[The following is the text of a talk I prepared for a panel discussion about authoring digital scholarship for history with Adeline Koh, Lauren Tilton, Yoni Appelbaum, and Ed Ayers at the 2015 American Historical Association Conference.]
I’d like to start with a blog post that was written almost seven years ago now, titled “Sunset for Ideology, Sunrise for Methodology?” In it, Tom Scheinfeldt argued that the rise of digital history represented a disciplinary shift away from big ideas about ideology or theory and towards a focus on “forging new tools, methods, materials, techniques, and modes or work.” Tom’s post was a big reason why I applied to graduate school. I found this methodological turn thrilling – the idea that tools like GIS, text mining, and network analysis could revolutionize how we study history. Seven years later the digital turn has, in fact, revolutionized how we study history. Public history has unequivocally led the charge, using innovative approaches to archiving, exhibiting, and presenting the past in order to engage a wider public. Other historians have built powerful digital tools, explored alternative publication models, and generated online resources to use in the classroom.
But there is one area in which digital history has lagged behind: academic scholarship. To be clear: I’m intentionally using “academic scholarship” in its traditional, hidebound sense of marshaling evidence to make original, explicit arguments. This is an artificial distinction in obvious ways. One of digital history’s major contributions has, in fact, been to expand the disciplinary definition of scholarship to include things like databases, tools, and archival projects. The scholarship tent has gotten bigger, and that’s a good thing. Nevertheless there is still an important place inside that tent for using digital methods specifically to advance scholarly claims and arguments about the past.
In terms of argument-driven scholarship, digital history has over-promised and under-delivered. It’s not that historians aren’t using digital tools to make new arguments about the past. It’s that there is a fundamental imbalance between the proliferation of digital history workshops, courses, grants, institutes, centers, and labs over the past decade, and the impact this has had in terms of generating scholarly claims and interpretations. The digital wave has crashed headlong into many corners of the discipline. Argument-driven scholarship has largely not been one of them.
There are many reasons for this imbalance, including the desire to reach a wider audience beyond the academy, the investment in collection and curation needed for electronic sources, or the open-ended nature of big digital projects. All of these are laudable. But there is another, more problematic, reason for the comparative inattention to scholarly arguments: digital historians have a love affair with methodology. We are infatuated with the power of digital tools and techniques to do things that humans cannot, such as dynamically mapping thousands of geo-historical data points. The argumentative payoffs of these methodologies are always just over the horizon, floating in the tantalizing ether of potential and possibility. At times we exhibit more interest in developing new methods than in applying them, and in touting the promise of digital history scholarship rather than its results.
What I’m going to do in the remaining time is to use two examples from my own work to try and concretize this imbalance between methods and results. The first example is a blog post I wrote in 2010. At the time I was analyzing the diary of an eighteenth-century Maine midwife named Martha Ballard, made famous by Laurel Ulrich’s prize-winning A Midwife’s Tale. The blog post described how I used a process called topic modeling to analyze about 10,000 diary entries written by Martha Ballard between 1785 and 1812. To grossly oversimplify, topic modeling is a technique that automatically generates groups of words more likely to appear with each other in the same documents (in this case, diary entries). So, for instance, the technique grouped the following words together:
gardin sett worked clear beens corn warm planted matters cucumbers gatherd potatoes plants ou sowd door squash wed seeds
As a human reader it’s pretty clear that these are words about gardening. Once I generated this topic, I could track it across all 10,000 entries. When I mashed twenty-seven years together, it produced this beautiful thumbprint of a New England growing season.
Interest in topic modeling took off right around the time that I wrote this post, and pretty soon it started getting referenced again and again in digital humanities circles. Four and a half years later, it has been viewed more than ten thousand times and been assigned on the syllabi of at least twenty different courses. It’s gotten cited in books, journal articles, conference presentations, grant applications, government reports, white papers, and, of course, other blogs. It is, without a doubt, the single most widely read piece of historical writing I have ever produced. But guess what? Outside of the method, there isn’t anything new or revelatory in it. The post doesn’t make an original argument and it doesn’t further our understanding of women’s history, colonial New England, or the history of medicine. It largely shows us things we already know about the past – like the fact that people in Maine didn’t plant beans in January.
