In my most recent lament over the lack of support and interest in basic scientific research, I've developed an analogy that not only helps explain the role of methodology, but also highlights the import of fostering more exploratory research. The analogy is to think of normal science (in the Kuhnian sense) as akin to solving puzzles (e.g. jigsaw puzzles, mazes, and crosswords). A puzzle has a clear goal, a known solution, constrained moves, and a collection of strategies/heuristics for reaching that solution. My claim is that people, and especially scientists, unfortunately see doing science as a similar activity.

First, let me describe picture puzzles in a way that makes the analogy clearer. You are given a collection of pieces that must be arranged correctly in order to form that picture. The picture itself is not the goal, it is merely the solution. The goal is the enjoyment one gets from the activity and the feeling of accomplishment one gets from completing the activity. The picture may be a famous painting, a landscape, or a pure white sheet -- it doesn't matter -- but the less constraining the image, the more constraints that must be imposed by the pieces. Also, some pictures are more appropriate for different types of puzzles: e.g., a completely white jigsaw is fine, but that doesn't work for the sliding or rotating tile types of puzzles.

When putting together a picture puzzle one works with and against the constraints of the pieces. It is rare that a piece could go in multiple locations, so you have to find its correct spot. Those same constraints can help you; for example, the corner pieces are the most constrained, you know where they must go first. Then edges must connect these corners and you typically know their required orientations. A salient feature of the image might make a particular cluster easier to fit together than other parts. Et cetera. Different types of puzzles require different methods to solve because they have different constraints. One puzzle is considered more difficult than another because it requires more sophisticated methods. A puzzle with more pieces requires more tenacity, but not specialized abilities. Regardless of one's skill level, with enough time and effort every puzzle can be solved by anybody who is capable of moving within the constraints. Hours and hours later you end up with an image that looks worse than a $5 poster of the same thing, but you did it yourself and you feel proud and accomplished.

Now I will explain how most scientific research can be seen as solving puzzles. Research science starts with either a specific problem or a particular phenomenon that needs explaining: Why do banks collapses cascade? Can one make a compound with inert atoms? Were Homo habilis capable of verbal communication? What role do bus routes have in disease spread? Et. cetera. This is akin to determining what picture to use in the puzzle. The discipline covering that problem or phenomena has established methods for solving problems: e.g. collect and analyze data, design an experiment, or run simulations. Different techniques are used for different questions even within the discipline, but there is an established way to do things.

The problem or phenomena to be explained is the solution to the puzzle, the methodology of the field determines what the pieces of the puzzle are, and that methodology combined with the available components determines which heuristics are appropriate. Often there aren't enough pieces to solve the desired puzzle (although that rare stops scientists from trying). Sometimes a problem is attacked with multiple techniques, some performing better and are more interesting than others, but the progress can rarely be combined. If the problem can be solved, then it is only a matter of time and effort to find the solution. If the problem can't be solved, then either you need more pieces or you chose the wrong kind of methodology for that problem (wrong puzzle time for that image). Likewise if it's too easy to solve (because then it's not interesting).

Many scientific projects have real consequences for policy, technology, etc. and so the solution is more than just a crinkled picture. But what scientists do, and what they are rewarded for, is picking the right methodology for a problem and then following the required steps to navigate the constraints and reach the solution. Nothing about this process is creative. The constraints of the problem fully determine the best analysis methods, and one must only follow through with that method's protocols. The method may not be sufficient, and some trial and error manipulation might be required to fill in gaps. Occasionally the methodology is extended to include protocols for filling gaps of that sort. This isn't real scientific progress, this is just getting better at solving puzzles of a certain type by solving puzzles of that same type. It is methodology progress, though, because it allows others to solve more complicated puzzles more easily.

What people call "interdisciplinary" research is usually just using a solution heuristic from one kind of puzzle and applying to another kind of puzzle. This is usually obvious, but sometimes one can transform the problem in a way to make this insightful. If you can translate a picture puzzle into a kind of maze, and solve it like a maze, then that's interesting. That's also a methodology problem -- how to analyze and manipulate the information -- and not a new result about the problem domain. For example, I have a project to translate N-person games into network structures that can then be "solved" by finding the optimal network flow on the resulting structure. This will turn certain situations that are unsolvable by current game theory techniques into ones that can be solved. Pictures that would not be good for current puzzle types would become fun and interesting with the new constraints.

However the potential for new and interesting puzzles is not valuable to scientists. Methodology research is only valued (these days) if you can already demonstrate that there is a problem people have been unable to solve that can now be solved. Of course people only care about problems they can already solve (or think they can), and what counts as methodology research is merely refining the existing heuristics to make more complicated puzzles of the same types already employed. But even that is rare most science is just applying existing tools to a well defined problem, going through the motions until everything fits together the way it's supposed to.

This is contrast to what basic research is supposed to be. Basic research is comprised of high-risk, high-payoff projects that explore new possibilities and totally new questions/problems. Not just problems that can't currently be solved, but problems that haven't been considered. And to solve these new kinds of problems one needs new methods. It's akin to inventing the first maze or the first sudoku. Once the field is discovered, it opens up new avenues of research. Unfortunately, because of how deeply the puzzle-solving mentality is ingrained in current academic training, most scientists can't even recognize a kind of problem they haven't seen before, let alone see why it might be interesting and worthwhile to pursue solving it.