I have made my independent research available as a book on my website. Why is it not celebrated by the mathematics community? [closed]

Question

Some mathematicians said that general topology in general and theory of proximity spaces in particular are dead (meaning that no new discoveries appear in this field of mathematics).

I have discovered a theory which generalizes general topology in general and theory of proximity spaces in particular, opening a new major area of research.

It is described in this draft book.

So general topology "resurrected".

Where are the celebration and fireworks proclaiming: "General topology is alive!"?

I am an amateur mathematician and my speaking English (and also my purse to buy air tickets) is still not good enough to participate in scientific conferences.

I am not allowed to submit to either arXiv or nLab.

Something is wrong: There should be a celebration of general topology being alive, but this does not happen. What is wrong?

Well, one thing because which this does not happen is that I have not (yet) solved any specific open problem (not counting open problems which I myself formulated). But what else keeps the world off celebration?

---

My question is not a duplicate of Publishing vs. putting work online under a free license because at that question I ask about how citing (not acceptance in general) of my work may be influenced by its license and method of publication. Here I however ask about acceptance (not citing) of my work independently on its method of publication.

It is surely not a duplicate of I believe I have solved a famous open problem. How do I convince people in the field that I am not a crank?, because in this situation I have not solved a famous open problem.

It is not a duplicate of Creating a community around my research book, because in that question I ask what to do but in this question why does it happen. These are entirely different questions.

Answer 1

There should be a celebration of general topology being alive, but this does not happen. What is wrong?

The people who say general topology is dead are generally not unhappy about this conclusion: they feel it died a well-deserved death due to a lack of important connections with the rest of mathematics. (They are wrong, both about whether it in fact died and about its lack of connections, but these beliefs persist.) Your work does not challenge these beliefs, because it appears to be almost entirely self-contained, with minimal connections to other topics in mathematics. If someone considers the field dead, then they will view your book as a zombie, rather than a sign of life.

This doesn't mean you have to try to change their minds. It's perfectly reasonable to ignore them and focus on the mathematicians who do care about general topology. But those mathematicians won't be surprised to hear that the field they work in is still alive.

Well, one thing because which this does not happen is that I have not (yet) solved any specific open problem (not counting open problems which I myself formulated).

This is a major issue. There are two ways you can attract researchers to a new research area. You can show them how this area is connected to things they already care about, or you can convince them the new area is outstandingly interesting and important in its own right (more so than what they are currently working on). The former is far easier, while the latter ranges from difficult to impossible. If you can't build connections, then the chances of ever attracting much interest are low.

But what else keeps the world off celebration?

Celebration is not the default state. Every day, several hundred new mathematics papers are posted to the arXiv, some of them rather important. On a typical day, none of them will get a reaction that could reasonably be described as celebration. You should not expect it to happen here.

As a general rule, it can be difficult for authors to predict how their papers will be received. Your book is exactly the sort of thing you like. Maybe it's your favorite topic in the world, but that doesn't mean it will be everyone else's favorite too. This can be really frustrating. Some of my papers are much more popular and influential than others, and they aren't always the ones I'm most excited about or proud of. I sometimes wish I could say to people "Hey, if you think X is so great, why aren't you twice as excited about Y?" But ultimately people's tastes and preferences differ, and you need to make a case for your work in terms that other people understand and value. This is not easy, but it's the only way forward.

Answer 2

Here is a brand new mathematical theory I have invented just now (in the last 30 seconds):

A Gobleflump is a set together with a ternary operation Star(a,b,c), and a binary operation Spade(a,b) satisfying Star(Spade(a,b),Spade(c,d),Spade(e,f)) = Spade(Star(a,b,c),Star(d,e,f)).

I could now devote my life to the study of Gobleflumps. I could publish papers about extremely regular gobleflumps, and the equivalence between hyperconvex gobleflumps and hypoconvex grendleflops. This might all be legitimate, correct mathematics.

No one will ever care about my lifes work, or probably even read it, unless it makes some connection to existing mathematical theory, illuminates why something disconnected from the theory works the way it does, or solves some existing problem.

The reason is just that mathematics is a social activity. People work on things which are important to the group, and the things which are important to the group are determined (basically) by fads. There is no objective reason that human mathematics should be so concerned with polynomial equations over finite fields, except that some people found it interesting, and they convinced other people to find it interesting. Eventually people found these tools could be useful for solving their other problem in algebraic topology or data encryption.