People seized on this blog post not because of its historical contributions, but because of its methodological contributions. It was like a magic trick, showing how topic modeling could ingest ten thousand diary entries and, in a matter of seconds, tell you what the major themes were in those entries and track them over time, all without knowing the meaning of a single word. The post made people excited for what topic modeling could do, not necessarily what it did do; the methodology’s potential, not its results.
About four years after I published my blog post on Martha Ballard, I published a very different piece of writing. This was an article that appeared in last June’s issue of the Journal of American History, the first digital history research article published by the journal. In many ways it was a traditional research article, one that followed the journal’s standard peer review process and advanced an original argument about American history. But the key distinction was that I made my argument using computational techniques.
The starting premise for my argument was that the late nineteenth-century United States has typically been portrayed as a period of integration and incorporation. Think of the growth of railroad and telegraph networks, or the rise of massive corporations like Standard Oil. In nineteenth-century parlance: “the annihilation of time and space.” This existing interpretation of the period hinges on geography – the idea that the scale of locality and region were getting subsumed under the scale of nation and system. I was interested in how these integrative forces actually played out in the way people may have envisioned the geography of the nation.
So I looked at a newspaper printed in Houston, Texas, during the 1890s and wrote a computer script that counted the number of times the paper mentioned different cities or states. In effect, how one newspaper crafted an imagined geography of the nation. What I found was that instead of creating a standardized, nationalized view of the world we might expect, the newspaper produced space in ways that centered on the scale of region far more than nation. It remained overwhelmingly focused on the immediate sphere of Texas, and even more surprisingly, on the American Midwest. Places like Kansas City, Chicago, and St. Louis were far more prevalent than I was expecting, and from this newspaper’s perspective Houston was more of a midwestern city than a southern one.
I would have never seen these patterns without a computer. And in trying to account for this pattern I realized that, while historians might enjoy reading stuff like this…
…newspapers often look a lot more like this:
All of this really boring stuff – commodity prices, freight rates, railroad timetables, classified ads – made up a shockingly large percentage of content. Once you include the boring stuff, you get a much different view of the world from Houston in the 1890s. I ended up arguing that it was precisely this fragmentary, mundane, and overlooked content that explained the dominance of regional geography over national geography. I never would have been able to make this argument without a computer.
The article offers a new interpretation about the production of space and the relationship between region and nation. It issues a challenge to a long-standing historical narrative about integration and incorporation in the nineteenth-century United States. By publishing it in the Journal of American History, with all of the limitations of a traditional print journal, I was trying to reach a different audience from the one who read my blog post on topic modeling and Martha Ballard. I wanted to show a broader swath of historians that digital history was more than simply using technology for the sake of technology. Digital tools didn’t just have the potential to advance our understanding of American history – they actually did advance our understanding of American history.
To that end, I published an online component that charted the article’s digital approach and presented a series of interactive maps. But in emphasizing the methodology of my project I ended up shifting the focus away from its historical contributions. In the feedback and conversations I’ve had about the article since its publication, the vast majority of attention has focused on the method rather than the result: How did you select place-names? Why didn’t you differentiate between articles and advertisements? Can it be replicated for other sources? These are all important questions, but they skip right past the arguments that I’m making about the production of space in the late nineteenth century. In short: the method, not the result.
I ended my article with a familiar clarion call:
Technology opens potentially transformative avenues for historical discovery, but without a stronger appetite for experimentation those opportunities will go unrealized. The future of the discipline rests in large part on integrating new methods with conventional ones to redefine the limits and possibilities of how we understand the past.
