How much THEORETICAL work is there in syntax?

In an indiscrete footnote in some earlier post I suggested that linguistics, or at least generative grammar, or at least syntactic “theory” had not yet escaped its philological roots. There are several marks of this. The footnote mentioned the inordinate respect for data. I would not be surprised if many readers saw this and either thought I was joking (me? Do you know me to joke about such matters?) or nodded knowingly that such a cavalier attitude to empirics is hardly surprising coming from me. However, I was not (entirely) speaking tongue in cheek and would like to defend the proposition that despite our best efforts, linguistics has yet to embody the true scientific spirit, one that embraces theoretical insight as one of the (maybe the) central goals of inquiry. I will confine my remarks to syntax, but I believe that my qualms extend beyond this particular bailiwick. To put my point bluntly: despite prevailing assumptions, there is precious little theory in theoretical syntax and this, I believe, is because we are still in the grip of the descriptivist demon.

There are four kinds of research in the real sciences: (i) phenomenological,

(ii) experimental, (iii) analytical/computational, and (iv) theoretical. The first is roughly descriptive: this variable covaries with that one in these circumstances (think pressure, volume and temperature). The second aims to test theory (e.g. if there is an aether then given the earth’s spin light will move measurably faster in this direction than that one). The third is intimately related to the second. Oftentimes to get testable predictions requires solving equations for special cases and this can demand a lot of computational skill (think black holes and general relativity). The forth kind of work is theoretical and it aims to explain why we find what we find and why we don’t find what we don’t. Fundamental theory achieves this using simple natural principles. What makes this enterprise especially demanding is that a large part of what theory does is discover what ‘simple’ and ‘natural’ mean in a given context of inquiry. ‘Simple and natural’ are a bit like pornography: hard to specify antecedently but recognizable (at least over time) when paraded.

Work in syntax has research that corresponds roughly to the above four-part division. Thus, there are roughly four kinds of syntax research: (a) Work that analyzes data in a given language. These are generally organized around constructions such as relative clauses in X or ‘tough’ constructions in Y or resumptive pronouns in Z. Here the targets of explanation are the intricacies of specific constructions and theory is used to explain the observed intricacies properties. (b) Research that explores given theoretical constructs empirically. In practice, this is often pursued in tandem with  (a), but the two are conceptually different. Here the aim is to refine or “test” a theoretical point and data is used to polish theoretical details or choose between competing alternatives. One argues from data to theory, rather than from theory to data. Examples include work in the mid 1980s investigating how exactly to state the ECP and subjacency conditions, looking for the right definition of government and binding domains. Other examples can be found in much current work trying to state exactly which heads are phases, differentiate weak from strong phases, or what the right statement of defective intervention should be. A particularly popular sport is to try and identify the right sets of features the grammar manipulates. (c) Papers that aim to unify disparate UG generalizations. This work has both an analytical and empirical dimension, with the second following the first.  The classical example of this is Chomsky’s reanalysis of Ross’s Islands in terms of the theory of subjacency and later extensions of this that aimed to incorporate Huang’s CED effects into a theory of bounding in terms of barriers. More current examples include Chomsky’s proposed unification of PS and movement rules in terms of Merge, Pesetsky and Torrego’s analysis of fixed subject effects in terms of economy, the unification of control and binding with movement and/or Agree, among others. (d) Papers whose aim is to “simplify” and conceptually “motivate” the basic machinery, e.g. Minimality in terms of search, the cycle in terms of Extension, Phase Impenetrability in terms of Multiple Spell Out, and islands as PF/linearization effects.

All of these kinds of research are valuable and contribute to the answering the central questions in linguistics. However, whereas the field values the first two unequivocally, it has tended to be less welcoming to theoretical research of the (c)/(d) variety above. Why so? Here are three speculations.

First, many linguists tend to confuse ‘theoretical’ and ‘formal.’ Since the beginning, Generative Grammarians, including syntacticians, have had a proprietary technical formalism for describing linguistic phenomena. Part of what it is to be a linguist involves mastering this technical formalism. However, being formal does not entail being theoretical.  Descriptive phonetics is quite formal but its aims are not theoretical. Ditto for most of statistics, and, in my opinion, semantics. Most theory is formal as formalism allows for the kind of abstraction/idealization that theory lives on. But formal is not equivalent to theoretical. Virtually all current work in linguistics is formal. Very little is theoretical in the sense of (c)/(d) above.

Second, it fits with the widespread Empiricist belief that science consists in the careful production and organization of facts.  Theory, on this view, is effectively a way of compactly summarizing the data. On this view, theory is useful, but epistemologically secondary. The main enterprise is to discover, collect and organizing the facts. 

This Empiricist conception contrasts with the Rationalist one. For Rationalists, correct theory identifies the underlying causal powers at work in generating the observed data. What theory identifies, therefore, is metaphysically prior to the observed data as correct theory delineates the basic causal ontology; the fundamental/basic operations/powers and primitives. Thus, if the aim of science is to understand how things work then a science succeeds to the degree that it can produce plausible theories. No theory, no candidates for causal powers, no such candidates, no explanation. True, data is part of (note, part of) how we evaluate whether or not a theory is plausibly true (or even exactly true), but a theory is not a compact summary of the (potential) data but a limning of the basic metaphysical furniture.[1]

The Empiricist attitude fits well with another one, not uncommon within linguistics, which luxuriates in the boundless variety that we find within natural languages.  The theoretical impulse involves abstracting away from this diversity in order to focus on the underlying invariant structures. To those impressed by the evident variety of NL phenomena, such a theoretical attitude can appear to be dismissive of the facts and hence non-scientific.

