David Hilbert Speaks
A focus on Hilbert’s famous speech, not on his problems
David Hilbert is the mathematician for whom Hilbert Spaces are named, as well as a huge number of other concepts and theorems. He has a type of hotel: Hilbert’s Hotel named after him too. Here is a very partial list of other things that are named for him:
- Hilbert’s irreducibility theorem
- Hilbert’s Nullstellensatz
- Hilbert’s Theorem 90
- Hilbert’s syzygy theorem
Today I wanted to look at the beginning of his famous speech on what became known as “Hilbert’s Problems.”
Many of his twenty-three problems—apparently a twenty-fourth has been found—have become famous, some like the “Tenth” are known by their number alone. The Tenth is the question, in modern terms: is there a decision procedure for deciding whether or not a polynomial equation
has a solution over the integers? The famous answer, of course, is no—this the work of Martin Davis, Yuri Matiyasevich, Hilary Putnam and Julia Robinson. I recently discussed the still open question: what happens if the values of the ‘s are allowed to range over the rationals.
I think the brilliance of Hilbert in selecting problems that still are interesting, problems that helped shape mathematics for over a hundred years, has overshadowed his wonderful insights about mathematics in general. It is his general insights that I want to discuss today.
Who of us would not be glad to lift the veil behind which the future lies hidden; to cast a glance at the next advances of our science and at the secrets of its development during future centuries? What particular goals will there be toward which the leading mathematical spirits of coming generations will strive? What new methods and new facts in the wide and rich field of mathematical thought will the new centuries disclose?
History teaches the continuity of the development of science. We know that every age has its own problems, which the following age either solves or casts aside as profitless and replaces by new ones. If we would obtain an idea of the probable development of mathematical knowledge in the immediate future, we must let the unsettled questions pass before our minds and look over the problems which the science of today sets and whose solution we expect from the future. To such a review of problems the present day, lying at the meeting of the centuries, seems to me well adapted. For the close of a great epoch not only invites us to look back into the past but also directs our thoughts to the unknown future.
The deep significance of certain problems for the advance of mathematical science in general and the important role which they play in the work of the individual investigator are not to be denied. As long as a branch of science offers an abundance of problems, so long is it alive; a lack of problems foreshadows extinction or the cessation of independent development. Just as every human undertaking pursues certain objects, so also mathematical research requires its problems. It is by the solution of problems that the investigator tests the temper of his steel; he finds new methods and new outlooks, and gains a wider and freer horizon.
It is difficult and often impossible to judge the value of a problem correctly in advance; for the final award depends upon the gain which science obtains from the problem. Nevertheless we can ask whether there are general criteria which mark a good mathematical problem. An old French mathematician said: “A mathematical theory is not to be considered complete until you have made it so clear that you can explain it to the first man whom you meet on the street.” This clearness and ease of comprehension, here insisted on for a mathematical theory, I should still more demand for a mathematical problem if it is to be perfect; for what is clear and easily comprehended attracts, the complicated repels us.
Moreover a mathematical problem should be difficult in order to entice us, yet not completely inaccessible, lest it mock at our efforts. It should be to us a guide post on the mazy paths to hidden truths, and ultimately a reminder of our pleasure in the successful solution.
I have read this a number of times, but cannot imagine having a speaker today start this way. I think there are several important ideas in his speech that I really like.
What makes an area important? He points out that what makes an area of mathematics less interesting is not the decision of someone or even a group. What can “kill” an area is the lack of new and exciting questions. Areas survive and thrive exactly when they have a multitude of interesting problems. There are many parts of theory I have discussed before that are no longer central, even though they once were. I hesitate to name one lest I hurt someone’s feelings. But certainly one example must be language theory. When I was a graduate student we learned many wonderful theorems about languages. Yet today I wonder how many know these old results? I do not think they are not important, but I believe that Hilbert would say that the area has lessened its output of problems, and thus has become less central.
What makes a theory well understood? He discusses a goal we should have in making theories “simple”: “A mathematical theory is not to be considered complete until you have made it so clear that you can explain it to the first man whom you meet on the street.” I sometimes wonder if we can even come close to that with any of the great ideas of theory. Can we explain the P=NP question in this way? Can we explain in this way any of the great results of theory? I wonder.
What makes a problem great? I always liked his notion of what makes a good problem: “for what is clear and easily comprehended attracts, the complicated repels us.” Questions that are simple to state are the best. This seems obvious, but I definitely have violated many times by working on complex problems. But I think the most important problems do satisfy Hilbert’s criterion.
There are some Hilbert problems that are still open, but most left are either not precise enough to really be solved or extremely technical. For example the sixth asks “Axiomatize all of physics.”
One more realistic problem for all of us is to ask do we agree with the ideas of Hilbert? Do you think his comments about mathematics still apply today? Do they also apply to complexity theory? What do you think?
Hilbert’s speech ends:
The organic unity of mathematics is inherent in the nature of this science, for mathematics is the foundation of all exact knowledge of natural phenomena. That it may completely fulfill this high mission, may the new century bring it gifted masters and many zealous and enthusiastic disciples!
Of course he was talking about the twenty century—yet his excitement seems to still apply and be relevant to this century.