This is the rhetorical style of digital history. While reading through conference program I was struck by just how many abstracts about digital history used the words “potential,” “promise,” “possibilities,” or in the case of our own panel, “opportunities.” In some ways 2015 doesn’t feel that different from 2008, when Tom Scheinfeldt wrote about the sunrise of methodology and the Journal of American History published a roundtable titled “The Promise of Digital History.” I think this is telling. Academic scholarship’s engagement with digital history seems to operate in a perpetual future tense. I’ve spent a lot of my career talking about what digital methodology can do to advance scholarly arguments. It’s time to start talking in the present tense.
25 thoughts on “The Perpetual Sunrise of Methodology”
Thanks for sharing this, Cameron. I do really like your piece in JAH. I’ve spent a lot of time with local and regional newspapers looking at all of that extraneous stuff, such as ads and reprinted pieces. Reconsidering papers and using all of the other matter, outside of articles, is also possible now that so many are digitized and are machine readable.
I also agree with you that there is much less traditional digital history scholarship produced than might be expected. But, we all know that it takes a corpus of machine-readable materials related to your topic, loads of time, and interest. There are things I’d love to know about stamp collectors, but I don’t have good data. I’ve done a minimal amount of work with newspapers on trends in discussions of collecting but it’s not the heart of my story and my story continues after 1923.
I have a theory about why academics ask specific questions about sources and methods when confronted with a piece of scholarship that is derived from digital methods rather than focusing on the end point: They are still skeptical of what digital methods and tools can do, and they are skeptical of computer-assisted “readings” of data and sources that they are used to analyzing with their own eyes. There might be a new finding or interpretation, but can the work be replicated by them? How can they possibly know if your building blocks are sound? I keep hearing from very smart historians that they are baffled by digital history projects and are not quite sure how to assess them. Ack. You’re right that they are not focusing on the right things. I’m still surprised each year when there is a session at AHA or OAH asking if blogging is scholarship.
One thing that I really like is the “show your work” model of digital humanities scholarship, because it gives us all an opportunity to really interrogate our sources and to make visible some of the naturalized processes of doing humanities-based research. I actually think it’s too bad that your companion piece wasn’t an integral part of your JAH article–but that’s me.
Part of the justification for running an intro to digital history for mid-career historians was to help address some of those issues: to prepare historians to do their own digital work, feel comfortable advising students interested in this area, and also to give them confidence to assess and review digital scholarship. Because, yes, we are still stuck.
Hope your session was well-received at AHA.
Thanks so much for the thoughtful comment, as always! I like your point about scholars’ unfamiliarity with digital methods driving their focus on them. I think we’re all hoping that the methods themselves will become increasingly enveloped into standard practices to the point where people are more comfortable with taking them at face value rather than an inherent suspicion that they wouldn’t have for non-digital approaches.
I often point to the Viral Texts project at Northeastern in relation to my article. It seems like a very smart approach to take advantage of machine-readable sources. Which speaks to your other point: we’re all limited by data, time, etc. Sometimes you have to be pragmatic – which is precisely what ended up happening to me. I don’t have an inherent fascination with the city of Houston, but I thought it would make for a very good case study for a number of reasons, both methodological and historical.
As for how integrated the online component was with the JAH article: I couldn’t agree more. I was ultimately unsatisfied with how removed it feels from the article itself, but part of that was a strategic consideration of my audience. Given that a lot of its readers would presumably be non-digital historians picking up their hard copies of the journal, I wanted the article to ultimately stand on its own. Baby steps…
Finally, the immersive workshop model at CHNM is a really, really important one. As you and I both know, it’s a lot easier to build new skills with that approach than it is to kind of dabble in it if you don’t have an existing technical base.
Nice piece. I’m not a historian, but I was Wonderista whether questions concerning methodology could ever be all that far from academic scholarship. If the focus of the questions you were asked were centered on “how” in a simply technological sense I can see your point, but the questions about why you didn’t differentiate between articles and advertisements or whether the results could be replicated do not sound at all to me as ones that would be restricted to digital humanities but sound as if they would be appropriate in any empirically-based academic work. What kind of questions were you hoping to get?
