I recently read an intellectual biography of Feynman by Lawrence Krauss (here) and was struck by the following contrast between physics and linguistics. In linguistics, or at least in syntax, if a paper covers the very same ground as some previously published piece of work, it is considered a failure. More exactly, unless a paper can derive something novel (admittedly, the novelty can be piddling), preferably something that earlier alternatives cannot (or do not) get, the paper will have a hard time getting published. Physicists, in contrast, greatly value research that derives/explains already established results/facts in novel ways. Indeed, one of Feynman’s great contributions was to recast classical quantum mechanics (in terms of the Schrodinger equation) in terms of Lagrangians that calculate probability amplitudes. At any rate, this was considered an important and worthwhile project and it led, over time, to whole new ways of thinking about quantum effects (or so Krauss argues). If Feynman had been a syntactician he would have been told that simply re-deriving Schrodinger equation is not in and of itself enough: you also have to show that the novel recasting could do things that the classical equation could not. I can hear it now: “As you simply rederive the quantum effects covered by the Schrodinger equation, no PhD for you Mr Feynman!”
Now, I have always found this attitude within linguistics/syntax (ling-syn) rather puzzling. Why is deriving a settled effect in a different way considered so uninteresting? At least in ling-syn? Consider what happens in our “aspirational peers” in, say, math. There are about a hundred proofs of the Pythagorean theorem (see here) and, I would bet, that if someone came up with another one tomorrow it could easily get published. Note, btw, we already know that the square of the hypotenuse of a right angles triangle is equal to the sum of the squares of the other two sides (in fact we’ve known this for a very long time), and nonetheless, alternative proofs of this very well known and solid result are still noteworthy, at least to mathematicians. Why? Because, what we want from a proof/explanation involves more than the bottom (factual) line. Good explanations/proofs show how fundamental concepts relate to one another. They expose the fine structure and the fault lines of the basic ideas/theories that we are exploring. Different routes to the same end not only strengthen our faith in the correctness of the derived fact(oid) they also, maybe more importantly, demonstrate the inner workings of our explanatory apparatus.
Interestingly, it is often the proof form rather than the truth of the theorem that really matters. I recall dimly that when the four color problem was finally given a brute force computer solution by cases, NPR interviewed a leading topologist who commented that the nature of the proof indicated that the problem was not as interesting as had been supposed! So, that one can get to Rome is interesting. However, no less interesting is the fact that one can get there in multiple ways. So, even if the only thing a novel explanation explains is something that has been well explained by another extant story, the very fact that one can get there both from varying starting points is interesting and important. It is also fun. As Feynman put it: “There is a pleasure in recognizing old things from a new viewpoint.” But, for some reason, my impression is that the ling-syn community finds this unconvincing.
The typical ling-syn paper is agonistic. Two (or more) theories are trotted out to combat one another. The accounts are rhetorically made to face off and data is thrown at them until only one competitor is left standing, able to “cover the facts.” In and of itself, trial by combat need not be a bad way to conduct business. Alternatives often mutually illuminate by being contrasted, and comparison can be used to probe the inner workings so that the bells and whistles that make each run can be better brought into focus.
However, there is also a downside to this way of proceeding. Ideas have an integrity of their own which support different ways of packaging thoughts. These packages can have differing intellectual content and disparate psychological powers. Thus, two accounts that get all the same effects might nonetheless spur the imagination differently and, for example, more or less easily suggest different kinds of novel extensions. Having many ways of conceptualizing a problem, especially if they are built from (apparently) different building blocks (e.g. operations, first principles, etc.) may all be worth preserving and developing even if one seems (often temporarily) empirically superior. The ling-syn community suffers from premature rejection; the compulsion to quickly declare a single winner. This has the side effect of entrenching previous winners and requiring novel challengers to best them in order to get a hearing.
Why is the ling-syn community so disposed? I’m not sure, but here is a speculation. Contrary to received opinion, ling-syns don’t really value theory. In fact, until recently there hasn’t been much theory to speak of. Part of the problem is that ling-syns confuse ‘formal’ with ‘theoretical.’ For example, there is little theoretical difference between many forms of GPSG, HPSG, LFG, RG, and GB, though you’d never know this from the endless discussions over “framework” choice. The difference one finds here are largely notational, IMO, so there is not room for serious theoretical disagreement.
When this problem is finessed, a second arises. There is still in generative linguistics a heavy premium on correct description. Theory is tolerated when it is useful for describing the hugely variable flora and fauna that we find in language. In other words, theory in the service of philology is generally acceptable. Theory in the service of discovering new facts is also fine. But too much of an obsession with the workings of the basic ideas (what my good and great friend Elan Dresher calls “polishing the vessels”) is quite suspect, I believe. As ‘getting there in different ways’ is mainly of value in understanding how our theoretical concepts fit together (i.e. is mainly of theoretical/conceptual value), this kind of work is devalued unless it can also be shown to have languistic consequences.
Until recently, the baleful effects of this attitude have been meager. Why? Because ling-syn has actually been theory poor. Interesting theory generally arises when apparently diverse domains with their own apparently diverse “laws” are unified (e.g. Newtonian theory unified terrestrial and celestial mechanics, Maxwell’s unified electricity and magnetism). Until recently there were not good candidate domains for unification (Islands being the exception). As I’ve argued in other places, one feature of the minimalist program is the ambition to unify the apparently disparate domains/modules of GB, and for this we will need serious theory. And to do this we will need to begin to more highly value attempts to put ideas together in novel ways, even if for quite a long while they do no better (and maybe a tad worse) than our favorite standard accounts.
 The two are very different. Data is problematic when inconsistent with the leading ideas of an account. These kinds of counter-examples are actually pretty hard to concoct.
Cognitive linguists love to publish things showing that they can explain phenomena that have already been explained by generative linguists, but in a way that accords better with what's known about the mind and brain in the rest of cognitive science, using completely different theories.ReplyDelete
The development of OT is an example of a genuine new theory arising out of otherwise well-known facts. And OT has been widely adopted despite the fact that there are some empirical observations (most notably opacity) that its standard formulation is unable to account for.ReplyDelete