It appears that in part the OP wants to know how to
do "original" mathematics. Well, to raise the bar a
little, the usual criteria for publication are new,
correct, and significant. So, the OP was asking
about "new", but likely he will also want to know
about "correct" and "significant". Okay.

My suggestion is to do applied math. How? There
is a famous recipe for rabbit stew that starts out,
"First catch a rabbit". Well, for applied math, we
could have a recipe that starts "First find an
application" or at least find a real problem that
needs a solution.

There is a broad range of how to use this recipe --
be in an applied department, e.g., business,
engineering, agriculture, medicine, and there get
the real problem to start. E.g., R. Bellman was in
engineering and medicine. Or, maybe better yet, be
in some such field in the real world, find your
problem, get at least at first-cut solution, then go
to graduate school in such an applied department and
use your work as your Ph.D. dissertation. I did
that.

Next, it turns out, if take what looks, first
glance, like a serious applied problem, or, really,
nearly any fairly new applied problem, and consider
this problem fairly carefully, say, try to find the
first good or a much better solution, then likely
can find a doable math problem to attack.

Automatic Presto! If for that serious/new applied
problem get a math result that is new and correct,
then the math can be viewed as "significant" due
partly to its being significant for the applied
problem.

"Correct"? Sure, as a means of being correct, do
the work with theorems and proofs. Compared with
what is available in other fields for being correct,
the theorems and proofs of math are a great
advantage.

Next, often you will find that existing math still
isn't quite or at all what you really need for the
applied problem and, thus, have to create some new
math, that, yes, will be guided by the applied
problem and get some of the significance of your
work from that problem. And at time can discover
mathematical questions that, maybe, are not
important for the applied problem but are
interesting as mathematics or have some promise for
other applications; so, starting with the applied
problem can provide an injection of secret
stimulant that can make clear several new
directions to pursue.

Also, since nearly everyone in academic STEM fields
or nearly everyone in academics has physics envy,
in particular, mathematical physics envy, in
nearly every field the work that is most respected
is that which mathematizes the field. So, do some
of that.

So, first get an application!

For tools, I would suggest a good background in
analysis, say, through Royden's Real Analysis
and/or the first half of Rudin's Real and Complex
Analysis. Also get a good background in
optimization. For a desert buffet of math,
especially the Hahn-Banach theorem, useful for
applications, take a pass through Luenberger,
Optimization by Vector Space Techniques. Then,
get a good background in stochastic processes. And
have some more, really, essentially anything and
everything in an ugrad math catalog.

You will find that in applied fields such as I
mentioned, nearly all the workers struggle terribly
with their math background -- they know that they
need much more math than they have, and you will
have a big advantage. Use it and, thus, do the
original math you want.

Do this in a department of pure mathematics? Maybe
some such department would like to have some
applications from outside the department and be
interested, but mostly not. But work in other
fields, especially some parts of engineering, has
long shown some really interesting and valuable
questions and results. E.g., the question P versus
NP is now taken as quite serious mathematics, but
heavily the question started with integer linear
programming in operations research. Some of the
work in linear programming and special cases of
linear programming on networks resulted in some
darned interesting questions with some nicely
non-obvious, original answers; in principle many of
the questions could have been pursued directly from
now classic work in linear algebra but were not and
apparently because the motivation was not
available or some significance was not clear. So,
there was interesting work by W. Cunningham, K.
Borgward, V. Klee and G. Minty, R. Bland, D.
Bertsekas, and more, and some of this work was done
outside departments of pure mathematics. Net, for
over 50 years there has been a big theme: Not all
the interesting, powerful, valuable, important
research in mathematics is done in departments of
pure mathematics.

Questions?