It’s a point well-taken. Questions about methodology aren’t inherently a bad thing – it’s more a reflection of a field (digital history) where the balance towards methodology and away from argumentation is quite skewed. I was hoping for more questions along the lines of whether other historians thought my interpretation of geography and national integration held weight, how it relates to existing literature, what other areas of late-nineteenth century society might reflect similar (or opposite) patterns, etc. Do we need to rethink our conception of Houston/Texas as a southern city? Did American commerce trend even more towards the Midwest than we may have thought? These kinds of things.
Thanks for the comment!
I’m going anonymous on this one so I can state a point without having to equivocate too much. Cameron has my e-mail.
This is sound advice for digital historians seeking to reach an audience of regular historians; I worry, though, that it’s dangerously flattering advice in the hands of regular historians who think their elevation of “argumentation” as the central feature of the profession is helpful. It’s not. Rather than an “imbalance” away from argument in digital history, I suspect, the real problem is that DH’s methodological interests are far more interesting to those outside our subfields than are our arguments, at this moment in time. One of the distinguishing features of the field right now is that individuals who started careers as professional historians like Ed Ayers, Dan Cohen, Elijah Meeks, and Trevor Owens have given up to greater or lesser degrees on traditional forms of argumentation. (Even those in the field snub it: as Tim Hitchcock’s bio used to say, “‘I used to write books, now I write history.”) Those figures now follow the “methodological” star to explore visualization, cultural heritage preservation, expanding access to historical resources, and so forth. That’s still history, of course: but just because post-1970 historians like to believe as if argumentation is the beating heart of the discipline, rather than research or storytelling, we end up forcing them to choose.
Another way of putting this is: the reason you get questions about sources and methods is because that’s what matters, both to historians and to the wider public. After all, DH didn’t “expand the scholarship tent.” It restored it. History’s mansion has many rooms, and too many of them—source criticism, public history, critical editions, close reading—have been nearly abandoned as we waste time developing new arguments of trifling importance, or reiterating ones such fantastical significance that evidence is practically beside the point. DH’s significance has been largely in reclaiming those spaces for historians trained in source appreciation, respect for past cultures, and all the rest.
tldr; Digital Historians should spend only as much time on arguments as they must to stay in the profession, and get on with the truly important work of history: teaching various forms of literacy to students and the wider public, giving them a multitude of frames to see the world through the lens of its pasts, sharing all different sorts of artifacts, advancing multiple different forms of storytelling, and giving voice to as many past subjects as they can.
Thanks so much for such a thought-provoking comment. I agree that argumentation shouldn’t stand on the towering pedestal that our profession has seemed to place it, especially when it’s of the “trifling importance” variety. But neither would I toss it on the scrapheap. There is incredibly valuable history being done through argumentation, just as there is incredibly valuable history being done through source criticism, storytelling, public history, etc. Arguments and the evidence that underlay them still matter for understanding the past. In part because making an explicit argument backed by evidence means that you put your own interpretive stance out in the open. It drives home that history is ultimately a process of interpretation, and that not all interpretations are as good as others. Making an argument is a way of letting people evaluate the quality of those interpretations. Some of those scholarly debates might be quibbling or little more than professional posturing. And I’m not saying that you can’t do this with non-argument driven history or that you need to do this with all other forms of history. But a lot of those explicitly argument-driven conversations matter quite a bit. To take an example from outside the academy, Ta-Nehisi Coates’s article making the case for reparations has had a real impact on contemporary conversations about the legacies of slavery and Jim Crow. Argument stood at the heart of his article. In sum, I don’t think the important forms of historical work you outline at the end of the comment are at odds with argument-driven scholarship.
Ironically, we’re re-enacting what I think of the classic historian’s form of historical argumentation: whether a particular thing, acknowledged by both sides to be important has been “over-emphasized” or “under-emphasized.” This in in contrast to the discipline where argumentation truly is central, philosophy, where they seem to maintain some hope of actually proving things true or false.
