research about smarandache some days ago, I was discussing about topic i'll use on my undergraduate theses with my lecturer. At some point, she said to me that Smarandache (we talked about the Smarandache near ring) is no more developed, and there is no more research about it. In my last question, there was a bit interesting relation between ring, near ring, and smarandache ring (near ring). Despite there was the relation, why there is no large research about smarandache (near ring), contrary with near ring, there are much research based on near ring. What makes researchers and mathematician not to dive more in it?
 A: TL;DR
In short, I think it is a problem of poor reputation. I think your advisor's advice is probably a polite version of that.
Below, let's cover how you might form your own opinion on a subject like this.
Disclaimer
And before I go on, let me say that I don't know Smarandache or anyone who writes papers mentioning that name, and I don't want the following to come off as something personal.  I am only giving what I think are objective comments about evaluation of mathematical literature in general.
Whatever names or subjects your checks might turn up for you, I am not judging any of them. I'm sure they are all very nice people, we all have our deadlines and priorities, and we can all study and write what we want. 
I'd simply like to outline a list of red flags to look out for when evaluating research quality.  This list should hopefully help inform people and help prevent them from becoming associated with bad practices, or a misadventure in which one becomes disappointed with the field they committed to. 
Life would be simpler in science if we could prevent undesirable research from ever appearing, but it seems that is intractable. The alternative is to hone one's ability to discern good from bad, and that's the best we can do. It's a healthy exercise to engage in no matter how you look at it!
Red flags
Objectively, when evaluating something like this, you should do a search of the literature, and watch out for red flags like these:


*

*fewer than a handful of people have written much about it

*The idea seems like a trivial refinement of a well-established idea, or else it seems like an unmotivated generalization of a well-established idea

*There are an enormous number of publications by the people from #1. Sometimes the publications seem to be really grasping for attention by alluding to other scientific fields.

*It looks like possibly the originator (or else an associate) might have named it for his/herself.

*It looks like an entire journal or publishing company has been set up to distribute things about the topic, often by the originator or associates.

*There is a pattern of too much invention of terminology and concepts

*Bibliographies with mostly self-citation or citation of the aforementioned colleagues. 


What do these red flags suggest? In my experience, they correlate with poor quality of research.  Researchers should not try to mimic the style or practices that would throw up these red flags.

None of the points above in isolation are guarantees that some academic subject is bad, but when they crop up together, it can be telling.
(2)+(3) are relatively reliable red flags. This is a huge problem in abstract subjects where authors essentially farm papers to try to get an impressive publication list. One tactic they use is to invent a field, or such a field invented by someone like themselves, and then reprove all the results from well-established fields which hold more-or-less trivially for their invented field. While this seems rather detestable, it is also somewhat understandable considering the incentives that modern academia places on professors at universities.
For (4), concepts which earn eponymous names are usually named long after their success in literature is established. Authors using tactics like those in (2)+(3) try to stand this on its head and make it appear as if a concept is important because it is named for a person.
(5) is usually a sign that the authors have been rejected from existing journals, and basically need a workaround for the lack of interest in the topic.
How to get started
Here's probably the first thing you should do in a case like this:
google:Florentin Smarandache
The top three hits (for me) seem like they would be helpful in evaluating the field based on the red flags above.
For me, the first hit is a link to a webpage called Smarandache notions Journal.
The second hit is a google scholar listing of citations and co-authors.
The third hit is a
reddit thread.
If the only research that exists in a field is of poor quality, then it should be a major factor in a decision about pursuing the field.
On the other hand, if you see some huge promise in an obscure field and you can do a lot to improve it with high-quality research... you should!
