Around 3.5 years ago, I asked a question about extensible automorphisms. The question was motivated by this simple, and weird consideration. I was looking at the proof that if H is a normal subgroup of G, then H is also normal in any intermediate subgroup K. This is really something obvious if you know the definitions, but I wasn’t satisfied. The core explanation, I felt, was the fact that any inner automorphism of the intermediate subgroup K extends to an inner automorphism of G.
This led me to the question: what automorphisms of a group have the property that they can be extended to automorphisms of any bigger group? I strongly suspected that the only such automorphisms are the inner automorphisms, but didn’t have the tools to prove this. The more I thought about it, the deeper the question seemed. In fact, it had interpretations and implications that could be couched in the language of model theory, category theory, and universal algebra. It wasn’t a terribly important thing to prove because its proof wouldn’t have important questions, but it seemed, in a way, a fairly fundamental problem.
The interesting thing about the way I came up with this problem is that, in general, it’s pretty different from the way a lot of research is done. Research is usually done incrementally and collaboratively: based on the new results, based on attempted ideas, on programs, on correspondences that need to be established. For instance, some of the big research in group theory these days involves getting some correspondences of various sorts between the representations of big groups, and small, local subgroups (subgroups that arise as normalizers of p-subgroups). This is a big theme, and new results are typically generated by looking at old results, and saying: okay, here’s a bit more in that direction. Similarly, proofs that attempt to get a better correspondence between Lie groups and Lie algebras, again work independently.
Even though the majority of mathematical research is of this kind, I believe that there is a lot of potential for just simple, stunning, and stupid ideas that can be raised by looking at the simplest and dumbest of results. And the beauty is that a lot of this can happen even without an in-depth knowledge of examples and advanced machinery. Alas, the questions cannot usually be answered without advanced machinery, but they can be asked.
Another important point is that usually, people seasoned in a field, have fairly strong views on what is the correct way to develop intuition in that field. Much of this is guided by the “example-oriented” thinking: to understand something, you need to look at, and work with, a lot of examples. Definitions on their own are worthless and misleading, we are often told. Working on the examples tells us what is really going on.
I strongly disagree with thinking of “examples” as a kind of oracle. Working with examples gives one kind of intuition: a very necessary and important intuition. But fiddling around with definitions gives another. Fiddling around using the ideas of logic gives another. Drawing pictures gives one intuition, pushing symbols gives another intuition, and fiddling with words gives yet another intuition. Definitions should not be degraded or delegated to second-order position, because the most interesting questions can often be asked just by staring at the definition.
The extensible automorphisms conjecture is an example of all these things. When I asked the question, I had practically zilch knowledge of representation theory, though most of the progress I’ve made on the problem (with inputs from many older, and more experienced, individuals) has been using ideas from linear representations and permutation representations. But at the time I asked the question, I wasn’t even motivated by a single example of a group. What I was motivated was by the sheer structure of simple proofs involving groups and normal subgroups.
So how did progress happen on the conjecture? The conjecture didn’t emerge from a solid understanding of groups, but efforts at solving it required a good understanding of groups. Based on ideas of Professor Ramanan, and based on long correspondence with Professor Isaacs and some email exchanges with Professor Alperin, I was able to come up with a proof that for finite groups, any such automorphism must send every element to its conjugacy class. This used the fundamental theorems of representation theory, in a fairly elementary way, along with some simple arguments about semidirect products. Independently, I proved that for a finite group, it must also send every subgroup to a conjugate subgroup. This was achieved by looking at permutation representations.
This highlights yet another interesting principle. If a problem is perceived independently and externally of a discipline, and yet can be solved (partly or completely) using fundamental results from the discipline, it proves the utility of the discipline. When Professor Ramanan first suggested fiddling with characters, I was stunned that something like linear representations could attack a basic group-theoretic problem. But after successfully implementing it in part, I was able to achieve a greater understanding and appreciation of the fundamental theorems of representation theory, from a perspective that didn’t require any knowledge of linear algebra.
Later, I learnt that linear representation theory also makes an unexpected appearance for proving results related to the hidden subgroup problem, and that it is the only way to prove some basic results in group theory including Burnside’s theorem stating that a group whose order has only two prime factors is solvable. In other words, representation theory comes up spontaneously for purely group-theoretic problems, and that happens for many reasons.
What I want to stress here is that for us to really understand how useful a discipline is, or what novel uses it can be put to, it’s important for people to keep asking questions that are apparently unrelated to anything at all, and then see what hammers need to be used to answer those questions.
The extensible automorphisms problem isn’t the only problem I’ve come up with. One, very closely related, problem is this. As mentioned earlier, if a subgroup is normal in the whole group, it’s also normal in any intermediate subgroup. But the same isn’t true for the notion of a characteristic subgroup. A subgroup that is characteristic in the whole group, need not be characteristic in the intermediate subgroups. So the question: what can we say about subgroups that we know can be made characteristic if we expand the bigger group? Clearly, they’re normal (because characteristic implies normal, and normality is preserved on going to intermediate subgroups). But can we say something stronger? If H is normal in G, can we always find a K containing G such that H is characteristic in G?