One of my worries about attempts to link DH to argumentation is that I think prejudices about science tend to elide those two understandings. The sort of arguments one can make from digital sources tend to be of the rather positivistic sort, what might even be called “discoveries.” David Hacker’s work on revising the Civil War death tolls is certainly a digitally based argument, and one of the most popularly disseminated arguments of any sort to come out of the historical profession in the last 5 years. But I don’t think it’s widely disseminated. Humanists who distrust the digital tend to set up some inflated expectations that digital work will have failed unless it makes similarly definitive claims on issues of much greater importance that put to rest old debates or stir up new ones. I believe that such claims are–in many cases consciously–setting the field up for failure. Or worse, for a perpetual cycle of hyperbolic claims based on digital materials that can’t adequately describe a full social field and end up discrediting the whole endeavor. We’ve seen this happen before.
Coates is an interesting case. The heart of Coates’s article was, not, I would argue, argumentation at all. It was the elegant re-presentation of information already known to professional historians, embedded in narrative and personal stories. It certainly it didn’t advance scholarly arguments (though it did popularize them), and IIRC one of the major complaints is that it really never got around to a detailed argument about reparations–what they’d look like, why even if the post 1900 white ethnics should be as implicated as the descendants of slaveholders, post-1970 immigrants should be involved, and so forth. “Racism is more alive than you think” is a powerful argument to make in the Atlantic–but could be easily dismissed by professionals with that hoary question of elders who decide not to think very hard during DH presentations: “This is pretty, and you seem to have put a lot of work into it–but what does this tell us that we didn’t know before?”
That’s a good point. I think framing or comparing DH in relation to science fields can be doubly damaging. First in the naive expectation for big, definitive “discoveries” that you outline, but also from trying to replicate the structure of STEMs. It’s telling that DH has borrowed the “lab” concept so wholeheartedly but hasn’t had as much critical engagement with whether or not that structure actually meets the goals and workflows of humanities research.
A quick note on Coates’s article: I loved it precisely because I saw it as a form of historical argumentation whose audience was decidedly not professional historians. As you note, there’s nothing in there that most historians would find especially new. But it took a very clear rhetorical stance against more popular conceptions or interpretations of our nation’s racial history. The reparations argument was underdeveloped, but I read the rest of the article as a compelling argument aimed squarely at the idea that America’s legacy of race is somehow buried safely in the past and divorced from its present.
As I think more about it, argument-based scholarship might be something of a red herring. What I worry more about with an overriding emphasis on methodology is the potential for us to give short shrift explaining why it matters. Argument is one kind of explanation for why our research matters, but it’s certainly not the only one. I think about this in terms of the Geography of the Post visualization that Jason and I released in the fall. It has been and will be very useful for my own dissertation, but I spent way, way more time thinking and talking about the technical side of it than I did thinking about how to convey to users why the visualization matters in terms of its history. To echo what I said in my post, there was a vast imbalance between my focus on methodology and the amount of attention I paid to its historical payoff – whether that payoff is in terms of generating arguments, storytelling, engaging the public, etc.
Well put–I think I basically agree about all of this. And yes, Coates’s article was far more important (and better?) than most traditional history because it had a point (or an argument, I’m happy to concede for these purposes).
One useful distinction, though, may between “technique/method” and “methodology.” I do agree there’s too much celebration after getting Gephi to label your nodes nicely. But I think methodology–the study of method–should continue to be DH’s defining strength. A good way to talk about placedness for cities other than Houston is a far more important contribution, I would say, than just situating Houston itself, even if the profession is much easier about accommodating the latter. Maybe even more in English, what’s exciting about DH is that it offers important contributions to how we talk about literature that aren’t just refutations or elaborations of existing theses; they’re new ways of thinking about what we do.
Fascinating piece; I really enjoyed it, even peering in from outside the discipline as a literary historian, there’s a lot of relevance here.
