My wife sometimes asks me why I am not working on important problems like world hunger. Instead, I am one of the top world expert in tag-cloud drawing. I am sure she thinks that I just fool around, faking serious research.
I actually take my research very seriously.
I like to distinguish abstract from concrete research. Concrete research is when you seek to obtain results in special cases. For example, an AI researcher may try to first understand how we can detect spam. Eventually he might move on to even more sophisticated tasks. In such a form of research, there are no overarching formal plans. You could say it is inductive, maybe. Researchers are often driven to this form of research because the deeper problems are simply too difficult to address directly. (I define a problem to be too difficult when you cannot make noticeable progress in a matter of months.) They hope for a breakthrough to an important problem to come as they work on a narrow issue.
Abstract research derives from a formal plan. Semantic Web is one such a plan. Tim Berners-Lee even drew diagrams early on of what the beast should look like. The research issues are clearly laid out. As a researcher you are tackling an extremely difficult problem, unsure whether you will ever make any noticeable progress. Researchers follow this path because they believe that only a focused effort in a definite direction can solve the difficult problems. Funding agencies love abstract research.
It might be a matter of biology, but my brain has always been much more productive in concrete research. I resist the inductive/deductive classification because it feels wrong. However, times and times again, working on a tractable, but possibly insignificant problem, has lead me to understand a deeper issue. When the problems are too big, my brain gets into circular and incorrect arguments. I need to chop down the problems to a manageable size. The problems need to be hard enough to push me to the limits, but easy enough that I can make weekly progress. Moreover, I cannot never know exactly what I will be doing a month later, as a researcher.
I will make a stronger claim: abstract research is never done. Researchers will give the illusion that they are working directly on some grand problem (like world hunger), but, in reality, they will work at a much smaller scale. And when a researcher solves a grand problem in what seems like a short time, and with few concrete possibly irrelevant steps, I attribute it to luck or lies.
See also my post my research process.