My own work as a Ph.d. student was probably only really interesting to about 50 people on the planet, but might possibly be interesting to some more people in connected fields if I did the hard work of convincing them that it is useful to them.

If you care about the impact of your work, then I suggest working on mathematics which arises naturally in connection with the mathematics of other people. If you do not care about other people, then work on something which is not connected to what other people care about.

Answer 3

A good and fair question.

I took a brief look at your materials, and it seems like you introduce a host of new terminology and notation. It would take a tremendous effort for anyone to learn it. What is the payoff? Why should anyone take the trouble? I don't mean to cause offense, but these are questions that you must anticipate and be prepared to convincingly answer.

The classical way to motivate people to learn a new theory is to use it to solve an existing open problem, whose formulation does not require the new language you develop. Failing that, you could give sleek, elegant solutions of problems (again, whose formulation does not require your language) whose only known solutions are complicated and kludgy.

I recommend to you that you learn about the history of Alexander Grothendieck, his mathematics, and of the development of modern algebraic geometry (i.e., of scheme theory). Nowadays it is common for advanced graduate students to spend a lot of time learning his intricate language for describing what are, essentially, the solution sets to algebraic equations.

Why? If you refuse to take it for granted that this material is worthwhile, and instead learn the history of its development and its applications, I would guess that you would learn a lot about what it takes to get a new mathematical theory accepted.

Best of luck.

Answer 4

You need a reality check.

Is this really a breakthrough? Are your assumptions and development of your theory solid? Are the consequences far-reaching?

Reading posts of yours like Is a university that grants me a PhD for $1000 and a copy of my unpublished book fake? or http://www.mathematics21.org/algebraic-general-topology.html makes me believe that the need is real.

Also go through this list or this one. Both are valuable checklists.

Answer 5

Even famous establishment mathematicians run into trouble when their work starts to become inbred, creating lots of new concepts and terminology that is not connected to anything anyone else is doing. Mochizuki's work on the ABC conjecture and Poenaru's work on the Poincare conjecture are both good examples. Both have constructed intricate theories with very little connection to mathematics that other people are working on, and as a result, the mathematical community is largely ignoring them. It simply takes too much time and mental effort to slog through their work, without any guarantee of a payoff. It could be that after several months of study, you find a mistake. Then that's basically several months down the drain!

So if establishment researchers working on big important problems run into this issue, a relatively unknown researcher with an elaborate theory that doesn't actually solve any open problems is not going to have much of a chance!

My best advice is to begin more modestly by writing up some part of your work in a short research article with plenty of motivation in the introduction. "This is a new theory that resurrects general topology" is not sufficient motivation! Instead "We provide a simplified conceptual framework for understanding phenomenon X" would be better. Avoid making grandiose-sounding claims or sounding like you are bragging. After getting a short article on your ideas published you can start building from there.

Answer 6

First, echoing @Anonymous ' answer: people need motivation to learn something that is outside their usual world. Why should they? How will it help them?

Second, "acceptance" is in some ways a very weak thing. People may "accept it" but ignore it. It is not clear what reaction you expect. This reminds me of my contact with an angry amateur mathematician who expected to somehow be paid a stipend by the nearby university due to the theorems he'd proven... He was angry that I merely gave him advice about what journals to submit the article to (this was pre-internet), and didn't care at all that I told him he could mention that he was referred to them by me (as opposed to cold-call submission), and didn't care at all about my advice about the style of his write-up.

Stylistically, academic mathematics is very conservative, and any element of non-conformity in language is viewed as evidence of crack-pottery... although, obviously, it is only evidence of disconnection from the forces of orthodoxy. But/and if one's goal is acceptance by the (mostly orthodox... if only from fear of ostracism) majority, essential-conformity in style is very important. In particular, don't say that you "have a new theory" or that anything is "resurrected", and so on. Minimize new terminology, minimize new notation.

That is, yes, give the (possibly misleading) impression that what you propose is as-little-different from the status quo as possible... thereby getting peoples' confidence.

For that matter, building off established technology is vastly more sensible than trashing everything and starting over. It's really tough to give a convincing argument that everything we (=professional mathematicians) have is misguided and we should all change something...

In short: be persuasive to the human beings you want to persuade. They are both "human" and "expert"...