Third, until recently, there has not been much scope for interesting theory. Theory lives when there are higher order generalizations to unify and rationalize. One of the glories of Generative Grammar, IMO, has been the discovery of a dozen or so of these kinds of non-trivial generalizations that have a claim to be properties of FL/UG. Once these exist, theory can emerge. Until these exist, whatever theory exists is so closely tied to the data that separating empirical from theoretical speculation is unproductive.  Let me explain with a simple example.

Chomsky’s unification of island phenomena presupposes that Ross’s description of islands is more or less correct.  Why? Because it is not worth unifying these phenomena in a simpler more natural framework if the various generalizations that Ross proposed are wrong. However, given that Ross was right, we can step back from the most immediate empirical data (e.g. acceptability judgments about island violations) and start investigating the properties of these generalizations. Or, to put this another way: Ross focused on first level acceptability data (e.g. is this sentence acceptable, how does this long distance dependency compare with that one wrt acceptability) in order to establish his generalizations. Chomsky, given Ross’s accomplishments, could now focus on a second level question: what features do islands have in common, or, why do we have the islands we have? Whereas Ross’s investigation was largely empirically driven (i.e. we postulate the CNPC because Who did you meet someone who saw is judged lousy compared to Who did you think that Bill said that you saw), Chomsky’s was not. For him the central concern was mainly theoretical: to rationalize the diverse island phenomena in terms of simpler more natural principles. And this was indeed the main motivation for Chomsky’s theoretical efforts:

… the island constraints can be explained in terms of general and quite reasonable computational properties of formal grammar (i.e. subjacency, a property of cyclic rules that states, in effect, that transformational rules have a restricted domain of potential application; SSC, which states that only the most prominent phrase in an embedded structure is accessible to rules relating it to phrases outside; PIC, which stipulates that clauses are islands subject to the language specific escape hatch..). If this conclusion can be sustained, it will be a significant result, since such conditions as CNPC and the independent wh-island constraint seem very curious and difficult to explain on other grounds. (p. 89; On WH Movement, my emphasis)

Of course, good theory leads, one hopes, to novel testable predictions. In the case of the Theory of Subjacency, the novel prediction was successive cyclicity, which, we discovered, had manifestations testable in terms of acceptability data (e.g. Kayne and Pollock on stylistic inversion in French, McCloskey and Chung on Complementizer agreement in Irish and Chamorro, etc.). However, the value of theory lies not merely in extending the factual base, but in introducing new explanatory desiderata, as Chomsky does in the quote above.

One of the most important contributions of the Minimalist Program, IMO, has been to emphasize the value of this kind of theoretical research, research that is one or two removes from the immediate empirical data. However, my read on what people are actually doing, suggests that this is an idiosyncratic position. The bulk of MP research seems to me to fit largely into categories (a) and (b) above. Moreover, much of it, IMO, could be just as usefully have been pursued in a GBish idiom, its minimalism being largely technical (i.e. lots of features and probes and goals and AGREE rather than overt and covert movements). This does not mean that this work is bad or unimportant. But, it is not particularly theoretical. It is pretty similar to older styles of research, ones driven largely by concerns of covering the first order data.

Let me put this another way: what a lot of minimalism has done is substitute one set of technicalia (GBish) for another set (Phases, probes/goals, feature driven operations, etc.). The larger initial goals of the program, to explain why we have the FL we do and not another, is often invisible in the work being done.  Papers that even ask this why question are pretty rare. Indeed about as rare as papers in GB that worried about whether the parameters being proposed or the principles being endorsed really alleviated the learnability problem.  Let me be clear here, or clearish: I am not saying that such questions are easy to answer. If they were, we would not have a field. But, it is surprising to me how rarely theory is even sensitive to their relevance. The focal question of GB theory was the learnability issue. The focal point of MP is the ‘why this FL/UG rather than other conceivable ones’ question. All the other stuff is the necessary pre-requisite for theoretical work. It is not the same as theoretical work.

So, why the dearth of theory even within the confines of MP? Maybe because the opportunities for doing this style of work are relatively recent (despite some very impressive precedents) and it takes a while for a novel style to gain a foothold. After all, we all know how to do research of the (a) and (b) type. Furthermore, we know how to teach it and test it and PhD it and review it. Maybe work of the (c)/(d) variety is less common as we have not yet found ways to impart its virtues. Maybe. But I suspect that work of the (c)/(d) variety will prove to be a harder sell precisely because of its greater inherent abstractness. The real message of MP is that you should not simply look at what’s sitting before your eyes, and this has always proven to be a tough sell, unfortunately.

Let me end by reiterating that all the varieties of research noted above are valuable and important. Theorists cannot do their work unless less theoretical work is pursued. However, theoretical work is different, and right now, it’s having a tough time gaining traction. One of the initial hopes of MP was to refocus activity in more theoretical directions. IMO, to date, this hope has not been especially well realized.

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[1] I still recommend Nancy Cartwright’s discussion of this, among other places here, as discussed a bit here.