#### by Evelyn Lamb

Marty Scharlemann was born in 1948. He received his undergraduate degree from Princeton University in 1969 and his PhD from the University of California, Berkeley in 1974 under the supervision of Robion Kirby. He spent most of his career at the University of California, Santa Barbara, with visiting positions at several other institutions, including the Institute for Advanced Study (IAS), Institut des Hautes Études Scientifiques (IHES), University of Texas at Austin, Mathematical Sciences Research Institute (MSRI), and the Research Institute for Mathematical Sciences in Kyoto, Japan. His research has probed several areas of low-dimensional topology, including Heegaard splittings, knot theory, and three-manifolds.

The following is a condensed and edited version of the author’s conversation with Scharlemann in June 2020, about his collaborations with Abigail Thompson and Michael Freedman.

**Lamb:** *How did you start working with
Abigail Thompson?*

**Scharlemann:**
Rob Kirby
and
Ray Lickorish
organized these summer
meetings of topologists in Cambridge, England. And so on one of
these — and I’ve forgotten exactly the year1
— Bill Menasco,
who was also
a Kirby student, brought along a graduate student, Abby Thompson.2
I started talking to her there about knot theory, which we were both
interested in. She was working on her dissertation, mostly with Bill
Menasco. (Her thesis advisor,
Julius Shaneson,
was interested in other
areas.) At some point, we both ended up at the MSRI in Berkeley.3
Bill
was transferring over to SUNY Buffalo and worked with Abby for half
the year. Then I came and he asked me if I would work with her for the
next half because we were interested in many of the same things. And
so I did, and I think she finished her thesis basically there. I was
kind of her ad hoc advisor. She was interested in some of the
well-known and deep problems in knot theory, things like property P
and the behavior of knots with crossing changes and band sums. At the
end of the year at MSRI, she had the problem of whether to go to
Buffalo and work with Bill, or we were having a special year in
topology at UCSB: the topologists were allowed to hire all the
lectures for the department that year, with the hope that we would get
a good group together. And so she,
in fact, came to Santa Barbara.
(I’m sure that the difference between the weather in Santa Barbara and
Buffalo had nothing to do with her decision!)

Because we were interested in the same things, and she had lots of good ideas, we started writing papers together. Eventually, she ended up at UC Davis, which is a beautiful train ride from Santa Barbara.

**Lamb:** *Your first paper with her is called “Unknotting numbers, genus,
and companion tori”*
[1].
*What is that about?*

**Scharlemann:** I had become very interested in something called sutured
manifold theory that was developed by
Dave Gabai
[e5].
I wanted to do it
in a slightly different way, a more combinatorial way. Dave used
foliations, which didn’t strike me as being at the heart of things,
and it wasn’t an area I understood well. And so I ultimately was able
to do that. Abby had used some theorems in work she did before that
[e6],
taking some of the
output of sutured manifold theory to address problems in knot theory.
One of the ways that this enters in is in thinking about crossing
changes in knots or about band moves. Crossing changes are intuitive.
You just change your crossing. Band moves are a little bit more
exciting. You take a ribbon from one place in the knot or link and
connect it to another. And then you cut out the middle of the ribbon.

I think it was in the earlier paper that she realized that the theorems that Gabai was creating were very relevant to questions about band sums and crossing changes. And so that first paper was an exploration of that topic, how to use sutured manifold theorems to say things about crossings and band sums.

**Lamb:** *I saw that solving the graph planarity problem*
[2]
*seems to be one of the most important problems from your collaboration. Can you tell me about that?*

**Scharlemann:** That came late in our collaboration, but it was one of
the most pleasing [projects] because you can explain to anyone what
the problem is. You’re given a graph in three-space: vertices and arcs
connecting them. And you ask the question “Can you move it, in
three-space, so that it lies on a plane?” There are two aspects of
that. One is the graph problem, which was solved by
Kuratowski
[e1]:
a graph cannot be put in a plane, even
abstractly, if and only if it contains one of exactly two
configurations. But beyond that, then you ask, “Well, once we know
that the graph itself can be embedded, can it be moved to the plane in
three-space?” And that’s what we were addressing.

The simplest example of that might be just the graph consisting of a single vertex and a single edge, a loop. Of course, that is a planar graph: you just put it in a plane. But it could start out in three-space embedded as a knot. So then it becomes the problem: how do you decide whether, or can you decide whether, a knot in three-space is unknotted, that it can be put in the plane? Well, that was solved by Papakyriakopoulos in the 1950s [e2]. And so our theorem could be viewed as an extension of that work, as well. It was a lot of fun. We fairly soon found an idea that seemed very promising via an inductive step, but it only worked on fairly large graphs. So there was a general idea, but then much of the work came in handling the smaller graphs as we got closer and closer to the smallest interesting one, which would be the Papakyriakopoulos result. Eventually we got it, and we were very pleased with it.

