A longtime concern of mine, never voiced until now, is the feeling I get that the field of syntax is not very committed to foundational work.
Simplifying a lot, the typical linguistics research agenda runs something like the following:
Standard Paradigm for Syntactic Research
1.
Identify some interesting dataset from some language.
2.
Adopt a specific set of syntactic assumptions (the theory).
3.
Show how to account for the dataset within the assumptions.
4.
If needed, tweak the assumptions to account for the dataset.
5.
Show how your account is better than other possible accounts within the theory.
6.
Show how the tweaking does not lead to inaccurate empirical predications.
This is the kind of work that linguists are by far the most comfortable with. Any change in the theory should be directly related to the data being analyzed. If a new theory is proposed, it should be evaluated on the basis of its success in handling data. On this way of looking at things, the link between data and theory is very tight.
I personally have no problem with this kind of work. I have engaged in such analyses many times in my life. But foundational work is of a different character.
By foundational work, I mean work at the deepest level, analyzing the most basic assumptions of the field. Can the assumptions be understood precisely with no handwaving? What is the logical relationship between the assumptions? Can certain assumptions be eliminated? Are there implicit assumptions in the current theory that need to be brought out? What is the motivation for the assumptions over other assumptions, which may be more or less equivalent in terms of empirical coverage? Why is linguistic theory the way it is (instead of some other logically conceivable way)?
Foundational work is often driven by the desire to understand the underlying order of a formal system, the symmetries and asymmetries, the hidden connections between seemingly unrelated assumptions, and interesting unexpected explanations for why the system is the way it is. The belief is that the human faculty for language is governed by simple and elegant principles, and it is our job as theoreticians to try to uncover them.
The research agenda runs roughly like this:
Foundational Paradigm for Syntactic Researc
1.
Identify a syntactic theory.
2.
Identify a foundational issue within that theory (related to the questions posed above).
3.
Try to gain insight into that foundational issue.
My characterization of these two paradigms is overly simplistic. Of course, there may be empirical consequences of foundational work. And there are degrees along the scale defined by the two poles above. There is not always a clear-cut distinction.
But the value of the foundational work may just be to gain insight into how the theory works. One of the most interesting papers of this kind was Sam Epstein’s paper on c-command ‘Un Principled Syntax and the Derivation of Syntactic Relations’, which subjected a fundamental notion (c-command) to close conceptual scrutiny, asking questions about why c-command was defined the way it is (instead of some other way), and answering those questions in terms of a derivational model of syntax. My paper on ‘Eliminating Labels’(and related work by Daniel Seely) was written in a similar spirit, proposing that the syntactic notion of label is unnecessary in syntactic theory.
Through many personal experiences, I know that it is very hard to get colleagues and students to engage in thinking about foundational issues. When you start asking foundational questions, people’s eyes gloss over, and they start yawning. In fact, some people even seem to be uncomfortable with foundational work. For example, one reviewer felt obliged to add the following comment to their review of one of my foundational papers:
“I cannot say that this is the kind of paper I care much for. It carefully and clearly discusses an issue that leaves me entirely cold. “
This comment was not about the arguments of the paper. It was about the topic itself. According to the reviewer, the issue left them cold, with the implication that doing such work was not important, and maybe even misguided. I have had similar experiences not just with reviewers, but in many in other areas of academic life (e.g., course enrollment, hiring decisions, selection of colloquium speakers, etc.).
If I am right, it raises the question of why? Why is the field of linguistics so apathetic to foundational work? I think there are a few reasons.
First, foundational work takes a lot of time and effort, and the payoff is uncertain. The question is what counts as progress. You may think for years and years about the ‘copy versus repetition’ distinction or about the definition of c-command or about the nature of workspaces without resolving the issues, even though in the end you have a much deeper understanding. Does that count as progress? Can you write it up and publish it? Does it count as currency in the academic monetary system?
Second, foundational work does not fit into the standard syntactic paradigm, which is the paradigm everybody recognizes as valuable. Meditating on the definition of c-command seems less satisfactory than showing that a particular definition of Agree accounts for more data than a different definition of Agree. Linking to data is a certain way to measure progress. If the work is not tightly linked to data, it may not be clear what the progress is.
Third, the field is beset by what I can call ‘the busy hands syndrome’. If a theory provides many opportunities for analysis of various kinds, including interesting new mechanisms to play with in different ways, it attracts people. It supplies with them things to do. But foundational work does not have this character. Rather, one focuses on some conceptual issue to try to gain insight into it.
Fourth, and related to the previous points, from the standpoint of a graduate student, the question is what kind of work will they be able to present at conferences and publish before they enter the job market. Committing to foundational work might not do the trick, if the rest of the field feels that it is not important.
To end this blog post, we can ask the question of how foundational work should fit into the future of the study of natural language syntax. If everybody is chasing data, competing on the best definition of Agree, or the scope of the impoverishment operation, or the number of projections in the left periphery, are we really making progress understanding the fundamental principles at play in syntactic theory?
I am definitely not claiming that such empirical work is unimportant. Far from it, it is the bread and butter of syntactic theory. But contrary to popular belief in our field, having an empirically adequate theory does not mean that it is a good theory. If your theory provides easy explanations for X, it does not necessarily add to the value of your theory. This is why, years ago, Chomsky introduced the notion of ‘explanatory adequacy’, in order to go beyond the clever organization of data into rules.
The purpose of foundational work is to push us out of our comfort zone with the goal of helping us to find deeper explanations for syntactic phenomena.
