One of the greatest errors I see in computer science research is a tendency to view research as a spectrum with "applied" at one end and "basic" at the other, with attached assumptions that "applied" is incremental, boring, and engineering-oriented, but "basic" is crisp, radical, and intellectually satisfying. This is a false dichotomy, and I like to debunk false dichotomies.
I think the most principled way to construct such a spectrum is to classify research projects according to the degree of simplifying assumption they make to reach a crisp problem statement. So "applied" research adopts most of the relevant "real world constraints" into its problem statements, and "basic" research throws most of them out. The error is to assume that "real world constraints" make a problem boring, intellectually unsatisfying, and non-conducive to finding real breakthroughs . This may be true "on average", but when choosing a research project one is not constrained by averages. In my experience, interesting research topics are abundant, and there are problems whose solution can be immediately applicable to the world while also being intellectually satisfying and potentially breakthrough science. (The current frenzy over combined symbolic and concrete execution is a good example.)
Let me suggest several such problems in the area of software development technology that I feel aren't yet getting the attention they deserve.
We know that verifying real software against full specifications is prohibitively expensive in most cases. However, I hypothesize that one could cheaply verify most changes that land in mozilla-central. The secret is that most patches are refactorings --- changes that should not alter observable behaviour --- or can be split into refactorings plus a smaller change that actually alters behaviour. "Should not alter observable behaviour" is very simple to state and understand, but still very tight. It would be huge win if we could prove that most such patches meet that specification. It's unclear how difficult this would be in general, but clearly patches that are the output of refactoring tools should be tractable to verify, and there is a lot of unexplored territory beyond that.
Improved Record And Replay Debugging
I don't have time to work on Chronomancer, but someone should be working out how to expose omniscience to the programmer to optimize the debugging experience.
Testing Fixes For Non-Reproducible Bugs
Record and replay technology is more or less here. (I'll post more about VMWare's solution later, but suffice to say it's working quite well so far!) Suppose you have recording of a bug which isn't reproducible. Now you can replay that recording one or more times and understand the bug and write a patch that should fix it. The problem you immediately run into is: how do you check that the patch really fixes the bug? You somehow need to inject the fix into the code and replay; that's tricky, and the fix may disturb the replay and cause the bug not to occur on that run for reasons unrelated to the bug actually being fixed.
Performance Measurement And Variation
Measuring performance is hard. One huge problem is that you want to measure effects that are much smaller than the random noise in the tests. I don't really know where this noise comes from. I would love to see research that analyzes the sources of run-to-run performance variation and describes techniques for reducing the variation.
I believe all these problems are reasonably easy to get into, have been little investigated in the past, have lots of room for exploration by multiple groups, are intellectually stimulating, and are likely amenable to solutions that could be immediately applied to the needs of software developers.
 The converse error --- assuming that "basic" research must not be boring or incremental --- is also widely held, but more easily falsified. Consider the endless stream of esoteric type theories that are both boring and completely incremental, such as my POPL '99 paper!