One of the stories associated with that is there was actually a bet between two knot experts, Cameron Gordon and Jon Simon, who proposed the problem. It was his conjecture that we proved. They bet \$20 on whether it would ever be solved. Cameron believed it would never be solved, and Jon bet against that because he was trying to encourage people to do it. I think that Jon Simon eventually collected his debt, but you’d have to ask him that.

**Lamb:** *So I guess that wasn’t a bet that actually remunerated the people who solved it.*

**Scharlemann:** Yeah, where’s our cut?

**Lamb:** *This might be showing my naïveté, but looking through
your publications, I see a lot that I would naturally think of as
being topology, but I would have thought of graph planarity as being
more in the graph theory/combinatorics world. So how is this connected
to what we might think of as classic low-dimensional topology?*

**Scharlemann:** There is a way of looking at the structure of
three-manifolds called Heegaard splittings, in which you start with
what’s called a handlebody. A handlebody looks roughly like a
thickened-up bouquet of circles. And it’s an elementary theorem,
probably going back to the 19th century, that any closed, compact
three-manifold can be written as the union of two such things along
their boundary.

One way of thinking about a handlebody is by thinking of a neighborhood of a graph. Take any finite graph, put it in three-space, and thicken that up. If you suppose the graph lies in a plane and you thicken it up, and then you ask, “What does the rest of three-space look like?” it doesn’t take long before you discover, well, that’s also the neighborhood of a graph. And so you’ve described in that way an actual Heegaard splitting of the three-sphere. One part is the handlebody lying near the plane, the other is its complement. A kind of fundamental theorem of Heegaard splittings, due to Waldhausen [e3], is that for the three-sphere, that’s it: any Heegaard splitting of the three-sphere looks like that. So one upshot of that theorem, if you try and think about it in terms of graphs in three-space, is that if you have a graph sitting in three-space, and you know that its complement also looks like a thickened-up graph, then you have a Heegaard splitting of the three-space. Waldhausen tells you that you can take this graph sitting in three-space, and if its complement is right, then you can slide it around, edges over edges and all that sort of thing, until finally it becomes a nice planar graph sitting in the plane. What Jon Simon asked was, “What if you don’t allow yourself to slide edges over edges?” If you just leave it as a graph, it’s obviously a more difficult question, and so then the conjecture was if you know that every subgraph can be put in the plane, and you know that the complement is right per Waldhausen’s theorem, and every subgraph of the original graph has the property that it can be put into a plane — then you can put the graph in the plane. So there are all these connections to Heegaard theory, which Abby and I were quite interested in at the time. We worked quite a bit on those kinds of issues — Heegaard theory and knot theory. Both of those come together in that kind of question.

**Lamb:** *In your collaboration with Thompson, did you feel like there was
an arc, one big thing you were trying to push to, or did you feel like
you were always finding new problems to work on and just kept
meandering?*

**Scharlemann:** I would say it’s more of the latter. We had techniques
and were thinking about problems where they might be applicable. For
example, this graph planarity thing. If my memory is correct, at first
we started thinking about ways we might apply sutured manifold theory
to that setting. In the end, it wasn’t necessary. That theorem could
have been proven without sutured manifold theory, and that’s the way
we ended up doing it. So it could have been proven decades ago. I
don’t think there was anything remarkably modern about the tools we
ended up using. It was just putting them together right.

**Lamb:** *How did you work together in this collaboration — what kind of
give and take did you have, how did you bounce ideas off of each
other?*

**Scharlemann:** I think of her as the architect, and I was the plumber.
She had these ideas; some of them struck me as completely off the
wall, and some of them seemed like they could probably work. (There
seemed to be no connection between my initial impression and how
things turned out.) But I have to confess I get really excited about
the technical details of arguments and trying to figure out exactly
how to nail things down, and she’s more of the idea person. So we kind
of worked in that way: she would pitch ideas, and I would try and
figure out whether there was an approach from, say, sutured manifold
theory. Our roles switched back and forth, but I would say
predominantly it was like that.

We had a lot of luck. We got a lot of stuff done, and I was delighted at how easily it worked. It seemed like most things we started thinking about went somewhere, and somewhere interesting.

**Lamb:** *That is lucky!*

**Scharlemann:** As I’m sure you know, 99 percent of the things you try in
mathematics don’t work, and somehow you don’t get credit for all those
great ideas that don’t work!

