The Holy Grail: In Pursuit of the Dissertation ProposalMichael Watts, Institute of International Studies, UC BerkeleyTo Page 1 of this essay Page 3 of 5 Primary Objectives and ParametersI am making a number of assumptions and exhibit a certain conceit in outlining the primary concerns that should inform the construction of a research proposal (as an exemplar of research design). I do this because I am assuming that most of you are in the process of doing this or thinking about it for your dissertation projects. And this is of course a formative moment in your training. I am assuming that most of you will conduct something like fieldwork and to do this you'll need to raise research grants and hence will need a research proposal (as indeed you will for your own internal departmental and disciplinary needs). So I am going to walk through the research proposal as a way of flagging some difficulties and some issues that we all need to think about -- because the process IS so difficult, demanding and drawn out. I'll do this by telling some stories about my own experiences conducting research in West Africa (Nigeria/Senegambia), in South India (Kerala) and California (the Sacramento valley). While my interests are eclectic I've had a particular interest in peasants, in rural transformation, in social movements, and in a variety of agrarian issues including household dynamics and gender questions. These interests will shape what I have to say. Let me immediately say that, aside from advice given on the research design page, I cannot possibly deal in any detail with all of the problems of research design as such: this is not an occasion for a crash course in designing surveys, training assistants, thinking about respondent bias, working through the problems of evidence, or a genealogy of hermeneutic theory. Neither is this a treatise challenging or even questioning the theoretical or disciplinary approaches you may have adopted as an economist, anthropologist or historian. Of course I have my own biases and for purposes of clarity, I might as well make them explicit now. The first is to take seriously the notion of considering a variety of methodological approaches through which one can approach a research problem -- to raise the idea of multiple methods as something I would encourage you to look into. And second to emphasize some of the key moments in research design and proposal writing (for example linking evidence to a particular question) as a way of driving home the point that you need to be as clear, as self conscious and as explicit as you can be in explaining HOW you will conduct a project (you've arrived in rural Idaho to study the militias with your truck and gun rack, now what are you going to do?). A good research design makes your research life in the barrios of Los Angeles or the NGOs of Bogota much easier. In this sense I suppose a research proposal is a sort of security blanket given all of the unknowns associated with doing fieldwork and collecting data. And in this regard a proposal by definition pushes you to construct something more than a fishing expedition -- "I'll go and poke around and see what is there". A good research proposal provides you with an identifiable problem, a tentative hypothesis or proposition, a road map of necessary evidences, and at least some ideas about how and where that evidence can be located and generated. To leave the warm and cuddly academic groves of Berkeley or Cambridge for the field without having thought carefully through all such matters is to invite catastrophe, or at least more confusion and anxiety -- which is where most people are when they start thinking about a dissertation topic. We can all do with less of this I presume. A proposal, then, has the merit of identifying a hypothesis or a hunch or an argument or a paradox to be explained. How else could one begin? There is something worse than a bad hypothesis, idea, or proposition, and that is no hypothesis (idea/proposition) at all. Let me start here with a brief definition of a research proposal: it is a text that links in a more or less formal way theory, method and evidence. More elaborately we could say that a question or problem is theorized in such a way that it generates evidentiary needs on the one side, and a series of means (methods) for generating, locating and assessing evidence on the other. How these pieces are articulated -- for example through a comparative study of three country cases using large-n samples -- represents what I would call the research design. As I have already implied, differing funders impose different requirements, needs and organizational templates; disciplines may vary in their institutional culture as regards how formal such proposals should be. The language of hypothesis testing may seem remote in some disciplines or outright anachronistic. But all of the social sciences and humanities have to grapple with the intellectual and practical problems of conducting independent research: namely that some evidence is theory laden, that some questions have particular evidentiary demands, that some methods may not be appropriate for some questions and so on. I am assuming that we are all in the business of writing narratives of differing sorts that sustain arguments, proposition, that provide differing sorts of explanations of social life. Put in this way it all sounds straightforward and perhaps pedestrian. But of course it isn't. It's the most difficult thing you will do (yes, even more difficult that writing the dissertation). There are very good reasons why in their book, In Pursuit of a Ph.D., Bowen and Rudenstein emphasize 'anxiety', 'paralysis' in their account of the genesis of a research project. Now we can talk about why this is the case: the process is often loosely institutionalized, it is compounded by bad advising and poor training, and it certainly is made no easier by the profound arbitrariness of arriving at a topic. How can something predicated on logic and reason be so illogical and unreasonable? Why on earth did I choose beer-brewing co-operatives in Burundi and not national dental organizations in Des Moines? There really is no avoiding this; selecting and designing a research project is hard, exhausting and unsettling; it is also thrilling, exhilarating and exciting. But the difficulty of designing and writing a good research proposal is unquestionably compounded by the lateness to which students come to it. Highly structured coursework, and the impending nightmares of qualifying exams and so on, typically make the planning horizon the immediate and the short term rather than three years down the way when you are stepping into the field. You cannot start thinking about your research project too early for a number of reasons. First of all the identification of a place and problem -- household dynamics in northern Kenya -- carries with it enormous implications as regards the skill-set that you need to acquire: language, area studies, large scale social survey design and so on -- all aside from the typical theory courses that are the very stuff of graduate formation. And I think that starting as early as you can is key so that you build into your formation not simply the need to know fields, but a series of integrated needs to conduct a project (it's sort of difficult to pick up Chinese language late in the game). Second, the process of writing a research proposal is profoundly recursive. Your proposal can change radically in the course of being put through 6-10 different drafts and through soliciting