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I am curious as to how academia continues itself without replication or reinventing the wheel. So many academicians in so many areas of work, how would one ever find out whether the work he or she is about to embark on can be considered an original work? That someone didn't already publish the very same result?

In engineering, we have all heard the story of Cooley-Tukey's method of Fast Fourier Transform. The story goes Tukey has been applying his own method of FFT for years without recognizing that the implementation was a fundamentally original approach. Until he brought it up in a meeting in the 1950s, he had always thought that this method was used widely given its extraordinarily simple implementation. Only later did everyone realize that Gauss had used the very same method 160 years earlier.

The same goes for the famed Wiener-Khinchin theorem in stochastic analysis. After two most ingenious mathematicians ever graced this earth came up with this theorem did they realized that Einstein had already published it a decade ago.

Doubtlessly, there are thousands of examples in all branches of natural sciences. It is less clear whether the social science encounters this problem since no two times and places are ever alike, and the social reality keeps on changing therefore novel results is always promised.

So how can one find out in the quickest way possible that his or her work is original work? Original in the sense that the end result is something that improves upon an existing result or opens up an entirely new field without duplications from other people. Does there exist a database somewhere to categorizes all recent and historic progress in a certain field? Are there people who are employed in academia or elsewhere to do this very task?

Edit: I guess same goes for asking a question without looking at the other questions first...seems like this question was resolved in another post T_T

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    "I am curious as to how academia continues itself without replication or reinventing the wheel.": Unfortunately, academia has reinvented the wheel many times (and sometimes it invented less "efficient" wheels) :-( – Massimo Ortolano Mar 1 '15 at 22:24
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    I don't know if Wiener-Khinchin is a good example; Wiener's 1930 paper cites Einstein, so he evidently knew of the latter's work (though conceivably he discovered it during the preparation of the paper). But Einstein merely stated the claim without proof, so Wiener's proof was a genuine advance. – Nate Eldredge Mar 1 '15 at 23:25
  • Sometimes, they just don't know: google.com/?q=medical+invents+newton+integral+gets+citations – Pavel Mar 2 '15 at 9:20
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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.

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You can never really find out for sure (which is why it's not uncommon for things which are not really original to be published). However, when a scientist has an idea that they would like to publish, it's expected that they be reasonably confident that it has not been published before. Someone who works in that field of research will have been keeping up with the latest developments, and should therefore know (99% of the time) whether their idea is new or not. If they don't know of any prior instances of that work, they should then search the standard references in their field, and these days, probably search the internet as well (e.g. Google Scholar) to see whether anything in a different field comes up.

When the paper is finished and sent for review, the reviewer(s) will go through the same steps; perhaps less rigorously, but still, there will be multiple people checking any given paper for previous work on the same topic. By the time a paper makes it to publication, one can be fairly confident that it contains something original.

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    Often anther field has discovered the same thing but using different words to describe it. – Ian Mar 2 '15 at 9:52
  • Indeed this happens sometimes, but many research problems are so specific that it's exceedingly unlikely they would show up in another field. – David Z Mar 2 '15 at 11:38
  • A simple example, is that software wrote as part of research on DNA, is now used to work out how hand written books have changed over 1000 of years. We just DON'T know how many other cases of the same solution working for problems in different areas, most of the time when you reinvent the wheel, you never find out that you have. – Ian Mar 2 '15 at 22:06
  • @Ian I'm not sure if it's clear, but I'm not disputing your claim that there are many cases in which results are rediscovered in different fields, often because of conflicting terminology. But I'm saying there are also many cases, probably a majority, where this does not happen. – David Z Mar 3 '15 at 3:12

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