Andrej Bauer and Ronald Brown On Monads and Groupoids and Alexander Grothendieck on his idea for a Science Fiction Novel on Motives
These are from the June 2009 archive of the Categories mailing list at MTA, Canada: https://www.mta.ca/~cat-dist/
One is Andrej Bauer on convergent rewrite rules for monad theories
I thank eveyone who answered my question so quickly. For reference I
post a summary of the answers.
Bill Lawvere answered that "the theory of a monad is just that of
ordinal addition of 1 on the augmented simplicial category Delta
considered as a (non-commutative) monoidal category wrt ordinal
addition." A relevant reference in this regard is his "Ordinal Sums
and Equational Doctrines" which was part of the Zurich Triples Book,
available online as TAC Reprints 18.
Similarly, Jaap van Oosten pointed out that the free "monad on a
category" on one generator is the simplicial category \Delta (nonempty
finite ordinals and monotone functions).
It follows from these observations that the theory of a monad is decidable.
Todd Wilson kindly pointed me to a thesis by Wolfgang Gehrke, see
http://citeseerx.ist.psu.edu/viewdoc/summary?doi=10.1.1.47.7087,
which contains a complete set of rewrite rules (page 40, Proposition
20) for the theory of a monad:
id f ==> f
f id ==> f
(f g) h ==> f (g h)
eta* ==> id
f* eta ==> f
f* g* ==> (f* g)*
f* (eta g) ==> f g
f* (g* h) ==> (f* g)* h
The last two rules are extra, compared to the original equations. So
the next time you wonder whether an equation holds of a general monad,
just use the above rewrite rules on both sides of the equation.
With kind regards,
Andrej
I thought a document with a DOI would be easy to find on Google. Apparently not! Just try searching for it. All I got was the bibliographic data:
author = {Wolfgang Gehrke},
title = {{Decidability Results for Categorical Notions Related to Monads by Rewriting Techniques}},
language = {english},
year = {1995},
translation = {0},
school = {RISC, Johannes Kepler University Linz},
Another is from Ronnie Brown on Open Problems in Category Theory.
In reply to Hasse Riemann's question (see below):
I remember being asked this kind of question at a Topology conference in
Baku in 1987. It is worth discussing the background to this, as someone who
has never gone for a `famous problem', but found myself trying to develop
some mathematics to express some basic intuitions.
Saul Ulam remarked to me in 1964 at my first international conference
(Syracuse, Sicily) that a young person may feel the most ambitious thing to
do is to tackle a famous problem; but this may distract that person from
developing the mathematics most appropriate to them. It was interesting that
this remark came from someone as good as Ulam!
G.-C. Rota writes in `Indiscrete thoughts' (1997):
What can you prove with exterior algebra that you cannot prove without it?"
Whenever you hear this question raised about some new piece of mathematics,
be assured that you are likely to be in the presence of something important.
In my time, I have heard it repeated for random variables, Laurent Schwartz'
theory of distributions, ideles and Grothendieck's schemes, to mention only
a few. A proper retort might be: "You are right. There is nothing in
yesterday's mathematics that could not also be proved without it. Exterior
algebra is not meant to prove old facts, it is meant to disclose a new
world. Disclosing new worlds is as worthwhile a mathematical enterprise as
proving old conjectures. "
It is like the old military question: do you make a frontal attack; or find
a way of rendering the obstacle obsolete?
I was early seduced (see my first two papers) by the idea of looking for
questions satisfying 3 criteria:
1) no-one had previously asked it;
2) the question was technically easy to answer;
3) the answer was important.
Usually it has been 2) which failed!
Of course you do not find such questions where everyone is looking! It could
be interesting to investigate how such questions arise, perhaps by pushing a
point of view as far as it will go, or seeing a new analogy.
"If at first, the idea is not absurd, then there is no hope for it." Albert
Einstein
It could be interesting to investigate historically:
if (let us suppose) category theory has advanced without a fund of famous
open problems, how then has it advanced?
