational to the field.

Do academics worry much about the growing insignificance (for lack of a better word) of their work? Or is any knowledge gained worth the effort, simply because the academic enjoys studying the topic (no matter how esoteric)? Any sort of discussion about this concept would be enlightening.

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    One might suggest that there are only so many 'fundamental discoveries' or 'foundational breakthroughs' out there. You just pay attention to them, and don't notice all the other work going on around them at the time. But, I don't see really how this question can be answered here. – Jon Custer Feb 25 at 14:41
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    How do you know that the 'large, fundamental contributions' in physics are all already made? A lot of people in the second half of the 19th century believed that physics was mostly done and didn't have much of a future as a research discipline. Today we can't properly mesh quantum physics and general relativity and we don't understand situations where both are relevant. – quarague Feb 25 at 15:04
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    Problems that remain unsolved in contemporary physics include (1) the nature of dark matter, (2) the nature of dark energy, and (3) quantum theory of gravity. The solution of any of these is, I think, likely to be a foundational breakthrough or at least lead directly to a foundational breakthrough. A problem may look specialized (e.g., black body radiation spectrum, or the Michelson-Morley experiment) until its solution turns out to rewrite the foundations of physics. – Andreas Blass Feb 25 at 17:58
  • @quarague exactly. the true masters make the impossible seem trivial. if I have seen farther, it is because I have stood on the shoulders of giants. I got good grades in my calculus classes and I mastered the material well. This in no way implies I could have discovered calculus had I been born several centuries earlier. – emory Feb 25 at 22:37

Actually, exactly the same question might have been asked around 1900 when Henri Poincaré ruled the world.

There is a tradeoff, of course. Some fields get saturated and the seemingly important questions get answered, closing the field in some ways. But those fundamental breakthroughs may open new lines of inquiry. And there is the corresponding effect that other fields open up. Mathematics is like the latter. People today think about a lot of mathematical ideas that didn't really exist historically.

Whether physics is a fixed field in which everything will eventually be known is, I think, an open and debatable question. I suspect that there will be new ways of thinking about things and thus new and important questions as long as humans can manage to still exist. Quantum entanglement is still pretty "spooky".

And in the social sciences we may be only at the beginning of what can be known.

Moreover, each new generation of scientists, in whatever field, starts out at a higher level than their predecessors, and so, have a base on which to reach still higher, with a deeper understanding. Poincaré had problems grokking relativity, as did many of those in his generation. After they started to actually die, relativity came to the fore.

  • +1 -- Even if some fields are decidedly "solved", there will never be an end to science itself. – 6005 Feb 25 at 19:05
  • Your answer resonates with a recent find in our university library: «Breakthroughs in Statistics» edited by Samuel Kotz and Norman L. Johnson. In the second volume, Gosset's / Student's contribution to statistics by his $t$-test is presented by Lehman including the statement «The importance of Student's new approach was not immediately realized by his contemporaries. Not too much blame should be attached to them for this lack of perspicuity since Student himself does not seem to have been aware of the significance of his contribution.» (doi 10.1007/978-1-4612-4380-9_3, p. 30) – Buttonwood Feb 25 at 20:34

Do academics worry much about the growing insignificance (for lack of a better word) of their work?

This looks like a personal question, so I'll give a personal answer. I have no idea how widely my opinion is shared, so don't attach too much "statistical significance" to it. IMHO, most of us (myself included) have never had any chance to make any "major breakthrough" in anything by ourselves. Such breakthroughs can occasionally be made out of the blue (at least, in mathematics) but more often than not they just occur when the time is ripe meaning that the relevant tools and ideas get slowly developed to solve lesser problems, many of which will be later just forgotten. So, I view my task as merely trying to figure out things that haven't been figured out yet in the hope that in the process I'll find some new approach or, at least, a new twist of an old technique that will come handy later when some people smarter than I will solve some "big problems". The nice thing (again, I can confidently say it about mathematics only, but it may apply to other sciences as well) is that our knowledge is (at least currently) resembling not a solid disk like in that famous depiction of PhD, but rather the Sierpinski carpet, so you can make a small side step from any position and find yourself on an uncharted territory where life immediately gets interesting enough to render all your existing knowledge if not totally irrelevant, then, at least, rather hard to use. Moreover, you don't need to search hard for those side steps.

is any knowledge gained worth the effort I would say yes, but not simply because the academic enjoys studying the topic.

