Mountain climbing is a beloved metaphor for mathematical research. The comparison is almost inevitable: The frozen world, the cold thin air and the implacable harshness of mountaineering reflect the unforgiving landscape of numbers, formulas and theorems. And just as a climber pits his abilities against an unyielding object — in his case, a sheer wall of stone — a mathematician often finds herself engaged in an individual battle of the human mind against rigid logic.
In mathematics, the role of these highest peaks is played by the great conjectures — sharply formulated statements that are most likely true but for which no conclusive proof has yet been found. These conjectures have deep roots and wide ramifications. The search for their solution guides a large part of mathematics. Eternal fame awaits those who conquer them first.
Remarkably, mathematics has elevated the formulation of a conjecture into high art. The most rigorous science cherishes the softest forms. A well-chosen but unproven statement can make its author world-famous, sometimes even more so than the person providing the ultimate proof. Poincaré’s conjecture remains Poincaré’s conjecture, even after Grigori Perelman proved that it is true. After all, Sir George Everest, the British surveyor general of India in the early 19th century, never climbed the mountain that today bears his name.
Like every art form, a great conjecture must meet a number of stringent criteria. First and foremost, it should be “nontrivial” — that is, not too easy to prove. Mathematicians will say things like “A problem is worth tackling only when it fights back,” and “If it’s not frustrating, you’re probably working on a problem that is too easy.” If a conjecture is proved within a few months, then perhaps its creator should have pondered it a bit longer before announcing it to the world.
The first effort to compose a comprehensive collection of the greatest mathematical challenges was made at the turn of the previous century by David Hilbert, who has been characterized as the last universal mathematician. Although his list of 23 problems has been very influential, in retrospect it was something of a mixed bag.
It included all-time favorites like the Riemann hypothesis — often considered the greatest of great conjectures, one that has remained the Everest of mathematics for over a century. When Hilbert was asked what would be the first thing he’d like to know after awakening from a 500-year slumber, he immediately picked this conjecture. It captures an essential intuition about the distribution of prime numbers — the atoms of arithmetic — and its establishment will have vast consequences for many branches of mathematics.
But Hilbert also listed much vaguer and more open-ended goals such as “the mathematical treatment of the axioms of physics” and “the further development of the calculus of variations.” Another of his conjectures, one concerning the relation of two polyhedra of equal volume, was solved in the same year he announced it by his student Max Dehn. While Hilbert described many towering peaks, this turned out to be more of a foothill.
The highest summits are not conquered in a single effort. Climbing expeditions carefully lay out base camps and fixed ropes, then slowly work their way to the peak. Similarly, in mathematics one often needs to erect elaborate structures to attack a major problem. A direct assault is seen as foolish and naive. These auxiliary mathematical constructions can sometimes take centuries to build and in the end often prove to be more valuable than the conquered theorem itself. The scaffold then becomes a permanent addition to the architecture of mathematics.
A wonderful example of this phenomenon is the proof of Fermat’s Last Theorem by Andrew Wiles in 1994. Fermat famously wrote his conjecture in the margin of Diophantus’ Arithmetica in 1639. Its proof required the development of more than three centuries’ worth of mathematical tools. In particular, mathematicians had to construct a very advanced combination of number theory and geometry. This new field — arithmetic geometry — is now one of deepest and far-ranging mathematical theories. It goes far beyond Fermat’s conjecture and has been used to settle many outstanding questions.
A great conjecture also has to be deep and lie at the very core of mathematics. In fact, the metaphor of scaling a summit does not adequately capture the full impact of a proof. Once the conjecture is proved, it is not so much the endpoint of an arduous journey but rather the starting point of an even greater adventure. A much more accurate image is that of a mountain pass, the saddle point that allows one to traverse from one valley into another. In fact, this is what makes the Riemann hypothesis so powerful and beloved. It unlocks many other theorems and insights, and suggests vast generalizations. Mathematicians have been busy exploring the lush valley to which it grants access, even though that valley is still, strictly speaking, hypothetical.