feedback from your committee, friends and peers. To expect that this process to take anything less than six months is myopic (see the timeline). Thirdly, the practical "start-up" demands of conducting a project, particularly in a foreign location, is time consuming. There is ideally a need to make regular pre-dissertation visits to establish scholarly contacts, affiliations and academic networks; there is a need to scout out possible field research sites and perhaps improve language skills; and most of all a desire to test one's primitive ideas on the local scholars who are familiar with the subject at hand. To ensure such pre-planning presupposes time and flexibility and such practical requirements can only be laboriously constructed over time. The great value of a research proposal carefully crafted early on in one's graduate training is that is acts as a sort of foundation upon which a program of work can be constructed; that is to say is provides an intellectual and methodological roadmap for you. To determine, for example, that you wish to study the relations between local Ecuadorian environmental NGOs and US-based transnational environmental organizations that fund them -- with the idea that foreign transnational organizations shapes the agendas and practices of local green groups in specific ways -- generates immediate demands for graduate training, to put yourself in other words in the best possible position to both secure funding for the project and to accomplish a well-organized and effective field project. Quite specifically, one might anticipate the student wishing to conduct this project identifying the following areas and fields as (minimally) necessary for the project:
Most of you will be in the business producing a 10-15 page research prospectus for funding purposes -- and this will provide the template for my discussion -- that includes sections on theory, method, design, and plan of work. There is no one way, one narrative structure or proposal organization, to link problem, theory, method, and evidence but I would say that there are some generic demands ("principles") that any compelling proposal must conform to:
By transparency, I mean that the logic by which theory, evidence, and method are connected must be explicit and obvious. This implies two things. One is that the reader must be ale to understand how you are designing your project and what your thinking has been about the ways in which you will approach your problem or question. Hence if you are proposing to study the nature of social and economic differentiation among peasants in northern Thailand in relation to the neo-liberal reforms then it must be clear how you are going to measure differentiation (what criteria, how many people), the means by which you will collect data appropriate to the measures you will use, and the measures you are taking to ensure that you can separate out the effects of the neo-liberal reforms on differentiation from other 'causal' forces (say farming ability, household size. Transparency then is simply the legibility of the process by which you construct a problem, pose a hypothesis or question, and explore the evidentiary needs of your research and the validity of your results (see more at research design). Clarity refers to the need to strike a balance between the specialized lexicon of theory and discipline and the need to be able to "walk-through" a proposal in a way that the reader fully and easily grasps the internal logic of the study. Clarity does not demand a sort of linguistic or expressive dilution but rather highlights the dangers of obfuscation (what exactly is this proposal suggesting?), ambiguity and a lack of sufficient information (what exactly is the author proposing to do in the name of ethnographic fieldwork or "hanging out" in the village?). Methodological precision asserts the importance of focussing on the "how" question( see also concepts and terminology and style pages. This is typically the part of the proposal that funders scrutinize with particular care: and it is often that part of the proposal which students fudge or gloss over the knotty problems of evidence. How large a sample, how will the sample be selected, is representativity an issue, how can one confidently assume that data on credit will be reliable, how exactly can evidence be collected on state espionage? The key point I wish to make here is that there are lots of exciting and creative and innovative questions that we as scholars can pose but have evidentiary demands that cannot be met (i.e. they presuppose that we have access to the internal records of large transnational oil companies). This may sound perfectly obvious in the abstract but all proposals must be able to convince a reader that reliable, valid and quality information appropriate to the question can be collected under the conditions of fieldwork in an ethically responsible way. Theoretical expectations is perhaps counter-intuitive and somewhat controversial. It is the idea that the ways in which you are couching your problem -- the theoretical tradition in which you have chosen to operate -- provides something more than a context for your research; it is theoretical precisely because it leads us to expect certain outcomes or specific hypotheses (see page on theory. One can argue over the extent to which this is predictive or overdetermines the research process. But theory must be useful -- it is a sort of toolbox that you have decided to deploy -- and to this extent it leads the researcher to a hunch about what is going on. The hunch may be wrong -- your research will discover this -- but a proposal must contain such a hunch and, through the principles outlined, convince a reader why your proposition is plausible and worth exploring. Do-ability highlights practical considerations that will shape the "fundability" of the proposal -- and indeed your ability to pull off the project! It is one thing to have a theoretically brilliant and well-designed study of financial markets and transnational capital flows; it is another to have the time, money and resources to analyze vast data sets and to complete the analysis in several months. In adhering to these principles the reader should be fully able to appreciate the nature of the problem, how the researcher is approaching his/her study, and how it is to be conducted (when, where, how). In this way, a good proposal offers the reader a clear answer to the following three questions:
All of these questions are in some measure shaped by field, by discipline and so on (validity for a rational choice analysis of collective action may be rather different from an ethnographic analysis of a social movement). But you must always keep them in mind because they represent one important set of criteria by which your project will be assessed and evaluated. A this point let me say a word about the construction of a proposal in relation to the reader, or more precisely those scholars (reviewers, screener, selection committees) and its assessment. I have already stressed the competitiveness of the selection process and its political economy for want of a better phrase. One can of course become almost immobilized by the prospect of second-guessing what funders "need" or are looking for. Indeed there are obvious intellectual and professional costs of "donor-driven research". Nevertheless, there are a number of narrative devices, "tricks of the trade", and obvious "dos and don'ts" that should not be overlooked.
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