**Lamb:** *Right. It seems very unfair. Glancing through your publication
list, there’s a mix of single-author papers and things that you’ve
written with collaborators. How do you feel like the roles of
collaboration and working by yourself have worked in your career?*

**Scharlemann:** I am probably more of a solitary worker than is the norm
now, though I think when I started my career it was more of a norm to
work on your own. I like to think intensively in ways that I often
have a very hard time explaining to people. In particular, I can’t
draw, and this is a real drawback if you’re a topologist. I can see
pictures perfectly in my head, but I can’t draw, and that makes
communication difficult. But one of the nice things about
collaborating with Abby was that she could draw. That’s kind of a
stupid comment, but she also had a way of reining me in when I started
boring deeper than was necessary for a given problem, kind of bringing
me back to reality and saying, “Why don’t we try this instead?” It
often seemed that I was enjoying thinking hard about problems in ways
that turned out not to be very productive. She was very helpful in
getting me back on track. And she had lots of ideas that would never
have occurred to me, and then I would get excited about exactly how to
make those ideas concrete. A lot of that was solitary work, but we
would return and start talking about things, and it often worked out.
I definitely get a lot of enjoyment in just thinking about things
hard, walking around and thinking about them. So I probably am not as
collaborative as many.

**Lamb:** *And how did you start working with Michael Freedman?*

**Scharlemann:** I ran into him in his first job, which was at Berkeley.
He arrived my final year in graduate school. We were both interested
in four-manifold stuff. I followed with great interest what he was
doing, but we didn’t collaborate at that time. The papers I’ve written
with him have been from the past five years. But we talked a lot in
the in the 1980s. Over the years, I would see him at conferences, and
we’d sometimes have conversations about four-manifolds. Freedman is
interested in all kinds of stuff, and he remembers it very well, too.
So my overlap with him became narrower and narrower in terms of his
broadening interests. I don’t know if we even ever came close to
working on a paper together [earlier in our careers]. We would bounce
ideas off each other, but it never went anywhere, though I learned a
lot and I hope he learned some.

As to our recent collaboration, he became very interested in physics and in quantum theory, quantum topology, et cetera, which I never really warmed to. At some glorious moment, he ended up in Santa Barbara, not as a mathematician in the math department, but connected to the Microsoft quantum computing lab. I kind of smile at that because it took way, way too long for us to be able to get things set up so that Mike could be associated with the department. But now he’s nominally a member of the UCSB Mathematics Department. So we were geographically in the same place, and we talked every once in a while about stuff. You know, I have to say, sitting in my office working on these problems, I’d feel a little bit like a mole underground, and then Mike would walk in, and he’d have all these ideas, and it was like the sun suddenly shining into my tunnel. And it was it was kind of fun.

But there was a question called the Powell conjecture. Maybe five or six years ago, Mike got very interested in this conjecture because he saw it as connected to four-manifold theory. The question that was involved there was a kind of analog to questions about braid theory in three-manifold theory. He thought it could be quite important in four-manifold theory, and so we started talking about that. He sent me over a sketch of a way he thought that you might be able to prove it. I was in the process of sending back an email explaining to him why I didn’t think that approach could possibly work when I started thinking, “Wait a minute! Maybe it could.” And so that’s what launched it. Over the years I think we’re getting fairly close to something that looks like proof. It’s still unclear whether it’s going to all work out, but along the way, we’ve proved some nice stuff that gave rise to the papers you can see. Other stuff is in the 99 percent that didn’t work, and so there’s kind of no record of that. But it’s an ongoing project.

There’s an interesting background story to the Powell conjecture.
Jerome Powell — not the chair of the Federal Reserve, but someone with
the same name — was a student of
Joan Birman
in the early 1980s and
proved a nice theorem for his thesis
[e4].
I mentioned Waldhausen’s theorem about how Heegaard splittings of
__\( S^3 \)__ look, but you can ask a sort of second-order moving picture
question. Given that you have a Heegaard splitting of __\( S^3 \)__, as
Waldhausen described, suppose you just sort of throw it up in space,
and then it comes back down and lands in the same place, but maybe
it’s moved around or changed during that process. And the question is,
are there simple moves that generate all possibilities of how this
handlebody could move in space to return exactly to itself? Powell
proved that five particular moves suffice. Many years later, I’d been
thinking about it, and one of the techniques that had worked very well
in a lot of settings, and in particular with my collaboration with
Abby Thompson, was the notion of thin position. She proved a really
important theorem in three-manifolds, the recognition problem for the
three-sphere, using thin position
[e7].
And I thought, “Well, it’d be nice to come up with a modern proof of
Powell’s theorem that would use thin position.” It would certainly be
easier. But I couldn’t figure out how to do it. I would get stuck at a
certain point, and I finally decided to “cheat” and read Powell to
see how he handled this situation. (I hadn’t really read his paper
carefully; I just knew the result.) And I discovered there was
actually a gap, that he had missed something. There seemed to be no
way to proceed, and no one knew how to fix it. I spent a lot of time
trying to fix it using thin position, but I still couldn’t do it.

Years later, Mike got interested in the problem for the reasons I’ve described, and remembered that I had been interested in it for a while, so that’s why he contacted me. He asked what I thought of his idea. And it’s a terrific idea, but it just isn’t quite enough. And we haven’t quite been able to work it out.

