The road ahead from Athens; some scattered initial remarks

I again mis-spelled someone's name. I "called" Winnie, "Wini." It is now corrected and I am sorry. However, the misspelling allows me to once again thank Winnie for all his great work in getting the Athens gig going. Thx and sorry.

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I am currently sitting on the 6^th floor of the Athen’s Way Hotel, eating some fruit and yogurt and sipping a cup of tea. It’s a beautiful day. The Road Ahead Conference (see here) ended yesterday and I thought that I would jot down some quick comments.  Before doing so, let me take this opportunity to thank the organizers (Winnie Lechner, Marcel den Dikken, Terje Londahl, Artemis Alexiadou and Peter Svenonius) for a wonderful event. It’s been a blast and my most secure conclusion from the past three days is that if you ever get invited anywhere to do anything by any of these people GO! Thx, and I am sure that here I am not speaking just for myself but for all participants. That pleasant task out of the way, here are a few impressions. In this post I’ll talk about very general matters. In some follow up posts I’ll remark on some of the socio-political issues raised and what we might do to address them. And in some yet later posts I’ll discuss some of the stimulating questions raised and ideas mooted. So let’s start.

My overall impression, one that runs quite counter to some of the pessimism I often hear from colleagues about the state of contemporary syntax, is that intellectually speaking, we are in a golden age of syntax (though politically and sociologically, not so much (I return to this in later posts)).  What do I mean? Well, the organizers invited a very talented group of people (present company excluded, of course) doing a pretty wide cross section of syntactic work. What is very clear is that there is a huge amount of excellent work being done on a wide variety of languages on a wide variety of topics. Typology and morpho-syntax are particularly hot areas of current interest, but syntacticians (in the wide sense meaning those with a good knowledge of syntactic theory and methods) are also heavily involved in “conjunctive” areas such as syntax + language acquisition, syntax + language impairment/disorders, syntax + processing, a.o. As a result, we now know more about the details and overall architectures of more grammars and have better models of how this grammatical knowledge arises and is put to use in more areas than ever before.  Don’t get me wrong: it is clear to all that there is a tremendous amount that we still do not know, even about fundamental issues, but to someone like me, who has been doing this stuff (or at least listening to people who do this stuff) for the last 40+ years, it is clear how much we have learned, and it is very very impressive.

Furthermore, it is also clear that we live in a time where all kinds of syntactic work can be fruitfully pursued. What do I mean by “all”?  Well, there are roughly three kinds of syntactic investigations: (i) there is work on the structure of particular Gs, (ii) there is work on the structure of UGs based on work of particular Gs and (iii) there is work on the structure of FL/UG based on the particulars of UG. (i) aims at careful description of the Gs of a given language (e.g. how does agreement work in L, how are RCs formed? How does binding work?). (ii) aims to find the features that delimit the range of possible Gs in part by distilling out the common features of particular Gs. (iii) aims to simplify UG in part by unifying the principles discovered by (ii) and in part by relating/reducing/unifying these features with more general features of cognition and computation.  All three kinds of work are important and valuable. And though I want to plead specially for (iii) towards the end, I want to be very very very clear that this is NOT because I disvalue (i) or (ii) or that I think that (iii) like work is inherently better than the others. I don’t and never did. My main take-away from Athens is that there has never been a better time to do all three kinds of work. I will return to a discussion of (iii) for I believe the possibility of doing it fruitfully is somewhat of a novelty and the field has not entirely understood how to accommodate it. But I return to this. First the other two.

Let’s start with (i). If your heart gravitates towards descriptive endeavors, there are many many entirely unexplored languages out there waiting for your skills, and there are now well developed methods and paradigms ready for you to apply (and modify). Indeed, one of the obvious advances GG has made has been to provide a remarkably subtle and powerful set of descriptive techniques (based of course on plenty of earlier theory) for uncovering linguistically (i.e. grammatically) significant phenomena. Typologists who fail to avail themselves of this technology are simply going to mis-describe the individual languages they investigate,[1] let alone have nothing to say about the more general issues relating to the variety of structures that natural languages display.[2]