The situation is a little different in literary studies, but I recognize a lot of features, and I think the risk you’re describing is basically present in both disciplines.
In literary studies, I think we’re now beyond the point where anyone could say “these new methodologies aren’t producing substantive results.” They clearly are. We’re seeing a lot of traditional publications now where the pay-off is really a claim about literary history rather than a new methodology. And more are in the publication pipeline.
But it took a long time for that to happen. “Distant reading” was coined around 2000, and of course it’s drawing on a number of even older traditions. But up to about 2010, it was possible to argue pretty persuasively that Franco Moretti was the only person getting high-profile results from numbers, and then you could say that his intervention was idiosyncratic and hadn’t really depended on computational methods, and was more of a methodological provocation than a substantive research program, etc etc.
Five years later, I think that’s clearly no longer true. But it took a long time for people to retrain, and for new work to make its way through the pipeline. And I think the digital turn was always going to be easier to pull off in literary studies than in history, because we have a more delimited field of primary sources. It’s hard to digitize all the world’s archives! So part of what I want to say is just that one needs to take a long view of disciplinary change.
The other thing I’d admit, though, is that you really are right. Even though digital methodologies can produce substantive results, it remains true that infatuation with methodology is a real danger.
One reason I think this is important is that it’s not a phenomenon at all restricted to digital methods. There’s a kind of sclerosis in some quantitative social sciences (econ comes to mind) where they get obsessed with refining methodology and forget the bigger picture; Piketty’s intervention has been partly about correcting that. And this danger is not limited to quantitative methods either: e.g. my own field has often been guilty of a disproportionate obsession with abstract “theory.” People imagine that “theory” is, like, the opposite of “digital methods,” but to my mind it poses basically the same risk: it’s easy to be fascinated by your own procedures, but a discipline can become inward-looking if we overdo it.
All that being said, it’s still true that your Ballard post was great and rightly influential. But topic modeling does make a good example of the risk. I’ve published some substantive articles that use topic modeling, but I do think there’s an infatuation with topic modeling in particular that may be a bit excessive, just because it’s a cool method with an unsupervised magic-trick quality to it. There are a lot of simpler methods that can be just as useful — and maybe more so — but generate less buzz.
It’s good to hear your perspective as a literary historian, Ted. Part of the difference between (digital) literary studies and history might be the really strong contributions of public history to digital history. As I say above, public historians have without a doubt been the ones pushing the field forward in history. While many of them certainly make arguments in their work, they don’t have the same professional need (some would say fetish) for argument that academic historians do. Given the preponderance of really fantastic digital public history works, those become the kind of model or standard for digital history writ large. Correct me if I’m wrong, but I don’t think there’s an equivalent within literary studies? If anything, it seems like literary studies has a longer history with, say, authorship attribution as a kind of genealogical precedent – which is acutely argument-driven.
And very good reminders that methodological emphasis is not endemic to digital history, and that a fixation on theory can distract from argument as much as a fixation on methodology.
I think that’s right. I suppose the closest analogy to the role of public history within literary studies might be the tradition that emphasizes editing and curating relatively small archives of digital texts. People who practice that kind of scholarship do occasionally suggest that the point is precisely to get us away from narrowly thesis-driven arguments. If we characterize TEI as a methodology, this is a tradition that does spend a lot of time talking about methodology, and it’s been pretty central to literary DH on the east coast (though not, e.g., at Stanford). But it sounds like public history plays an even more central role in digital history than (say) TEI does in literary studies.
Wonderful post Cameron and great ensuing conversation. Many thanks.
The following does not discount any of what you are exploring here, but isn’t the perpetual emphasis on the future breakthroughs of digital history bound up with the rhetorics of the contemporary tech industry? Silicon Valley thrives on this sort of sensibility in which the triumphant breakthrough to true knowledge, wisdom, happiness is just around the corner, just over the horizon, one click or app purchase or smartphone acquisition away, always about to arrive but never quite delivering. Shoot, that doesn’t just come from Silicon Valley, it’s at the heart of modern consumer capitalism itself, isn’t it!?
