This earlier post quoting Rob Chametzky’s typology of linguistic research generated some interesting discussion, much of it needed in my opinion. I would like to spend a paragraph or two ruminating (ranting might be more like it) on the current state of theoretical work as Rob characterizes it, and in particular, on why there appears to be so little of it. Before starting, let me reiterate that concentrating on theory is not intended to impugn the other kinds of research that linguists do. There is a lot of excellent descriptive and analytic work out there, and three cheers for that! However, as Peggy pointed out in the comments section, theory is not generally accorded much of a hearing unless it comes from Chomsky, and, IMO, even proposals from this quarter are less well received than they once were. Why?
Peggy offers one very plausible hypothesis: that it is “easier to evaluate analytical work,” which “adopts some premises, applies them within a domain, and analyzes the outcome.” How so? Well because “[t]heoretical work involves examination of premises, and it's much more difficult to convince people that their premises are wrong than to convince them that such-and-such data can be analyzed within their (perhaps slightly amended) premises.” Peggy’s observations express Kuhn’s old observation that “normal science” is, well, the norm, and it generally accepts and adapts given theoretical conceptions rather than challenges them. So, in this regard, theory within linguistics is no different from theory anywhere else.
However, I am not fully convinced of this. Here’s why. Rob notes that theory itself rests on meta-theory and meta-theory concerns itself both with general methodological concerns (simplicity, consistency, relation to other theories etc.) and with domain specific adequacy conditions. In the domain of linguistics, the first general methodological concerns have been made prominent within recent minimalist theory, the hard part being how to concretize the methodological concerns in the particular setting of linguistics (e.g. when is a proposal “simpler” or “more elegant” or “less redundant” than another?). Rob illustrates domain specific meta-theory with Chomsky’s differentiating theories that are observationally, descriptively and explanatorily adequate. These meta-theoretical desiderata, especially the third, are where theory lives. I believe that the field has sometimes forgotten this. And if it has, then the dearth of theory should be unsurprising. What then are the large meta-theoretical issues that drive theory?
The first one, which traces back to what Chomsky likes to call “the earliest days of Generative Grammar,” is Plato’s problem (PP). The second, is of more recent vintage, and has been dubbed “Darwin’s Problem” (DP). A theory attains explanatory adequacy (EA) when it can deduce the attested Gs in combination with a specification of the PLD. A theory can be EA+ (‘+’ = ‘beyond’) if the principles the EA theory postulates are ones that did (or at least, plausibly could have) arisen in humans. The PP, DP duo raise theoretical questions all by themselves for they pull in opposite directions; PP feeling comfortable with a richer more linguistically specific FL while DP happier with a poorer less linguistically specific FL. Reconciling this tension is a worthy theoretical project all by itself.
Note that both PP and DP are based on two big, and IMO, hardly contestable facts: viz. (1) that any human can acquire any language in a pretty short time and in pretty much the same way regardless of the language at issue when exposed to PLD of that language, and (2) that human language capacity emerged at some time in the recentish past from ancestors that were not language endowed the way we are. These big facts are (two of) the fixed points of our linguistic meta-theory, and in terms to which theory should be addressed. This meta-theoretical background places demands both on proposed analyses concerning the structure of particular Gs and on the structure of FL/UG. And it is precisely these demands that allow for the evaluation of proposals somewhat independently of whether they are analytically (in Rob’s sense) sound. In other words, aside from specific familiar linguistic data (e.g. that ‘flying planes can be dangerous’ is ambiguous) that we use to evaluate a given proposal, there is also the question of whether a given proposal can be argued to be acquirable/evolvable. Respect for theory starts with taking these meta-theoretical demands seriously. IMO, our sensitivity to these concerns is currently inappropriately low.
Why do I say this? Here’s some anecdotal evidence for this judgment.
First, I think that many practitioners of the syntactic arts misperceive what the object of inquiry is. If asked: “what does linguistics study?” many will answer: “language.” But language is not the object of study, at least for generative linguists. The faculty of language (FL) is. FL in combination with other cognitive faculties leads to language behavior, utterances, perceptions, plays, movies, etc. But these products are not the primary object of inquiry despite the fact that studying language behavior, both in the wild and in more artificial settings (e.g. acceptability judgments), has been a good place to find data that bears on the structure of FL. This noted, the goal of generative grammar has never been to describe or regiment language (in fact, many generativists, me included, do not believe that languages are natural kinds and so not appropriated targets of study) but to describe the fine structure of FL. Now here’s the kicker: if one thinks that the target of inquiry is language, then the theoretical considerations that PP and DP lead to will not seem particularly germane to the enterprise. To address PP and DP we need to advert to the structure of FL and this involves considerations that go beyond covering the data that linguists primarily rely on to make their analytical arguments. Thus, if language replaces FL as the research topic then PP and DP won’t loom so large with the consequence that theory will seem pointless and, thus, not surprisingly, it’s pursuit will be undervalued.