Similarly if your interests are typological you are also in luck. Though there are many more language families to investigate, many have been looked at in great detail and Generative linguists have made a very good start at limning the structural generalizations that cut across them. We now have mapped out more properties of the grammar of case and agreement (at both the specific and general levels) of more languages than ever before. We have even begun to articulate solid mid level generalizations that cut across wide swaths of these languages (and even some language families) enabling a more sophisticated exploration of the parametric options that UG makes available. To me, someone interested in these concerns but not an active participant in the process, the theoretical speculations seemed extremely exciting (especially those linking parameter theory to language change and language acquisition). And though the trading relation between micro vs macro variation has not yet been entirely sorted out (and this impression may be an optimistic appraisal of the discussions I (over)heard) it is pretty clear that there is a thoughtful research agenda about how to proceed to attack these big theoretical issues. So, Generative Syntax (including here morpho-syntax) in this domain is doing very very well. 

Concerning (ii): A very nice outcome of the Athens get-together was the wide consensus regarding what Amy Rose Deal dubbed “Mid-Level Generalizations” (MLG). I have frequently referred to these as the findings of GB, but I think that MLGs is a better moniker for it recognizes that these generalizations are not the exclusive property of any specific research tradition. So though I have tried to indicate that I consider the differences between GB and LFG and HPSG and TAG and… to have been more notational than notional, I adopt ARD’s suggestion that it is better to adopt a more neutral naming convention so as to be more inclusive (does this count as PC?). So from now on, MLGs it is!  At any rate, there is a pretty broad consensus among syntacticians about what these MLGs are (see here for a partial enumeration, in, ahem GB terms). And this consensus (based on the discovery of these MLGs) has made possible a third kind of syntactic investigation, what I would dub pure theoretical syntax (PTS).[3] Now, I don’t want to raise hackles with this term, I just need a way of distinguishing this kind of work from other things we call “theory.” I do not mean to praise this kind of “theory” and demean the other. I really want to just make room for the enterprise mentioned in (iii) by identifying it.

So what is PTS? It is directed at unifying the MLGs. The great example of this in the GB tradition is Chomsky’s unification of Ross’s island effects in “On Wh Movement” (OWM).[4] Chomsky’s project was made feasible by Ross’s discoveries of the PLGs we (after him) call “islands.” Chomsky showed how to treat these apparently disparate configurations as instances of the same underlying system and in the process removed the notion of construction from the fundamental inventory of UG. This theoretical achievement in unification led to the discovery of successive cyclicity effects, to the discovery that adjuncts were different from arguments (both in how they move and how porous they are) and to the discovery of novel locality effects (the ECP and CED in particular).

Someone at the conference (I cannot recall who) mentioned that Chomsky’s work here was apparently un-motivated by empirical concerns. There is a sense in which I believe this to be correct, and one in which it is not. It is incorrect in that Ross’s islands, which were the target of Chomsky’s efforts at unification, are MLGs and so based on a rich set of language specific data (e.g. *Who did you meet someone who likes) which hold in a variety of languages. However, in another sense it was not. In particular, Chomsky did not aim to address novel particular data beyond Ross’s islands. In other words, the achievement in OWM was the unification itself. Chomsky did not further argue that this unification got us novel new data in, say, Hungarian. Of course others went on to show that whatever Chomsky wanted to do the unification had empirical legs. Indeed, the whole successive cyclicity industry starting with Kayne and Pollock on stylistic inversion and proceeding through McCloskey’s work on Irish, Chung’s on Chamorro, Torrego’s on Spanish and many many others was based on this unification. However, Chomsky’s work was theoretical in that its main concern was to provide a theory of Ross’s MLGs and little (sic!) more.

Indeed, one can go a little further here. Chomsky’s unification had an odd consequence in the context of Ross’s work. It proposed a “new” island that Ross himself extensively argued against the existence of. I am talking, of course, about Wh-islands, which Ross found to be highly acceptable, especially if the clausal complement was non-finite. Chomsky’s theory had to include these in his inventory despite Ross’s quite reasonable empirical demurrals (voiced regularly ever since) because they followed from the unification.[5] So, it is arguable (or was at the time), that Chomsky’s unification was less empirically adequate than Ross’s description of islands. Nor was this the only empirical stumble that the unification arguably suffered. It also predicted (at least in its basic form) that who did you read a book about is ungrammatical, which flies in the face of its evident acceptability.  We now know that many of these stumbles led to interesting further research (Rizzi on parameters for example), but it is worth noting that the paper, now a deserved classic, did not emerge without evident empirical problems.

