I think the main disagreement I have with your translation is that I don't think that "normatively good research" is the same as "research that the scientific community approves of". I believe that the standards of the scientific community can and should be criticized on rational grounds. I anticipate you might ask, given the above, on what is meant by "normatively good research" then, I guess I just mean that which corresponds with intellectual and epistemic virtue. My use of "normative" isn't my own innovation though, it is the same sense in which logic is a normative science. Logic doesn't describe how people actually think, but how people /should/ think; but this normativity shouldn't be understood exclusively in moral terms. Normativity refers to how well does the subject matter, in this case thinking, relate to it's end. Normatively good research, then, refers to research that best satisfies the purpose or goal of research.
I guess, to be fully clear, I should clarify on what the purpose or goal of research is. You could say that the goal is usefulness, in which case my proposition would be a tautology ("Research that is good at being useful is useful and research that is bad at being useful is not useful."), but I don't think that's the answer. Maybe I'm being an idealist, but I think the primary purpose of research is to satisfy curiosity, without disregarding any other ulterior aims and purposes that actual researchers might have. I think curiosity is one of the few actual drives that people have that points to truth for it's own sake, it represents a person's "will to know"*.
Is what satisfies curiosity also useful? I think if my argument is wrong, this is where it is weak and potentially vulnerable. But I don't think it is obviously wrong. Your concern seems to be that researchers have a responsibility to prefer research that is useful over research that isn't useful, even if it doesn't satisfy the researchers interest as much. But I doubt that it is that easy to determine whether research will be useful /a priori/. C.S. Peirce uses the example of conic sections being useful for Kepler's astronomy, which in turn was useful for Newtonian physics. We're talking about research that had been worked on for generations, and its hard to imagine any of these men "optimizing the usefulness of their research programs". Yet it is hard to imagine work that has had a greater positive affect on our standard of living than these men.
So you believe that the pursuit of knowledge is inherently virtuous, and you endorse research on those grounds? I.e. research is good to the extent that it reveals truth, and bad to the extent that it reveals falsehoods?
Can you clarify if you also believe that usefulness should be a non-negligible factor in evaluating the virtuousness of a given piece of research (irrespective of other factors which might make it impossible to care about usefulness directly)?
In a recent post I posed the question: is the common good served by directing research efforts towards theoretical problems which are interesting to researchers?
komponisto defends interesting problems, arguing that researcher's perceptions of interestingness are often better able to predict future usefulness than anyone trying deliberately to determine what will be useful. This is a plausible claim (although I disagree), and I have encountered it a number of times in the last couple of days. This claim was advanced as a defense of the status quo, but if we really believe it then we should certainly try and understand all of its consequences.
When setting out to predict the usefulness of a research program (as I suggest we should), we are not required to do it via deductive arguments which estimate the likelihood of certain applications. We can use all of the data available, including how interesting the problem seems---to us, to other researchers, to lay people, etc. If intelligent observers' notions of interestingness are substantially corellated with future usefulness, potentially in unpredictable ways, then we would be wise to take this information into account. This is precisely what komponisto and others argue, and they conclude that we should support work on the problems an investigator finds most interesting. I claim this is an example of motivated stopping: the argument was thought through just far enough to support changing nothing.
We have access to many, many indicators of interestingness for any candidate research problem. A problem can seem interesting only to a single person who understands the background in great depth; it can seem interesting to a small group of researchers in related fields; it can seem interesting to mathematicians broadly; it can seem interesting to computer scientists, to physicists, to biologists, to engineers, to laypeople. It can seem particularly interesting to professional mathematicians, or to novices with new ideas. It can invoke feelings of immediacy, of needing to know the answer; it can simply be fun to work on. Particular countries or cultures or time periods or subfields may have objectively better or worse aesthetics.
If our aim is to use interestingness as a predictor of potential usefulness then all of this variability is an asset. We have a historical record to be scoured; patterns to be evaluated. Understanding these patterns is of critical importance to the quality of our predictions and the efficiency of our research institutions. If the historical record is too opaque, we should at least establish a culture of transparency: make records not only of what work is done, but why it is done. Who did it seem interesting to? How did they feel about the research program; why were they really working on it? In the long term, we can hope to discover whose intuitions were valuable and whose were not; we can understand which aesthetics lead to useful work and which do not.
Over time (if not immediately), we can hope to develop a common understanding of the link between interestingness and future usefulness, and develop institutions which exploit this understanding to produce valuable research.