On Starting Something New


I’m in the middle of teaching a graduate research seminar – and also bereft of a book project – so I’ve been thinking a lot about how to start something new.  I asked a few friends a simple question: how do you go from zero (no ideas and no project) to sixty (a book project, with evidence and an argument that makes sense)?  Their generous answers are reprinted below.

This isn’t an idle question.  Writing is easy.  Finding an idea – an idea that can become a book – is hard.



Look for patterns in your own work. What were your favorite courses? What were your best seminar papers? What did you find most exciting to teach? You may find yourself going back to a particular object. Or a similar question. Or a place, time period, or historical event. Or a similar theoretical approach.

Approach question one, but in the reverse. If you could change something about a course you’ve taken, a fields exam, a mode of scholarship, or a critical debate, what would it be? I studied for exams in 19th and early 20th century literature. I was surprised that despite burgeoning criticism on US empire, no one had a sense of Filipina/o responses to the occupation. So that was the first question that led to an archive and dissertation.

Apply for grants, early and often. It’s the best way to construct a clear narrative of what you’re interested, why your work is important, and what you need to do to accomplish it. If you don’t get one, ask for feedback, and try again.

Play the “so what?” game, and see how far you can go with your answers. Try to state the significance of your project in broader terms, and in different ways. How would you describe the importance of your project to a) your advisor; b) the scholar you most admire in your field; c) your best friend; d) your student; e) a complete stranger. Write down your answers, or, if that’s too difficult, record yourself (I developed key moments in my book recording myself on an iPhone while walking my dog).


Always be thinking and asking: so what? If you want the research project to matter and to appeal to a wide range of readers, this question should be considered from the very beginning–even as you ponder, imagine, and conceptualize the topic.

Always be thinking about sources: If a topic or problem or question interests you, how will you explore and examine it? What materials will you use? Will you be able to access the archives, visual texts, etc. that you need to develop a full-scale research project?

Always be thinking about methods: What approach will you take? How will your approach differ from other scholarly works on the topic? What can you learn from other scholars whom you admire? What sources and methods do they use?

What truly interests and inspires you? What will hold your attention and excite your imagination for the duration of the research and writing?


Coming up with a good project is always the hardest part. BUT, coursework and comprehensive field exams give grad students a great sense of current scholarship–really, it will be hard to EVER read this widely again. So, look for opportunities. I dislike the phrase “gaps in the historiography”; it’s too trivializing. Looking for big gaping holes, reorientations, possibilities to connect two or more disparate historiographies. Think of something manageable enough for a dissertation, but significant to develop into a book manuscript that will wow multiple audiences.

Related to no. 1, consider special skills that you already have or can develop in graduate school that will enhance your ability to write an authoritative work. Here, I’m mostly thinking about foreign language skills or interdisciplinary training, but this could also be experiential knowledge or previous professional experience.

This is pretty obvious, but read relevant scholarship, for argument, method, and sources. This will be especially helpful as you develop a bibliography. In consultant with your advisor or other experienced mentors, consider what archives might have been overlooked by previous scholarship. Digital media is great, but keep in mind that there are millions of undigitized collections in the US. It’s worthwhile to contact potentially relevant archives. If records have been microfilmed, you might be able to get reels copied or sent to your home institution through interlibrary loan, which saves a lot of time and money.

Before you even begin to do research, develop a plan for note-taking and data management. Do not write or store notes in a haphazard fashion. Try out a couple of different software options; I like Filemaker Pro. This will take some time on the front end, but it is so worth it.


Let the sources speak, let them school you.  In the early stages, if you’re using your archive to document what you already think, you’re on the wrong track.  That part comes much later.  At the outset, you are serving the sources, not they you.

Read broadly, be playful, relish the odd juxtaposition, be alert.  Your best ideas are likely to be kindled by the spark created by some chance encounter with this text on Monday and that text on Tuesday.

Pose some impossibly difficult puzzle for yourself–a kind of sub-question within your research question–and never let go of the promise of solving it.

Know thyself.  Get to know and understand your own work rhythms, and maximize your usefulness (to yourself) on any given day.  Some days we’re just brain dead–but lucky for us, there’s plenty of work (doing footnotes, bibliographic work, data entry, etc.) that can be accomplished while brain dead.  Other days we’re sharp and quick and brimming with insight–learn to recognize those days upon waking, and tackle the kinds of tasks that most require that version of yourself.