Once again, this seems a fairly hard problem, and one on which I’ve made hardly any progress. I don’t have too many ideas on where to start it. I do know of some strong relations with the problem of extensible automorphisms, but nothing that proves anything conclusively. Again, this is the kind of problem that doesn’t yet fit into a grand scheme of the subject of group theory. It’s an isolated problem that’s probably hard but isn’t getting a lot of attention because there’s no immediate payoff to solving it, either in terms of the machinery developed to solve it, or the consequences of its being true. But to me, it is important because it’ll help me understand exactly what the meanings of the words “normal” and “characteristic” are.
The problem with exploring both these questions, apart from the fact that they do not live in a broad scheme, is that exploring them basically requires looking at all the overgroups (or supergroups) of a given group. This is a challenging task, because — there are infinitely many groups containing a given group, and there isn’t even a nice way to start about it. But this problem also presents an opportunity, because it allows us to invert our thinking about a group. We usually think of a group in terms of what lives inside it. But now we’re concentrating on a group in terms of what groups it lives inside. My gut feeling is that perhaps trying to solve these problems will lead us to new tools to understand how to tackkle problems that “quantify over all overgroups”. With such tools at hand, people might be able to formulate and solve a lot more problems in group theory that currently seem beyond the possibility of stating.
To this end, let me mention a third cluster of ideas, one that is probably more achievable, and which I have been helping out with some experimentation using GAP, a computational package using group theory. Again, it stems from looking back at a simple proof, though this time, not an obvious or easy one. This is the proof that for a finite group, the Frattini subgroup is nilpotent. I looked at the proof, and then said: okay, what’s going on here? Can we replace Sylow by something weaker? I did exactly that: replaced it by the condition of being an automorph-conjugate subgroup — an idea that I’d been playing with for some time. And it turned out that the proof actually showed that Frattini subgroups of finite groups (and of a more general class of groups) satisfied a property in terms of these subgroups: any automorph-conjugate subgroup is characteristic.
This is again an overgroup search problem. If I give you a group G, and ask you: does G occur as a Frattini subgroup? Overgroup search would suggest that you need to look at all possible groups containing G. But that’d only be helpful if the answer were actually yes. What if the answer were no? In that case, we need to say something like if G were a Frattini subgroup, it would satisfy some property, which in fact it doesn’t. So, the fact that Frattini subgroups are nilpotent, tells us that we can reject G right away if it isn’t nilpotent. What I’d obtained was a more sophisticated condition that could even reject some nilpotent groups: a condition that was purely in terms of the subgroups, which is essentially a finite condition. I called groups satisfying this condition ACIC-groups.
Next, I started asking some questions: what are ACIC-groups? For finite groups, they live somewhere between Abelian and nilpotent. Any Abelian group is ACIC, any ACIC group is nilpotent. But where exactly do they live? Is a subgroup of an ACIC-group an ACIC-group? Apparently, no. Even a normal subgroup of an ACIC-group need not be ACIC. But a characteristic subgroup of an ACIC-group is ACIC: again, a purely formal argument that requires practically zero knowledge about the structure of groups.
What about quotients? A quotient of an ACIC-group need not be ACIC. But a quotient by a characteristic subgroup is ACIC. This suggests interesting things: starting with ACIC-groups, as long as we restrict ourselves to subgroup-defining functions and their respective quotients (like the center, commutator subgroup, etc.) we’ll remain in the ACIC-world. But as soon as we take an arbitrary subgroup, not “canonically” defined, then we could exit the world. So the ACIC-world enjoys a somewhat different kind of closure properties from the typical world.
Finally, what about direct factors? A direct product of ACIC-groups need not be ACIC, and direct factors of an ACIC-group need not be ACIC. However, if the groups have relatively prime orders, then both conclusions hold. That’s because the subgroups, as well as automorphisms, can be analyzed component-wise.
Finally, is the ACIC condition tight with respect to being realizable as a Frattini subgroup? The jury’s not out on that yet, but my strong suspicion, based on preliminary analysis on GAP, is that the answer is: far from it. My guess is that most ACIC-groups do not occur as Frattini subgroups, but I don’t have a stronger version that will narrow the gap.
The ACIC-problem is interesting as it combines the “overgroup” search that I was alluding to in earlier problems, with things that can be tested more tangibly. What it lacks is something to make it important enough for people to work on.
To summarize, I’ve mentioned three problems that I’ve come up with. All of them are noteworthy in that they come by looking at the structure of simple proofs and manipulating a few assumptions. They don’t use any of the deeper intuition into finite groups. All of them are noteworthy in the sense that, as of now, they don’t hold a promise for group theory. Solving any of these problems will not change the group theory world. They’re also noteworthy because the kind of tools needed to prove or establish the final results in these are likely to be completely different from the tools that were used to bring up the questions. But they all involve a challenge: the challenge of “overgroup search”. Thus, solving these problems, or developing approaches to solving similar problems, might allow people to start looking more aggressively “over” a group and at bigger groups, rather than the current trend of focusing on the structure of subgroups and automorphisms.
At the core: diversity matters. Diverse ways of coming up with problems. People looking at a subject from a purely formal angle. People looking at specific examples that they love. People looking at group theory as a special kind of universal algebra. People looking at group theory as a beautiful particular language in model theory. And we need that diversity, and we need to know that the most interesting questions can have answers from diametrically opposite fields. Much of research is, and should remain, incremental, and in the fashionable directions. But we also need that stream of new and freaky questions that come from totally new perspectives to keep determining the relevance and sturdiness of the stuff that’s already around.