To start with, enjoyment is a rare event. The normal state is somewhere between slight frustration and deep depression and the main feeling is that of being totally inept and stupid. Normally with any problem worth being called by that name you start as "a blind kitten in a dark alley" going by touch, bumping your head against everything, and backtracking from dead ends at every turn. Slowly you may start seeing some light and distinguish some shapes (the more alien they look, the more interesting). Finally, if you are lucky (more often than not that event never comes), your eyes suddenly open fully and you see the surroundings and your way through. Then you have your few minutes of "enjoyment".

The value of any piece of knowledge comes primarily from the fact that the connections between problems, their relative significance, etc. are totally unclear until everything is done (by which time one writes short end elegant textbook expositions for students using about 1% of the work that went into obtaining a theorem). You cannot possibly predict what effect the solution of any particular "small problem" will have "on the big scale" as long as that solution is not achieved by totally routine means that have been available before. Usually you are just collecting sand grains that will be later mixed with water and cement powder to make blocks that later will be put together to form walls of magnificent buildings that together will form the city we call "scientific knowledge". Thinking of great cities, one rarely thinks even of cement blocks, let alone the sand particles (though some individual buildings may still come to mind and, on rare occasions, even the architect's names, but not the names of more numerous masons that did the work). The same with mathematics. The collectors of sand particles get always forgotten and the sand itself just becomes "common building material" available in abundance, but it is an endless process of sand collecting that makes the higher level building possible in principle. So, I'm personally quite content with being a "sand collector".

One may argue endlessly about whether there exists a qualitative difference between the process of obtaining a mathematical equivalent of a sand grain and that of building a grand theory. I would just say that a good theory builder works at higher level than a bad sand collector and a good sand collector works at higher level than a bad theory builder and stop at that (like a good CEO is worth more than a bad janitor but a good janitor is worth more than a bad CEO).

As to "most large contributions have already been made", I doubt it very much (though, by the very nature of the question, I am unable to come with explicit examples of the large contributions to be made within the next 50 years). The life is abundant with crazy twists and so is science. One just plays the game and sees how much he can score, leaving the erection of various "Halls of Fame" to future generations. Let me ask you one question however: you mention "general relativity" and "quantum mechanics". How well do you know either one? (I should confess that I'm almost a total ignoramus). If not really well, then those "major contributions" haven't happened in your life yet (though you can benefit from them indirectly), so it may be a good idea to scale down a bit and see how many relatively major things happened recently in the domain you have good knowledge about (say, within the particular area of research you work on) and then project the number upward making (perhaps, unwarranted) assumption that you just don't see the whole large picture but it is not dissimilar to the smaller scale one.

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    This all tallies pretty well with my own perspective (also from within mathematics). – Mark Meckes Feb 25 at 17:40
  • Agree with this perspective, I think it holds in computer science as well (even the more applied subareas). (+1) – 6005 Feb 25 at 19:02

In present day academia, it seems much harder to make foundational breakthroughs than it was in the past. Most work now synthesizes previously discovered results to study something extremely specific. Although this extremely specific thing may be valuable to know, it generally does not have the potential to rewrite the field.

I see at least two factors at play in explaining this phenomenon, and the upshot may not be as cynical as it seems.

1. It only seems harder, due to survivor bias

Comparing academics today to Einstein is not a fair comparison due to survivor bias. Einstein was not the only physicist working in his day. For every Einstein there were at least hundreds of other people who tried to work on physics but failed to invent general relativity. For every Archimedes and Euclid there were at least dozens of other mathematicians who failed to make a name for themself reaching into the present day. In fact, it is impossible to even tell how many there were, as most have been lost to history: they will not have a Wikipedia page, or any mention on the internet, etc.

In other words, you are comparing the average academic of today with the most successful academics of the past, so you are not comparing apples to apples.

If we were to compare the average academic today and in the past, would we see a difference in how difficult it is to make foundational breakthrough? I expect that there would still be some effect, but it would not be nearly as pronounced.