**Lamb:** *Are all your papers with Freedman related to Powell’s conjecture?*

**Scharlemann:** They’re all related to the train of thought initiated
there. One paper is a discussion of Mike’s big idea of how Powell’s
conjecture might be solvable
[3].
It was known to be true for genus two Heegaard splittings. (That goes
back to the 1930s.) And one of our concrete results there was that the
Powell conjecture is also true in genus three. It’s not a big thing,
but it was at least a concrete result. We haven’t submitted that paper
for publication anywhere yet. We view it as more of a discussion
document. The hope is that we’ll figure out some way to have a happy
conclusion to it, but at the moment, it’s not a satisfactory paper.

At some point we worked on the Dehn’s lemma paper [4]. It was Mike’s idea that this might be true, and he really pushed it through. When I first met him back in the 1970s, he was an expert on Dehn’s lemma and just knew it in and out. He realized there was a somewhat stronger statement you could make, and that just floored me. It’s such an old and honorable theorem. That there’s a way of making it even stronger after all this time really surprised me.

The paper that comes next on my vita is called “A strong Haken’s Theorem” [5], which solved a problem that goes back to the 1960s. The argument, together with ideas that came out of Freedman’s original ideas for the Powell conjecture, were what led then to the second collaborative paper with Mike Freedman, “Uniqueness in Haken’s Theorem” [6]. It’s a weird coincidence that the upgrade of Dehn’s lemma was exactly the tool that was needed to make the Strong Haken Theorem work.

**Lamb:** *Do you feel like the style of your collaboration with Freedman is similar to your collaboration with Thompson?*

**Scharlemann:** There are similarities, but somehow [working with
Freedman] was always a bit more formal than working with Abby. Part of
that probably has to do with the fact that I was her advisor, so I
kind of felt like the senior figure, whereas it’s clear when I work
with Mike that he knows several orders of magnitude more than I do.
But I would say in both cases, the collaboration is pretty
comfortable. And I have to say I am — maybe I shouldn’t be, but I
am — concerned about wasting his time because he’s doing so much in so
many different fields. I don’t want to call him up and say, “I just
want to talk about this.” I feel like I have to have something to
say.

**Lamb:** *How do you feel looking back on what you’ve managed to do in this field? Are there still big problems that motivate you?*

**Scharlemann:** Oh, I really like big problems. But I go towards them
with the attitude that I don’t necessarily expect to solve them. I
would like to understand them, and that often gives rise to other
theorems that I end up finding really interesting and can solve. I’ll
mention the Schoenflies conjecture as an example. It is just a
beautiful problem, and thinking about it, trying to figure out how you
might try various approaches, has been really productive for my
thinking. I also like tools that I understand that are visual. I get
interested in how I can use them to try and view different problems.
Sutured manifold theory is an example. When I learned about that, it
seemed like it was kind of on the borderline of something I might be
able to understand if I worked really hard. And that worked out. I did
finally understand it enough to use it in original ways. Thin position
is another example. A lot of the stuff that Abby and I did was a
combination of those two tools. I started out on this Powell
conjecture with exactly that in mind. I didn’t think the question
itself was particularly interesting, but I enjoyed trying to think
about how this new tool of thin position might be applicable to
Powell’s theorem. Well, it went in totally different direction when it
turns out that the theorem hadn’t been proven, and I’ve spent a lot of
time working on that. It’s not a Schoenflies conjecture level problem,
but it’s a very interesting problem. And it has led to nice papers: a
strong Haken theorem paper with Mike — well, both of the papers
are on an attempt to solve the Powell conjecture, and the Dehn’s lemma
came out of that. So even though we haven’t solved the problem yet, I
think we’ve done a lot of nice mathematics.

No one has ever asked me that question before and I’ve just made that up in the last five minutes, but I think it’s pretty accurate. I get excited by big problems that I can understand, and I get excited about new tools that I can use.

**Lamb:** *I’ve heard other mathematicians say they got a lot of mileage
out of knowing how to use one particular tool or argument. It sounds
like that’s sort of been your experience, to some extent: “I know how
to do this, so let’s see if it will work.”*

**Scharlemann:** I think part of the thing that’s interesting in
mathematics is how different people can be, and still be successful. I
think there are quite a few mathematicians for whom what I’ve
described wouldn’t be a natural way of thinking about things. That’s
one of the exciting things about working in it for so long, is seeing
such a variety of personality types and approaches to mathematics, and
seeing that they can all be successful in different ways.

*Evelyn Lamb
is a freelance math and
science writer based in Salt Lake City, Utah. She holds a Ph.D. in mathematics* (*Rice University, 2012*) *and has
written for such national publications as Scientific American, Quanta
Magazine, Slate, Science News and Nautilus.*