For researchers, history is a thing we do. It is an activity, a handling of old books, a building seen from the vantage point of its past. 

As working historians, we submerge ourselves in the cultural pools of an earlier time. Those who write about Isambard Kingdom Brunel know, too, the streets of Victorian London, “firebox” and “tender” and all the terminology of the steam train, the timeline of the Crimean War, what one might eat with tea (subdivided by social class), when tea might be taken (subdivided by social class), perhaps even the fashionable eccentricities of Beau Brummel in exile or the conduct of the first Opium War in China. In short, they know all the collected scientific, cultural, and political knowledge of the time and place inhabited by Brunel, their chief subject of study. 

Scholars who work on the Tokugawa shogunate have likely visited Dejima Island, illustrated here in a woodblock print. Utagawa Hiroshige II/British Museum/CC BY-NC-SA 4.0. Image cropped.

Scholars who work on Japan’s Tokugawa shogunate have seen Kabuki theater, visited Dejima Island and the Edo castle, perhaps purchased a print showing Ainu hunters in bearskins or a room screen depicting alternate attendance at the Tokugawa court. In their lives as in their work, they have surrounded themselves with the material things of a bygone past. We know our subjects well precisely because we have enough historical perspective to partially inhabit a foreign time and place in our mind’s eye—and, if we’re lucky, in the real world too.

One way we come to know these detailed worlds is through the secondary literature, which we read for graduate qualifying exams, for professional development, and out of pure cussed interest. But studying the secondary literature is not really doing history. Our most substantive work is often the most intimate: watching newsreels, analyzing objects, handling documents. Historical discovery—in an archive, in a museum, or, for that matter, on the streets of London or Tokyo—is the primary job requirement and the greatest pleasure of the working historian.

This is rarely how we frame the “research process.” In writing conference abstracts and applying for funding—indeed, in structuring our own thought processes about books and articles to come—we propose a project before we’ve drunk deeply at the well of primary source material. I will argue, we say, that internecine conflict brought down the Aztec empire; send me to find documentary evidence. There is more to be said about rickshaws in colonial Singapore; bring me to your institution to say it (and between now and then I shall figure out what it is that still needs saying).

What happens if the hoped-for evidence proves elusive or simply doesn’t exist?

Yet we are all familiar with the actual course of historical research. We may say we will work on “mass movements in Qing China,” but until we sift through the archival materials, this topic is nothing more than a broad suggestion. Research at its most effective and delightful is a journey of unexpected discovery. We don’t really form our arguments—or even discover our true research subjects—until we’ve sat with our documents and found the interesting truths within them. That’s how Karl Jacoby could turn “a history of the National Parks” into Crimes Against Nature, a compelling account of the way that early American conservationism criminalized local land use so that outsiders might enjoy the land in the “right” way. It’s also how we got Philip A. Kuhn’s Soulstealers, a riveting work about haircutting, sorcery, and mass hysteria in 18th-century China. Both books are memorable, detailed, and thought-provoking. I would be immensely proud to have recommended either project to my students.

But how could I have? Nobody knew there was such a culturally rich pigtail-cutting panic until Kuhn sat down and found it. I might have suggested looking at superstition in Qing China, but the only way to come up with Kuhn’s specific project would have been to notice references to the panic in the source material. The only way to do that would have been to read a wide variety of sources from the relevant time and place.

In fact, it turns out that “good research technique” is simply setting oneself up for serendipitous historical discovery. Practically, this requires finding the time and money to examine old objects and texts for as long as it takes to uncover a story that is shocking, important, unexpected, or just plain interesting. It means walking the streets of our chosen place and immersing ourselves in the artifacts of our chosen time. It also means giving our students the luxury to do something similar before they’ve settled on a narrow research topic.

This is rarely what we tell our students—or ourselves. Convinced that archival research is intimidating and hard, we instead write proposals, fine-tune arguments, and review the secondary literature, all before stepping foot in a relevant archive. We tell our protégés to hand in thesis statements and compose annotated bibliographies first, long before we ask them to look at any primary source material. We pronounce research projects “promising,” “too grand,” “unlikely,” or “compelling” before students have even begun to look for real evidence of their claims. We routinely suggest theoretical frameworks for papers that are not yet written, based on documents that have not yet been found. And we ask graduate students for detailed prospectuses while pretending that they are anything more than well-informed fictions. In short, we ask our students and ourselves for thoughtful historical analyses before we’ve yet found anything of substance to analyze.

The actual course of historical research often relies more on luck and serendipity than we may like to admit. Thomas Rolandson/Metropolitan Museum of Art/Public Domain. Image cropped.

There is something deceitful in this. If a chemist determined the outcome of an experiment first, and only then looked at experimental data (massaging it as necessary to fit a preordained narrative), we would call that fraud, or at least incompetence. Yet in our own field this is practically the norm: we promote a project because it will “completely change our understanding of race relations in antebellum New Orleans”—and then, having received the necessary time and money to pursue research on the basis of this routine fabrication, we finally dig down into the source material that will prove our predetermined point. This mis-ordering of things is so institutionalized that we positively force the process onto our doctoral students, invariably requiring a complete outline of the dissertation before ever letting them loose to do the basic research that supports it.

What happens if the hoped-for evidence proves elusive or simply doesn’t exist? What if the thesis is wrong and the theoretical framework inappropriate? Some historians fudge the project anyway and produce embarrassing work. But most of us know that our initial proposals were disingenuous, that our firm promises were really just malleable suggestions, that the sources never tell us exactly what we expect them to. In response, we breezily shift our narratives to match the existing documents. Good history is still, in fact, grounded in the sources—and there is plenty of good history about.

But why not be a little more honest about the process, with ourselves and especially with our students? It’s reasonable to have some idea of a broad topic to pursue through the primary source material (though it’s also reasonable, sometimes, just to read anything that looks interesting), but let us stop pretending we know ahead of time what our book will argue or what our reading will turn up.

And let us candidly admit that the pleasures of a historian’s work are intimately tied to quality research, that walking foreign streets, hanging around mosques (to study Sufism), or swimming the Dardanelles (to study Byron), snooping in outdated personal diaries and gawping at anachronistic (and horrifying) ads—“Is it always illegal to kill a woman?” asks one example from 1947, in an attempt to sell a postage meter—this is the very stuff of good historical writing. Interesting tidbits turn up when you let them, and they naturally become the basis for interesting books.

The funny thing about doing history in this way—history by text and by thing first, archive before argument—is that it is, in fact, so very easy. Doing research like this requires, perhaps, a shift in perspective; it requires time and receptivity to the serendipitous; but it makes history immersive, and it makes writing fun. For any curious soul, an aimless stint in the archives is the simplest, most satisfying way there is to make historical inquiry intellectually honest and enormously enjoyable.