A good project builds on previous knowledge, older passions, longer interests, good luck and better friends.  It can’t be made out of whole cloth overnight or even in a year.  It can’t be fabricated on demand.  Research is not ‘just in time’.

But any project, good or merely workmanlike, has to start with either a problem within the literature or a document of some kind.  If the former (and that problem can be something you don’t like, a lacuna, whatever) then the problem drives the archival direction.  You have to answer the question “If I want to think about X, where do I go look?” If the latter, then the document (whatever it is – piece of paper, image, event) raises the questions for you, eventually.  Its internal logic pushes the historiographic and ultimately additional archival agenda.

I don’t think that you ever have a complete argument until the project is finished (remember how often you rewrite intros?) but you have to try to have one, if only to abandon it.  But that argument has to come directly from the problem or the evidence.  In other words, it has come directly from the historiography or directly from the sources. Otherwise, it’s just fluff.


Whatever project you take up, it must be one that really engages you. You have to follow your instincts and your heart. Also, just read read read until you find a topic that you just can’t stop reading about.

I always try to ask myself what is a politically important project at this time. Not that our books can change the world, but they may get people to look at the world differently.


This is *all* good advice.  Read it, chew on it, own it.

It reminds me, to be frank, of how I started my own dissertation topic. I’d written an undergraduate thesis on the Irish Renaissance.  In the course of doing that, I’d read everything on the period of time between Douglas Hyde and the Easter Rising.  (Yes, obscure references).  I’d written an essay on the literature on cultural nationalism, on race and nation. In my first semester of graduate school, I read the epigraph to David Lewis’s When Harlem Was in Vogue, a quote from Alain Locke’s The New Negro on the the comparability of Harlem and Dublin. Deciding that I wanted to understand *why* Locke thought this comparison made sense, I read 15 years of The Crisis, The Messenger, and The Crusader.  I found a ton of essays and reflections on Ireland and literary production between 1915 and 1930.  Then I went through the biographies of Claude McKay, W.E.B. Du Bois, Locke, etc.

I started to look through the more general newspapers of the day.  I followed footnotes.  I copied everything.  Opened every file cabinet (not every record is digitized, and *none* were digitized in 1994).  This led me to other things and other people, not all of them related to literature.  It let me to Garvey, and to Madison Grant. I came, as time moved on, to believe that the story of *connection* was actually far less interesting (and important) than the increasing metaphorical distance of Ireland and Harlem. Why, I asked, were there so many references to Ireland in 1915, or 1925, but so few in 1930?

Answering this question took me even further away from that original undergraduate thesis. Convinced that the answer had something to do with race, I went to the library, dug out all of the old scientific racist texts of the day, and tried to figure out what race meant in 1915, 1925, etc. I also, once again, looked to understand the field – to know what had been written on this topic and by whom.

Then, in a moment of extraordinary clarity, I got it.  I knew.  I could feel it in my bones.  I found that an Irish Race Convention had been held in NYC in 1916 – the same year as the Easter Rising – and the language of the convention suggested that Irish Americans were “white” in a way that the Irish in Ireland were not.

Only then, really, did I know exactly what I was arguing. Of course, by then I’d written an undergraduate thesis, an MA thesis, and several seminar papers, none of which exactly matched my project, but all that writing was about refinement and creative speculation.  Not a word of my MA thesis or my undergraduate thesis appears in the dissertation or the book that resulted.  And yet, all the effort was worth it.

The research phase was intense.  In the library or the archives every day (despite classes).  I was on the phone with archivists, writing letters, sending off FOIA requests, photocopying everything, or scribbling notes to myself.  I travelled up and down the coast, routinely.  By train or by borrowed car.  Some days I’d find something. Some days, not.

This entire narrative of the discovery and reinvention and revision of the idea took three years.

So, then, strap in.  There is a lot of introspection and lot of questing. Relentless acquisition of materials, dogged bibliographic work, and the constant need to lay out an argument – even a half-assed one. So, then, you should get started!  Because all the misfires, and false starts, and efforts to force the issue are actually a part of the process.  We dig and sift; we ask questions and then we ask better questions; we keep at it.

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