Idee für neues Subprojekt: Gegenbeispiel für Beal-Vermutung

[fwjmath]

Could you please explain a bit more in detail why you think it might not be worth the effort?
If you come up with a working code, we can run it on Yoyo@home - provided you analyze the resulting data, of course.

Michael.

I have a working code, but it is not good for BOINC. Let me explain.

Not all algorithm can be readily run on BOINC. It needs to be able to run on parallel with minimal data-interdependency, i.e., it can be turned into a form that deals only with small compute range, and combining these ranges will give the whole result.

Unfortunately, the most powerful algorithm up to now does not satisfy this condition. It has to compute a huge hashtable using the whole range, and that defeats most of the attempt to parallelize it. There are algorithms that can be paralellize to give small enough workunits, but the gap of complexity is very large (at least an O(nlogn) factor to be precise). I have done a rough estimate. To check all the parameters up to 7000, using the most powerful algorithm, it can be done with 2 months' computing time on a server with 32 threads; to do the same with less powerful algorithm, it takes at least 7000 times the same computing time on the same machine, therefore at least 7000 such machine on BOINC, and due to the nature of the algorithms, this is only a sub-estimation.

We won't want to do something that can be done on one large server with much more computers. That would be a waste. We can do it in our own computer farm. If we learn something then time is not wasted. But anything put forward to the public needs to be efficient, not to waste.

[Michael H.W. Weber]

Then, why don't you run it on a double CPU system where each processor has 16 cores?

Michael.

P.S.: Hatte die Höllenmaschine von Thomas R nicht solch eine Konfiguration? Könnten wir im [hsmr] laufen lassen...

[fwjmath]

Then, why don't you run it on a double CPU system where each processor has 16 cores?

Michael.

Here comes the second reason: the mathematical one.

It is not difficult to check to 7000. Even if I don't have such a machine, I can rent one on Amazon EC2, and the whole check will only cost ~200 bucks (using spot instance). But I won't.

Why? Because I know my math and I have a hunch that it will not find any counter-example. I also asked a friend who studies something related (algebraic geometry and algebraic arithmetic, spiced with number theory), and he confirmed my thought.

Disclaimer: I am not an expert in algebraic number theory, nor my friend. But we both have been trained in mathematics and have had courses on algebraic number theory and related fields, and some knowledge of the subject matter. This is the best guess we have, but may differ from the point of view of experts in this field. So the following cannot be taken as a general consensus of experts concerning the conjecture.

There is a way we talk heuristically about problems. An "algebraic" problem is one that has its root in algebraic structures, thus rigid and hard to alter. An "analytical" one depends, in the opposite, on concrete value of a quantity, thus "softer" and easier to alter. This is not an "all-or-none" division. A problem can be "algebraic" but solved by analytical methods, or vice versa. It is just the nature of the problem itself, an algebraic problem is usually either outstraight false from small examples, or correct but difficult to prove, and an analytical problem can have its first counter-example at middle-to-high range, if it has one.

This conjecture, also named (in a more proper way) as Tijdeman?Zagier conjecture, is a natural extension of Fermat's last theorem. It is thus also deeply related to modular forms (or more generally automorphic forms) and elliptic curves. It is a type of "algebraic" problem depending on structures. Thus it is not really probable that it is false and we haven't found out up to 1000. There are plenty of papers out there proving it for special cases. For me it is very improbable that there is a counter example.

Furthermore, I think there are already number theorists who have done some verification. They have plenty of computational power, and are not timid at using them. I once talked to Helfgott who posted a complete proof of the weak Goldbach conjecture. He told me that the proof contains a chain of primes that he found using several weeks on a computer. It is difficult to imagine that, if the verification is anything useful, they have not done that. So either they have done that but found nothing, or it may simply be that they know/believe it is true, thus never bother to check.

Again, it is just a guess, but an educated guess. The contrary can happen and a counter-example may exist. But instead of doing this verification, maybe computing something else will be more fruitful.

[nico]

Thanks for your explanations fwjmath!