I believe I have a clever idea/tool that should be widely adopted by the research community. How to interpret a lukewarm response?

Question

Related to this question, except I do not believe (and have not claimed) that I have solved an open problem, famous or otherwise.

I came up with an idea (specifically, how to pronounce numbers in bases that are a power of two) that I think is useful for the research community, for educators, and in recreational math.

I have seen it mostly ignored and poorly understood. Occasionally it has been ridiculed and called 'pure crankery', 'Doctor Seuss names', 'pure bullsh*t' without the asterisk, downvoted, and even in a some rare cases deleted on internet answers sites. But about three (out of about a hundred) maths and computer professors have said it is 'valid', 'very clever, or 'works to some extent' (all on Quora).

How do I interpret this? How to find out whether I am a crank? I am not aiming to convince others that I am not a crank because only others can judge whether I am a crank or not. I don't want to convince people that I am not a crank if I actually am one, because that would mean I would be more likely to stay deluded, if I am deluded.

How should I respond to those that refuse to discuss the idea on the ground that it is crankery? What are they thinking?

Answer 1

A lukewarm response would mean that either the idea is not interesting or useful to the intended audience. You should try to judge whether the idea is intrinsically interesting (the question certainly indicates that you feel so) and whether you are approaching an appropriate audience using an appropriate medium.

It certainly seems that you are pushing the idea too hard when you face a lot of indifference and still continue to reach out to individual professors. It is evident that they aren't interested in discussing it, and you should respect that. Maybe the proposed method has value in a different setting. Not every tool that is/could be useful to a researcher is published in scientific literature or discussed on academic fora. Seek out other media, gauge interest and try to identify if there is a group that is interested in/benefits from the idea as you envisage them to.

If you don't find such a group, record the method somewhere, preferably on an open platform and simply leave it until somebody that finds it useful comes along. If the idea is ahead of its time, then you should wait for somebody visionary enough to come across it. If you feel that the idea can do with more refinement, keep working at it and then try exhibiting it once you find significant improvement. Or if you feel it can be monetized and are interested in that, explore intellectual property options.

The bottomline is, irrespective of the true worth of an idea, it is counter-productive to force people to take note of it.

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EDIT: Since articles related to the idea/tool have recently been shared by the OP, I am adding a few thoughts specific to the present situation. I hope that these will help clarify the difference between a research submission and an invention.

At the outset, the idea is (to me) clever, of possible interest to hobbyists and recreational number crunchers, and may have some potential contributions to specific fields (linguistics). There is no indication of crankery. As such, a case may be made that this idea (once established as novel) could be converted into a research submission. To make this case, the following crucial points would need to be addressed:

1. Identification of a target group/domain which would be benefitted by this work.
2. A clear and emphatic justification of why there is a need to undertake this effort. Presently, this is lacking. There must be a concrete use-case or demonstration of value, beyond a general statement of it being interesting or 'worth exploring'. Without this, the academic reader would conclude that insufficient background study and thought has gone into this idea. The onus of establishing worth through objective arguments lies on the author of the idea, not on the reader.
3. A discussion of why this has not been addressed so far (i.e. did nobody think of it or was it not worth the effort), and the related work that has already been done in the field. This may indeed require access to some academic literature, but is necessary. Hopefully OP has found some useful references in the linked answers.
4. A clear statement of what benefit the proposed tool gives. Is it to make teaching easy (in that case, look for a pedagogical audience)? Is it to enhance linguistic/numerical abilities (look for a linguistic audience)? It is going to make some computational process more efficient or unambiguous (go to computer scientists)? Is it going to add to how we deal with number systems (seek out mathematicians)?
5. Related to 4., demonstrate (ideally quantitatively) that the tool achieves this objective in comparison to the existing procedure, and therefore is worth consideration.

If these can be addressed, the response from academicians may be warmer. Personally, I think the blog format is well-suited and is quite engaging for these ideas.

Answer 2

If I draw a drawing on a piece of paper and show it to some friends, that won’t make me a crank despite the fact that I have zero talent in drawing. But if I start claiming my drawing is an important work and should be published or sold or talked about, then I am a crank. The difference is in having a realistic view of the significance of what you’ve done.

Your idea is “valid” and can be reasonably described as “clever”. It is a cute idea, in the same way that I thought it was cute one day many years ago when I discovered I can count all the way to 1023 using my fingers instead of 10 if I make use of binary representations. But your idea is not an idea in math — maybe in math education or in the general area (that doesn’t have a proper name because there is little need for one) of math terminology/notation. And, like my idea at the time, it solves a problem that I don’t think is a real problem anybody has: there just aren’t enough people with a need to extensively communicate numbers in base two by reading them out loud.

What does it mean when on the Internet most academics ignore your idea, and a few say you are a crank and a few say your idea is valid?

It means your idea is technically valid but not as interesting as you think it is.

How do should I respond to those that refuse to discuss the idea on the ground that it is crankery?

You should not respond in any way but leave those people in peace. People have no obligation to discuss your idea, and if they don’t want to discuss it then it means they don’t think it is interesting enough to discuss. Find someone else who does, or find a better idea that people will be more impressed by.