I believe that this shift from FL to language as the cynosure of linguistic inquiry has gotten greater of late. Here’s some anecdotal evidence. There once was a time when the first intro chapter of virtually every thesis in syntax began with a discussion of the logical problem of language acquisition (aka PP) and ended with a concluding chapter considering what the technically meaty chapters 2-5 had implied about UG and Plato’s problem. One might argue that this was mere window dressing and that the formulations and discussions were very pro forma. To a degree, I would agree with this. However, the required discussion (even if cursory) pointed to a (tacit) recognition that the details in the middle were in service of the larger questions driving the field and this served to legitimate these questions and the theory that lives on them.
Nowadays, any similar discussion is hard to find. Indeed, I would go further, the very idea that one’s analytics deserve even cursory consideration in terms of the more encompassing framework concerns is considered sort of quaint. There’s lots of concern of how syntax interfaces with semantics or phonology, lot’s of worries about how structures proposed in language A compare to those in B. But there is relatively little overt worry about PP or DP.
Here’s a question for my senior colleagues: How many times have you asked in a public venue (e.g. at a thesis defense or at a talk), or even over beer, how some proposal you’ve been talking about (with such and such principles and this and that parameters) could be acquired? How many of you in teaching about grammatical variation stop and concentrate on how some rather subtle difference/parameter one is interested in (e.g. the (purported) difference between English and Romance wrt extraction out of weak WH islands) could have been acquired/set? I agree that this is not the only kind of question worth asking and I agree that an analysis might be valuable even in the absence of an answer to this kind of question, but in my recent experience, we act as if this really doesn’t matter at all, which is why such questions are never raised. Indeed, I suspect that many believe that such questions are either BS or are more properly addressed to our psycho-ling colleagues or both (and yes this does suggest a certain kind of unattractive attitude not uncommon to syntacticians).
I would add that in my experience linguists tend to be hostile to theoretical innovation. This is manifest in two ways.
First, we really don’t like having multiple routes to the same conclusion. In other fields, it is considered interesting to reach the same end in two different ways. So there are myriad proofs of the Pythagorean theorem, and all are considered to be of interest. Why? Why would a novel proof still be publishable (and published)? Because it is not only interesting that a certain fact is true (viz. the square of the hypotenuse...) but it is equally (maybe more) interesting how different concepts link together to demonstrate this. Linking concepts together is what theory is all about and the reluctance of linguists to prize this kind of thing betrays a lack of interest in theoretical work.
Second, the field has a severe “historical bias.” What I mean by this is that we demand that later proposals surpass in empirical coverage earlier proposals in order to get a hearing. But why? Why should a newcomer be required to do better than a senior citizen? In fact, let’s go one step further, why shouldn’t a newcomer be given some empirical slack? After all, most of the proposals we prize have been augmented over time to increase their empirical range, so why demand of a new proposal that it cover all the ground of the venerable ancestor and more? Isn't this just a way of making it impossible for new ideas to breathe? And doesn’t this attitude indicate that what we really care about is that the data points be covered rather than how they are covered? And doesn’t this reflect an instrumental conception of theory?
So, in sum, not only do we often act as if having two ways of thinking about a problem is intellectually abhorrent, we often act as if theoretical novelty is (or should be) a punishable offense, novel theory being acceptable only if it brings in its train wider empirical coverage.
So, that’s why I think that linguists don’t really prize theory, and that’s too bad. It’s unfortunate because it reflects the fact that we have turned away from the foundational questions of the discipline, from the big facts and questions that, IMO, are the problems of deepest interest. Theory is not the only kind of inquiry worth doing, but it has its place and we should once again recognize this. How? Here’s an easy first step: next time you hear a talk or read a paper, ask yourself how the proposal put forward bears on the structure of FL and what kind of light it sheds on PP and/or DP, our two great meta-theoretical questions.
 Interestingly, for this to take place so readily there must be an assumption that what data are relevant to a proposal is easy to determine without committing theoretical hostages. I am not sure that this is always the case. So a chunk of the controversy surrounding the movement theory of control (something that I am relatively familiar with) hangs on whether certain observations (e.g. partial control) are reflected in syntactic representations or not. It is not clear that this kind of dispute is a purely data dispute however.
 Alex C makes a similar point in the comments section, though he embroiders it in ways I would not.
 Actually both were big questions posed at the start of the Generative enterprise. However, as a matter of fact, PP was central to the discussion since (at least) Aspects while DP became important only with the advent of the Minimalist Program. There are good reasons for this (viz. that DP was not really worth discussing until we had some candidate principles of UG). However, right now, both PP and DP are important meta-theoretical framework questions.
 Indeed, the route to the conclusion is often more interesting than the conclusion itself. I recall the following (not verbatim) comment from a mathematician after the four-color problem was solved via a computer crunching through all the possibilities: “I guess the problem was not as interesting as we supposed.”
 A point that Greg Kobele defends in his thesis.