The adoption of this kind of language, self-understanding, and professional approach within digital history comes, at least partly, from our own historical moment, in which a certain imagining of entrepreneurial “making” is idealized. It’s not just a love affair with methodology; it’s a love affair with marketing. As if every digital history or humanities project were the launch of the next Apple iPhone, and it will, finally, *change your life!!*
Not that anyone is adopting this kind of approach on purpose. More that it’s in the air. When the slower sifting through the soil of specialized historical arguments out of the spotlight of that perpetual sunrise you describe is increasingly lambasted, even within the profession, and when the successful tech entrepreneur is increasingly fetishized not only as the American success story economically, but also the ideal model for the American citizen, while at the same we conflate the public with the consumer, it’s no wonder that an emphasis on the promise of a “deliverable” of a “user-driven” methodological process trumps substantive debates over actual interpretive findings.
In the end though, after my little Christopher Laschian outburst here, I wonder this: are you making too strong a distinction between methodology and argument? Has not the best scholarly history always found an astounding way to show us precisely the deep links between methods and findings, between the way we come to know something about the past and what that specific knowledge actually is? And then to root that interplay between method and interpretation in a historiography of prior attempts to make sense of the past. To me, our job as digital historians is to continue in that tradition, and this, from my perspective, is something that you are beginning to do quite strikingly in your work.
Great parallels to the Silicon Valley rhetoric – given where I live and the institution I’m at, I’m pretty much swimming (drowning) in it every single day. I liked a word that Ed Ayers used at the panel: anticipointment. Given both how comparatively new digital history is and, frankly, how expensive it can be, we often put on the salesmanship hat. That’s doubly problematic when the thing you’re selling involves technology, which is steeped in even higher expectations of the kind you outline. What’s interesting to me is that in many ways we’ve outgrown the need to proselytize about the payoffs of digital methods and yet we continue to do so (myself included). I find myself thinking: who are we trying to convince here? Sure, there’s still resistance to it, but overall I very rarely have to defend the validity of what I do. Of course, that’s from the particularly privileged perspective of being at a place like Stanford.
Wonderful post and discussion here. From the perspective of art history, I would add only that we need to acknowledge the more generic function of disciplinary and academic historiographical debates when we talk about a split between discussions of method and those of argument. That is to say, it is not merely that a digital methodology faces off against argument-based scholarship, but that digital methodologies occupy a different position within the disciplines themselves in terms of the kinds of questions best suited to these means. Many humanities fields are dominated in their top ranks by scholars of a generational and intellectual composition who have spent long careers building up and defending scholarship based on the application of theoretical models, microhistories or ever-more fragmented senses of social identity, among others. It goes without saying that the aggregating nature of digital methods and their emphasis on comparable patterns of historical activity (as one example) relies on both an evidentiary and theoretical basis radically different than many of the most dominant approaches. This is a long way of saying that the reason digital humanities have not been widely accepted in the “argument” corner of our disciplines may very well be that those bastions are well-guarded by journals, tenured faculty, institutional structures, reputations and intellectual commitments, all of which have something to lose. Thus, we are not only seeing a split between method and argument, but we are also seeing a more classic battle on the substance of humanities questions and methods that occurs every generation when one set of intellectual commitments replaces another. This has positive implications (a critical approach to scholarship and the status quo) but negative ones as well (the obvious role of market, that favors a new approach as the next best thing). It seems to me that we must also acknowledge these disciplinary and institutional conditions if we hope that critical digital humanities scholarship will make a broader impact on the humanities and the public as a whole. As you say, methodology has been the dominant substance of digital humanities scholarship and, as a result, at times limits its ability to engage more broadly and analytically; but, at the same time, methodology from the digital humanities can also be a threat to vested interests, a condition which creates its own dynamic in the marketplace of ideas.