Answer 3

In my opinion, "Dr. Seuss names" and other epithets you get don't contradict statements like "it's valid" or "clever". If I understand your idea correctly, you basically propose to introduce alternative number names, such as "shi" for what I'd pronounce as "sixty-four", which provides some potential benefits.

Academics would ignore this proposal because it's simply outside the domain of academic research. For me, introducing "shi" as an alternative for "sixty-four" is like proposing Dvorak (or other alternative) keyboard layout instead of the usual QWERTY.

You can do it, and you can argue why it is superior in your opinion, but what kind of response do you expect? Some people would like your idea, others would not. I personally can't force myself to use "kibibytes" and "mebibytes" even though they are kind of established.

Even if you manage to prove that your method is "better" according to some well-defined criterion, I think it is still mostly a political and cultural matter, and should be treated as such, rather than a part of an academic discourse.

Answer 4

The main question to ask is: why should anyone care?

Naming conventions are a dime a dozen. It's not like they need to be nonsense, not at all. Every computer library developed from scratch comes up with naming conventions, usage conventions, interface conventions, etc. But precisely because such conventions are quite freely choosable, it creates a cost to use them consistently and this will not happen if there is not a very tangible benefit.

If I have a software library with very extensive, say, parallelization support, then it may make sense to learn the conventions that it imposes on the user. Maybe it even finds a way of expressing things more cleverly than existing models and if that happens, it may ultimately take on. Still, this can take a very long time. Many clever programming paradigms from languages such as Lisp or Haskell took decades to seep into the mainstream. Mind you, these are operational advantages that they confer and yet it was not easily accepted.

Introducing a notation/expressive language that does not fill an obvious niche or confer a distinct advantage is mostly a futile exercise and rarely takes off, independent of its rationality. Perhaps the most interesting such experiment is Esperanto, which is, comparatively spoken, a modest success.

So, your idea may be rational (I cannot judge if it is), it may be even modestly useful (I have no opinion on that), but to get many people to adopt it or even just take it seriously, it needs to provide very tangible and substantial benefits and even then its success may still be decades off.

Unlike a mathematical theorem where there may be few people able to judge its merits or proof, but where there is at least a kind of "objective" importance to the question and reality check to the proof, naming jugglery is often close to crankery in the sense that many self-styled physics "revolutionaries" simply clothe either trivialities or non-committal vague statements with verbal jiu-jitsu which makes them capable of "proving anything" and impossible to falsify. I guess that your idea is also a name game is what may induce some of your critics to consider your idea close to crankery.

Again, I personally do not have an opinion about that, but it's clearly not an idea many people consider important to discuss or advances their own understanding of things.

The fact that 3 out of a hundred profs have stated something positive about your idea, may give some indication that you are trying to cram the idea into a hundred people's throats. Is it really such an important idea? I mean, it's not solving world hunger, cancer or even just determining the nature of Dark Matter or the Hubble constant.

It begins and ends with the one question I mentioned at the beginning: Why should anyone care?

Answer 5

Terry Tao might suggest that you be skeptical of your own work. In order to produce great ideas, you need to put bad, average, and good ideas through many phases of refinement. If you do not view your own work critically, you might not identify necessary changes.

It is my personal opinion that your idea is not a mathematical idea (or at least, not an interesting one); based on the responses you have received from others, it seems like I am not alone in this opinion. It may be an idea about a topic relevant to math, but it does not provide any insight into the sort of questions that math aims to study. If you view your work skeptically, you may come to the same conclusion as me.

However, this is not to say that your idea is not interesting whatsoever. Suppose I were reading a science fiction book with a civilization that used binary as their customary number system. If one of these creatures said the word "tinmirlish" for 2^123456, I would be intrigued. If I then went and read your naming system, I would be floored by how creative and interesting it is -- changing vowels to express negation and inversion?? Awesome!

Upshot: Maybe the real issue you are facing is how to categorize your idea. I don't think your idea is interesting mathematically, but I think it is very interesting as a world-building concept. Perhaps other people find it interesting in some scopes and uninteresting in others. If you want to convince someone that your idea is interesting, try presenting it in a context that best fits the idea.

Answer 6

In answer to the 'How to find out whether I am a crank?' sub-question, you could try surveying the (especially peer-reviewed) literature in the same area to see whether there are any easily-discoverable objections to your ideas, or alternatives to your proposal, with which your articles have failed to engage. For example, given the IEC definition of "kibi", isn't it rather unfortunate that your proposal uses "ki" for $2^7$, rather than reserving it for $2^{10}$? And what makes your proposal better than that of Stern (1958, Science 128(3324):594-596), or that of McFeely (1959, Math. Teach. 52(5):356-357)?

You could also check the text of your articles for potentially-controversial assertions that are presented without a citation or other supporting evidence (For example, 'In schools and universities around the world, students are often invited or required to do arithmetic in base two, and/or in base eight. The students are often explicitly asked to compare base two or base eight with base ten' sounds far from obviously-true to me.)

Answer 7

First of all, find out if you are not even wrong. From your description of your proposal, it does not seem to be a falsifiable statement.