How do people in academia know whether their research, result, theorem or thesis is original work?
I think that to answer this effectively, one needs to carefully distinguish between two concepts that are often conflated in discussing research: originality and significance.  The originality of a piece of work is the degree to which it is distinguished from other pieces of work, while the significance of a piece of work is the intellectual impact that it has.

I think that these two tend to get tangled up because what typically concerns us is significance, but significance can only actually be measured in retrospect.  Originality thus gets used as a proxy for determining significance.  Intuitively, it makes sense: the more creatively different an idea is, the more likely it seems that it will have an impact. 

Originality, however, is a matter of both perspective and scale of measurement.  Newton's famous quote: "If I have seen farther it is by standing on the shoulders of giants", summarizes that no intellectual work exists in a vacuum: the myth of the lone genius is just that, a myth.  Edison did not invent the lightbulb, he made a significant improvement in its design which moved it past the tipping point; Einstein did not invent relativity, he had a mathematical insight which crystalized a collection of growing problems that many were starting to pay attention to; Hopper did not invent the compiler from whole cloth, she simply was the first to achieve that milestone amongst a number of others who were working on the automation of computer control. Reinvention, at this gross intellectual level, is not only frequent, it is to be expected.

At a finer granularity of measure, however, pretty much every non-plagiarized work is quite original: even if two people come up with effectively the same approach to a problem, how they approach it and how they validate their approaches will generally end up being very different, simply because the space of possible viable realizations of a program of research is so large.  Likewise, even a highly "unoriginal" idea at the grand scale may have great impact when introduced to an area where it is not commonly used, such as the recent Bayesian revolution in cognitive science.

So, originality per se is not a very useful measure; instead, you really want to be able to evaluate the likelihood of intellectual significance in your work.  For that, there is simply no substitute for getting to know the community that you want to impact.  You can do the most beautiful and elegant research in the world, but if it does not connect with intellectual issues that matter to others, it will remain in a sort of limbo... perhaps to be revived in 100 years (cf. the swing between frequentist and Bayesian statistics), or perhaps simply to be forgotten in the archives of history.

Thus, when it comes to evaluating one's own research, the thing you really should be worrying about is not unoriginality, but insignificance.  If you are working honestly, you will be original.  To estimate the significance of a piece of your work:


Know who you are trying to affect, and learn how to speak their language.  This typically involves reading relevant parts of the literature.
With respect to that literature, be able to explain how your work changes how people in that community should be thinking and acting.


And that's the (perhaps unsatisfying) long and short of it: if your work is done honestly and has an impact on the scientific community, then its originality is sufficient.