One aim of mathematics is understanding, making difficult things easy,
seeing why something is true. Thus improved exposition is an important part
of the progress of mathematics (even if this is ignored by Research
Assessment Exercises). R. Bott said to me (1958) that Grothendieck was
prepared to work very hard to make something tautological. By contrast, a
famous algebraic topologist replied to a question of mine about his graduate
text by asking: `Is the function not continuous?' He never gave me a proof!
And I never found it! (Actually the function was not well defined, but that
I could fix!)
Grothendieck wrote to me in 1982: `The introduction of the cipher 0 or the
group concept was general nonsense too, and mathematics was more or less
stagnating for thousands of years because nobody was around to take such
childish steps ...'. See also
http://www.bangor.ac.uk/~mas010/Grothendieck-speculation.html
The point I am trying to make is that the question on `open problems' raises
issues on the nature of, on professionalism in, and so on the methodology
of, mathematics. It is a good question to start with.
Hope that helps.
Ronnie Brown
That link is no longer live [fortunately it was archived by the Wayback Machine] This is the text:
Extract from letter 14, 14/06/83 from Alexander Grothendieck to Ronnie Brown
Your idea of writing a ``frantically speculative" article on groupoids seems to me a very good one. It is the kind of thing which has traditionally been lacking in mathematics since the very beginnings, I feel, which is one big drawback in comparison to all other sciences, as far as I know. Of course, no creative mathematician can afford not to ``speculate", namely to do more or less daring guesswork as an indispensable source of inspiration. The trouble is that, in obedience to a stern tradition, almost nothing of this appears in writing, and preciously little even in oral communication. The point is that the disrepute of ``speculation" or ``dream" is such, that even as a strictly private (not to say secret!) activity, it has a tendency to vegetate - much like the desire and drive of love and sex, in too repressive an environment. Despite the ``repression", in the one or two years before I unexpectedly was led to withdraw from the mathematical milieu and to stop publishing, it was more or less clear to me that, besides going on pushing ahead with foundational work in SGA and EGA, I was going to write a wholly science-fiction kind [of] book on ``motives'', which was then the most fascinating and mysterious mathematical being I had come to met so far. As my interests and my emphasis have somewhat shifted since, I doubt I am ever going to write this book - still less anyone else is going to, presumably. But whatever I am going to write in mathematics, I believe a major part of it will be ``speculation" or ``fiction", going hand in hand with painstaking, down-to-earth work to get hold of the right kind of notions and structures, to work out comprehensive pictures of still misty landscapes. The notes I am writing up lately are in this spirit, but in this case the landscape isn't so remote really, and the feeling is rather that, as for the specific program I have been out for is concerned, getting everything straight and clear shouldn't mean more than a few years work at most for someone who really feels like doing it, maybe less. But of course surprises are bound to turn up on one's way, and while starting with a few threads in hand, after a while they may have multiplied and become such a bunch that you cannot possibly grasp them all, let alone follow.
[The proposed article on groupoids finally became `From groups to groupoids: a brief survey', Bull LMS 19 (1987) 113-134. There is further speculation in the web article `Higher dimensional group theory'.
October 6, 2006]
See the Wikipedia page on Motives:
A commonly applied technique in mathematics is to study objects carrying a particular structure by introducing a category whose morphisms preserve this structure. Then one may ask when two given objects are isomorphic, and ask for a "particularly nice" representative in each isomorphism class. The classification of algebraic varieties, i.e. application of this idea in the case of algebraic varieties, is very difficult due to the highly non-linear structure of the objects. The relaxed question of studying varieties up to birational isomorphism has led to the field of birational geometry. Another way to handle the question is to attach to a given variety X an object of more linear nature, i.e. an object amenable to the techniques of linear algebra, for example a vector space. This "linearization" goes usually under the name of cohomology.
There are several important cohomology theories, which reflect different structural aspects of varieties. The (partly conjectural) theory of motives is an attempt to find a universal way to linearize algebraic varieties, i.e. motives are supposed to provide a cohomology theory that embodies all these particular cohomologies. For example, the genus of a smooth projective curve C which is an interesting invariant of the curve, is an integer, which can be read off the dimension of the first Betti cohomology group of C. So, the motive of the curve should contain the genus information. Of course, the genus is a rather coarse invariant, so the motive of C is more than just this number.
See https://sophiethemathmo.wordpress.com/.
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