2. Scientific progress inherently involves specialization

Looking back on foundational results like Einstein's theory of relativity (or Turing's definition of a computer, or Mendeleev's discovery of the periodic table), we get the feeling that a "breakthrough" is something like a huge paradigm shift, where everything we knew before was wrong, and now some new theory is found to be correct instead. But as science progresses, paradigm shifts may become less and less common, because we see that many prior breakthroughs turned out to be correct, so we must build on them rather than replace them. And the way that this happens is that subfields develop which build on the previous (now thought to be correct) theories in different ways, and/or explore the limits where those theories do not apply.

But is it accurate to say that these "specialized" results as less "foundational"? When Turing invented the definition of computer, he was a mathematician, not a computer scientist: at that time, you could say that computer science was just a small subset of math. But it later grew into its own field (and separated from engineering as well, a century later). So today, "computer science" is its own field, along with "physics", "chemistry", "biology", etc.

In summary, the possibility for foundational results within a field is independent of time; it is just that the set of fields changes. For example, today, rather than making foundational results in physics as a whole, you might try to make foundational results in quantum mechanics or in fluid dynamics.

  • I'm unsure about aspect 1. I think the comparison is not between an average scientist of today and Einstein, but about the best scientist of today and Einstein, the point being that not any such revolutionary discoveries as general relativity are made today. – lighthouse keeper Feb 25 at 15:19
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    @lighthousekeeper True, but I was responding especially to this part: Most work now synthesizes previously discovered results to study something extremely specific. That is talking about most work, not the best work. If the question is about the best work today and in the past, then the answer would be different. And I think it is easy to compare the present and past incorrectly, failing to account for survivor bias. – 6005 Feb 25 at 15:25
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    @lighthousekeeper The thing is, it's hard to tell today whether any of the best scientists of the current decades will go down in history as Einsteins. I suspect some will - there is still much we have to learn in many fields. – xLeitix Feb 25 at 15:46
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    @lighthousekeeper Public key crypto was only invented in 1976. In computer science that's as foundational as relativity. I think we see similarly foundational results at least a few times a decade (although I can't tell whether the pace is slowing down or speeding up!) – 6005 Feb 25 at 18:59
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    @6005 Now that you say it, I suspect if quantum computing becomes a real thing it will change computer science comparably to how relativity changed physics. – xLeitix Feb 26 at 15:04

The problem is not that there are no fundamental problems to solve. The problem is seeing the obvious big problem just at your feet while you are checking the horizon.

This happens more often than one would think. Perhaps not in the magnitude of the great two theories of QM and relativity, but there are quite amazing surprises lurking all around us. Just to give an example, in game-playing AI, the rediscovery (for the second time) of deep feed-forward networks and their combination with Monte Carlo Tree Search cracked a problem that was considered open for another 30 years (winning against the human Go champion).

Yes, this was a numbers' game, but with the old techniques, even with all number crunching power available, we probably would still be far off.

Information theory is a big one. After its discovery by Shannon, confined for a long time to the computation of point-to-point data transmission and a bit of glorified correlation measure, has now become an incredibly powerful Swiss army knife for all kinds of analyses and AI algorithms with major subbranches emerging every few years.

Or remember Quantum Computing, with its complete rethinking of what computation means.

Or the Quantum Decoherence framework which does away with the ad hoc Kopenhagen Interpretation axiom of measurement and embeds the latter organically as part of QM proper which leads to (experimentally verifiable) models for the dynamics of measurement in QM. This is particularly remarkable, because essentially for a long time any attempt to "understand" measurement properly in the QM framework was bluntly dismissed by the mainstream community with reference to Kopenhagen. This may have held back our theoretical understanding by decades. Zurek and his colleagues, however, understood that here is an important phenomenon to characterise here, and while the relevant mathematics is not particularly difficult in principle, and matches effectively what Kopenhagen had to postulate as axiom, they needed to attack the belief that what seemed obvious most certainly wasn't.

In short (I do not know who to attribute this saying to): "The fish is the last to discover water." - The water is there, but recognising it is the actual challenge.

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