Why is it worth noting this? Because it demonstrates a typical feature of theoretical work; it makes novel connections, leading to new kinds of research/data but often fails to initially (or even ever) cover all of the previously “relevant” data. In other words, unification can incur an apparent empirical cost. Its virtue lies in the conceptual ties it makes, putting things together that look very different and this is a virtue even if some data might be initially (or even permanently) lost. And this historical lesson has a moral: theoretical work, work that in hindsight we consider invaluable, can start out its life empirically hobbled. And we need to understand this if we are to allow it to thrive. We need slightly different measures for evaluating such work. In particular, I suggest that we look to this work more for its ‘ahaa’ effects than for whether it covers the data points that we had presupposed, until its emergence, to be relevant.

Let me make this point a slightly different way. Work like (iii) aims to understand how something is possible not how it is actually. Now, of course to be actual it is useful to be possible. However, many possible things are not actual. That said, it is often the case that we don’t really see how to unify things that look very different, and this is especially true when MLGs are being considered (e.g. case theory really doesn’t look much like binding theory and control does has very different properties from raising). And here is where theory comes in: it aims to develop ways of seeing how two things that look very different might be the same; how might they possibly be connected. I want to further observe that this is not always easy to do.  However, by the nature of the enterprise, the possible often only coarsely fits the actual, at least until empirical tailoring has had a chance to apply. This is why a some empirical indulgence is condign.

So you may be wondering why I got off on this jag in a post about the wonders of the Athens’ conference. The reason is that one of the things that make this period of linguistics such a golden age is that the large budget of MLGs the field seems to recognize makes it ripe for the theoretically ambitious to play their unificational games. And for this work to survive (or even see the light of day) will require some indulgence on the part of my more empirically conscious colleagues. In particular, I believe that  theoretical work will need to evaluated differently (at least in the short and medium run) from the two other kinds of work that I alluded to above, where empirical coverage is reasonably seen as the primary evaluative hurdle.

More specifically, we all want our language particular descriptions and MLGs to be empirically tight (though even fashioning MLGs some indulgence (i.e. tolerance for “exceptions”) is often advisable), elegance be damned. But we want our theories to be simple (i.e. elegant and conceptually integrated and natural), and it is important to recognize that this is a virtue even in the face of empirical leakage. Given that we have entered a period where good theory is possible and desirable, we need to be mindful of this or risk crushing theoretical initiative altogether.[6]

As you may have guessed, part of why I write the last section was because the one thing that I felt was missing at Athens was the realization that this kind of indulgence is now more urgent than ever. Yours truly tried to argue the virtues of making Plato’s Problem (PP) and Darwin’s Problem (DP) central to contemporary research. The reaction, as I saw it (and I might be wrong here), was that such thinking did not really get one very far, that it is possible to do all theoretical work without worrying about these inconclusive problems. It seemed to me that to the degree that PP was acknowledged to be important, it struck me that the consensus was that we should off load acquisition concerns to the professionals in psych (though, of course, they should consult us closely in the process). The general tone seemed to be that eyeballing a proposal for PP compatibility was just self-indulgence, if not worse. The case of DP was even worse. It was taken as too unspecified to even worry about and anyhow general methodological concerns for simplicity and explanation should prove robust enough without having to indulge in pointless evolutionary speculation of the cursory variety available to us.

I actually agree with some version of each of these points. Linguists cannot explore the fine details of PP without indulging in some psychology requiring methods not typically part of the syntactician’s technical armamentarium.[7] And, I agree that right now what we know about evolution is very unlikely to play a substantive role in our theorizing. However, PP and DP serve to vividly bring before the mind two important projects: (i) that the object of study in GG is FL and its fine structure and (ii) that theoretical unification is a virtue in pursuing (i). PP and DP serve to highlight these two features, and as these are often, IMO, lost sight of, this is an excellent thing.