It’s very interesting to see all these perspectives from outside history itself.
They highlight for me, though, something that’s distinctive about our field. Underwood’s describes a “sclerosis” of method, similar to Jaskot’s “limited ability to engage more broadly and analytically.” In history, I think just the opposite is the case. Because our methods have been as much about building web-oriented narrative forms as about exploring algorithms, non-argumentative digital history frequently has a larger audience than academic history. Kramer is right that there’s hint of hucksterism in the promises (mix Omeka with a concise explanation of why America never developed socialism, and the crisis of the humanities would be solved?) But at least in history, I think it’s probably incorrect to suggest that connecting to live arguments in the profession will increase the audience; the books that get you tenure at Madison are far less widely read than your article on Martha Ballard. (And probably not everyone who read it know what sort of plants you garden in Maine, or whatever). TEI has a much narrower audience than the Digital 9/11 memorial.
It’s still caught up in a struggle with vested interests, to be sure. But historians have a particularly live tradition of non-argumentative literary work at the pinnacle of the profession somewhat distinct from public history. The literary tradition (think of, for example, the Parkman prize; or microhistory, which particularly after Ginzburg was as much about inculcating understanding through experience as through argumentation.) I think one could argue that that’s the area where most of the exciting digital history work has been happening, not really in topic modeling or network analysis; if we can expand the acceptance of the literary to include other forms of narrativity, then we’d really be accomplishing something interesting. And that’s fundamental a methodological (though not a technical) challenge.
It opens up the question of: who exactly is the audience that we’re talking about? Are we trying to engage “the public”? Other digital humanists? Other historians? Other historians from the “argument bastion” of the discipline? On one end of the audience continuum you’ve got the dissertation-monograph that’s never been checked out of the library and on the other end of the continuum you’ve got the Digital 9/11 Archive. But most of our digital work operates in between. I’m guessing many, many more people will interact with the Geography of the Post visualization than will “interact” with my written dissertation. But while I understand what the interaction with a written dissertation looks like, I don’t have as firm a handle on what the interaction with a visualization looks like. I mean this not in the UI sense, but in an intellectual sense. Are most people just looking at all those dots on a map, saying “oh, neat” and moving on? Or does it really spark people to think in new ways about western geography and the role of communication networks? I hope the latter, but I suspect the former.
Thanks so much for the comment and the perspective from art history! And good reminders about the institutional dimensions at play, although I wouldn’t paint it in quite so combative terms. I don’t see myself as launching an assault on the castle of “traditional” history, nor do I get that reciprocal sense from more established historians who aren’t using digital methods. I often sense more curiosity paired with discomfort (and the normal healthy does of academic skepticism) than I do feelings of besiegement.
Audience! Yes, yes, yes. We all have to be very intentional about audiences, and designing projects for primary and secondary audiences. I’m not sure if you have a wide audience for the visualization. And I think you’ll have to reach out and make this project known to folks whom you think might be interested in it. They are not likely to just find it on their own unless they know to look for it (Geography of the Post, I’m thinking of specifically).
To get a sense of how people are interpreting and understanding the map, you’d have to test for it. While you’re familiar with UI/UX testing, there is another line of content testing. There are ways to design interview questions, film users to see what they do with the site–either with guidance or without–, or to frame it like a think-aloud (Sam Wineburg) to capture how historians (or whomever) are reading, exploring, and understanding the project.
I think this is one of the biggest differences in how digital public history is designed and how digital history is done–digital public history is generally designed for and with specific audiences and then tested, and sometimes redesigned and adjusted based on the feedback. Then there are rounds of content testing, and sometimes revisions. It’s not easy.
It is possible to identify audiences for our projects, and in fact we need to if we want them to be successful endeavors. And perfectly okay if your audience is small, such as historians of the American west, or even just your dissertation committee. We just need to be honest with ourselves about our goals and aims. And if there is something that you build that furthers your research and findings, and there isn’t a wide audience, it’s okay. It served you well, and that is also important.