Furthermore, there must be substantial evidence for a conjecture. Niels Bohr famously defined a great truth by the property that its opposite is also a great truth. But this is definitely not the case for a great conjecture. Since there is generally much circumstantial evidence pointing to its truth, the negation is seen as most unlikely. For instance, the first 10 trillion cases of the Riemann hypothesis have been checked numerically using computers. Who, at this point, can still doubt its validity? But all this supporting material does not satisfy mathematicians. They demand absolute certainty and want to know why the conjecture is true. Only a conclusive proof can provide that answer. Experience shows that one can easily be fooled. Counterexamples can lie far ashore, like the one found by Noam Elkies, a mathematician at Harvard University, disproving Euler’s conjecture, a variation on Fermat’s conjecture that states that a fourth power can never be written as a sum of three other fourth powers. Who would have guessed that the first counterexample involved a number of 30 digits?*
The best conjectures usually have modest origins, such as Fermat’s casual note in the margin, but their implications and ramifications grow over the years. It also helps if the challenge can be stated concisely, preferably with a formula containing only a few symbols. A good conjecture should fit on a T-shirt. Goldbach’s conjecture, for instance, reads “Every even integer greater than 2 can be expressed as the sum of two primes.” This problem, formulated in 1742, remains unsolved. It became famous thanks to the novel Uncle Petros and Goldbach’s Conjecture (2000), by the Greek author Apostolos Doxiadis, not least because the publisher offered $1 million as a publicity stunt to anyone who could prove it within two years of the book’s publication. The conciseness of a great conjecture adds to its perceived beauty. One could even define mathematical aesthetics as “impact per symbol.” However, this elegant beauty can be misleading. The shortest statements can require the longest proofs, as again demonstrated by Fermat’s deceptively simple observation.
We should perhaps also add to this list of criteria the response from the famous mathematician John Conway to the question of what makes a great conjecture: “It should be outrageous.” An appealing conjecture is also somewhat ridiculous or fantastic, with unforeseen range and consequences. Ideally it combines components from distant domains that haven’t met before in a single statement, like the surprising ingredients of a signature dish.
Finally, it is good to realize that the adventure does not always end with success. Just as a mountaineer can be confronted by an unsurpassable crevasse, mathematicians can fail, too. And if they fail, they fail absolutely. There is no such thing as a 99 percent proof. For two millennia, people tried to prove that Euclid’s fifth postulate — the notorious “parallel postulate” that states roughly that two parallel lines cannot cross — can be derived from the other four axioms of planar geometry. Then, at the beginning of the 19th century, mathematicians constructed explicit examples of non-Euclidian geometry, disproving the conjecture.
This was not the end of geometry, however. In a perverse way, the refutation of a great conjecture can be even better news than its success, since the failure makes clear that our imagined map of the mathematical world is seriously wrong. Defeat can be productive, the reverse of a Pyrrhic victory. Non-Euclidean geometry proved to be an important precursor of Einstein’s curved space-time, which plays such an important role in the modern understanding of gravity and the cosmos.
Similarly, when Kurt Gödel published his famous incompleteness theorem in 1931, showing that in any reasonable mathematical system there are true statements that cannot be proved, he essentially answered in the negative one of Hilbert’s problems about the consistency of arithmetic. But the incompleteness theorem — often seen as the greatest logical achievement since Aristotle — did not herald the end of mathematical logic. Instead it induced a blossoming that even led to the development of modern computers.
So, in the end, the search for solutions to great conjectures has something else in common with climbing expeditions to the highest peaks. Only when everyone is safely home — whether the goal is reached or not — does the full extent of the adventure become clear. At that point, it is time for the heroic tales of the ascent to be told.
Robbert Dijkgraaf is director and Leon Levy Professor at the Institute for Advanced Study in Princeton, New Jersey.
* 20,615,6734 = 2,682,4404 + 15,365,6394 + 18,796,7604.