Moreover, at least with PP, it is not correct that we cannot eyeball a proposal to get a sense of whether it will pass platonic muster. In fact, in my experience many of the thoughtful professionals often get their cues regarding hard/interesting problems by first going through simple the PoS logic implicit in a standard syntactic analysis.[8] This simple PP analysis lays the groundwork for more refined considerations. IMO, one of the problems with current syntactic pedagogy is that we don’t teach of our students how to deploy simple PoS reasoning. Why? Well, I think it’s because we don’t actually consider PP that important. Why? Well the most generous answer is that it is assumed that all th work we do already tacitly endorses PP’s basic ideals and so worrying PP to death will not get us very much bang for the buck. Maybe, but being explicit really does make a difference. Explicitly knowing the big issues what the big issues are really is useful. It helps you to think of your work at one remove from the all important details that consume you. And it can even serve, at times, to spur interesting kinds of more specific syntactic speculation. Lastly, it’s the route towards engaging with the larger intellectual community that the Athens conference indicated so many feel detached from.

Personally, I think that the same holds true with DP. I agree that we are not about to use the existing (non-existing) insights from the evolution of cognition and language to ground type (iii) thinking. But, I think that considering the Generative project in DP terms enlarges how we think about the problem. In fact, much more specifically, it was only with the rise of the Minimalist Program (MP) in which DP was highlighted and stressed as PP had been before that the virtues of the unification of the MLGs rose to become a central kind of research project. If you do not go “beyond” explanatory adequacy there is no pressing reason for worrying about how our UGs fit in with other domains of cognition or general features of computation (if indeed they do). PP shoves the learnability problem in our faces and doing so has led us to think constructively about Chomsky Universals and how they might be teased out of our study of Gs. Hopefully, DP will do the same for cleaning up FL/UG: it will, if thought about regularly, make it vivid to us that unifying the modules and seeing how these unified systems might relate to other domains of cognition and computation is something that we should try to tease out of our understanding of our versions of UG. 

I should add that doing this should encourage us to start forcefully re-engaging with the neuro-cognitive-computational sciences (something that syntacticians used to do regularly but not so much anymore). And if we do not do this, IMO, linguistics in general and syntax in particular will not have a bright future. As I said in Athens, if you want to know about the half life of a philological style of linguistics, just consider that the phrase “prospering classics department” is close to being an oxymoron. That way lies extinction. So we need to reengage with these “folks” (ah my first Obamaism) and both PP and DP can act as constant reminders of the links that syntax ought to have with these efforts.

Ok, enough. To conclude: Intellectually, we are in a golden age of linguistics (though we made need to manage this a bit so as to not discourage PTS). However, it also appears that politically things are not so hot. Many of the attendees felt that GG work is under threat of extinction in many places. There was animated discussion about what could be done about this and how to better advertise our accomplishments to both the lay and scientific public. We discussed some of this here, and similar concerns were raised in Athens. However, it is clear that in some places matters are really pretty horrid. This is particularly unfortunate given the intellectual vigor of generative syntax. I will try and say something about this feature in a following post.

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[1] Jason Merchant made this point forcefully and amusingly in Athens.

[2] I suspect that some of the hostility that traditional typology shows towards GG lies in the inchoate appreciation GG has significantly raised the empirical standards for typological research and those not conversant with these methods are failing empirically. In other words, traditional typologists rightly fear that they, not their subject matter, is threatened with obsolescence. To my mind, this is all very positive, but, for obvious reasons, it is politically terrible. Typologists of a certain stripe might be literally fighting for their lives, and this naturally leads to a very hostile attitude towards GG based work.

[3] Yes, I also see the possibility of a PTSD syndrome (pure theoretical syntax disorder).

[4] Continuing a project begun in “Conditions on Transformations” and ending with Barriers.

[5] Though see Sprouse’s work which provides evidence that wh-islands show the same super additivity profile as other islands.

[6] I will likely blog on this again in the near future if all of this sounds kind of cryptic.

[7] Though this is changing rapidly, at least at places like the University of Maryland.

[8] I’d like to thank Jeff Lidz for showing me this in spades. I sat in on his terrific class, the kind of class that every syntactician (especially newly minted syntacticians) should do.