What I'm looking for in the WIRED back catalog

"History doesn't repeat itself, but it sure does rhyme."

[This is a piece I wrote last summer, primarily for myself. It’s an attempt to spell out both what I am attempting to accomplish with the History of the Digital Future research project, and also to expand a bit on how I approach social science research.]

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When I started this Substack in 2021, the plan was to primarily use it to work out some ideas in the #WIREDarchive project. This has been my main research obsession for the past few years — I read the magazine’s entire back catalog in the summer of 2018, wrote about it for the October 2018 issue, and I’ve been slowly fiddling with a more ambitious book-length version of the ideas that came out of that work.

There are a few reasons why this project has moved slowly. Some of it is <gestures at everything> other life and work responsibilities. But it has also been tough to write on this topic because of the nagging voice in my head asking “Dave, this is not your field. What do you think you’re even doing here?”

I imagine some readers of this Substack must have similar (albeit likely more polite) questions. “…Um, why is the Bret-Stephens-heckling political scientist writing about parallels between tech stocks in 2021 and 1999? Karpf, buddy, what are we doing here?”

So, to properly air and answer all these misgivings, what follows is a little Q&A interview between myself and my gnawing self-doubt.

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Q: Alright man, let’s start with a softball. What’s the WIRED project supposed to be, and how did you get started with it?

A: I came up with this idea over a decade ago — 2011, I think. It was while I was still at Rutgers, just starting out as a Professor. It was also during one of those peak moments of optimism about the digital future. I thought it would be fun to design a class where we read through back issues of the magazine to see what the digital future looked like in retrospect.

This was in the waning days of peak Web 2.0 enthusiasm. Facebook, Google, Amazon, and Apple were fantastically successful and fantastically profitable. The iPhone seemed to be ushering another wave of technologies, continuing a streak of relentless change that dated back to the mass adoption of the World Wide Web in the mid 90s. The Arab Spring and Obama’s victory were inspiring deep confidence that technology was empowering people, disrupting old systems of power and replacing them with something better.

I thought we could learn a lot about the under-explored challenges of the present moment by revisiting previous waves of contemporaneous tech optimism. Plus, it just seemed like a fun side project.

At the time, I filed the idea away as “too-weird-to-do-pre-tenure.” I had a book to write and had to find my footing in the career.

I revisited the idea in 2017. I had earned tenure at GWU, my second book had come out, Donald Trump was President, and we were expecting the birth of my first child. One thing about those early Trump months was that they were just a psychological vortex for people in my field of study. As a researcher, you couldn’t look away from the news cycle — even when, as a human being, you desperately needed a break. Everything was absurd chaos that changed hour-to-hour. And I started thinking about how nice it would be to take refuge in the study of history, since history doesn’t change.

In early 2018, I talked with an editor from WIRED about something else entirely. I mentioned that I had this goofy idea of reading the whole back catalog. The magazine was approaching its 25th anniversary, and he pointed out there could be a good opportunity there if I expected to have the research done in time. That conversation resulted in a magazine pitch, and also to an unexpectedly hectic research deadline.

I ended up spending the first six weeks of summer 2018 anchored to a desk in GWU’s Gelman Library, frantically reading through all 25 years of the magazine’s back catalog, assembling “field notes” on what the digital future looked like as it was arriving, free-writing about unexpected ideas and patterns, and organizing topical “throughlines” on connected subject areas that appeared over the years (future of journalism, civic technology, future of the economy, etc).

It was a big, bold, ridiculous swing at an entirely new project. I loved it. But I knew I’d have to give the whole thing a second, more systematic read if I wanted to do something more substantial with it.

This, it turned out, would take awhile. I spent a couple years as associate director of GW’s School of Media & Public Affairs (department chair, essentially). Then the pandemic hit. And we had our second kid. The result is that I’ve been thinking about this project for over four years, but it’s somehow still in the pretty early stages.

…But, you’re my gnawing self-doubt. You know all this already. Let’s get on to the real questions, shall we?

[My self-doubt]: yes, let’s proceed.

Q: Let’s take a step back and focus on the bigger picture. You’re a political scientist and an old activist. Your main intellectual contributions have come from careful study of the “organizational layer” of American politics. And now you… just read old WIRED magazines. What are you actually doing here? How does these pieces fit together into a whole?

A: The throughline is that all of my best thinking comes from getting stuff wrong. That’s the angle from which I approach all social science research questions.

My first book/dissertation was The MoveOn Effect. It was about groups like MoveOn.org and the blogosphere and the aftermath of the Howard Dean campaign. That book was motivated by my previous years as an environmental organizer with the Sierra Club. In 1999, when I was the director of the Sierra Student Coalition (SSC), I met the head of MoveOn at a conference. He was an old SSC staffer, so we got to talking about his new organization. They were running digital petitions, and had attempted to stop Congress from censuring Bill Clinton. It all sounded kind of silly to me.

Digital petitioning in 1999 seemed like a shiny object, a distraction. By 2003, MoveOn was playing a critical role in mobilizing mass anti-war demonstrations. It was arguably the most impactful progressive organization in the country during the George W. Bush presidency. My model of how politics works, how the world works, was either outdated or outright wrong.

My second book, Analytic Activism, came out of an interaction I observed at the Netroots Nation conference. I was supposed to grab lunch with my friend Stephanie. Before we could go, she got into a debate with a colleague, arguing over how to frame a political ad they were going to put on air. They went back-and-forth, arguing competing visions and rationales. I know how these tactical arguments typically go. They last forever. They are decided through attrition. Instead, after making their case to each other, Stephanie declared, “well, we’ll test it.” and her colleague abruptly agreed, “yeah, let’s test it.”

I’d served six years on the Sierra Club Board of Directors at that point. I’d been an activist leader and trainer for over a decade. The Sierra Club (at least back then) doesn’t incorporate testing into its tactical decision repertoire. This was a whole layer of digital political campaigning that was absent from the finalized book manuscript I had just sent to the publisher.

“Shit,” I muttered, “I’m gonna have to write another book.”

All of my research is guided by an attempt to explore and explain that parts of political and social life that don’t fit my existing framework for understanding the world. I’m, in effect, a bayesian. I try to make predictions, look for the spots where I’m wrong, and then dig deep into those areas to learn something new.

The idea in systematically studying old WIRED magazines is to apply this approach to other peoples’ predictions — people who are granted a platform to make confident claims about the trajectory of technology, society, and power. I suspect that many of the predictions we hear today ought to be refined, challenged, or outright rejected based on a critical reassessment of the predictions from decades’ past. There’s a lot that we can learn from what we previously failed to notice or got wrong.

Q: So… you’re a historian now?

A: Well, no. But my graduate training is in American Political Development/historical institutionalism. That’s the subfield of political science that is most historian-adjacent.

I won’t lay claim to being a proper historian, and I imagine some historians will grimace when they hear me refer to WIRED magazine as a primary or archival source. But what I’m doing — capturing historical discourse through contemporaneous media coverage — is methodologically pretty well-established in my subfield. It’s just that the subfield of APD typically focus on topics like 19th century state-building, not 21st century technocultural discourse.

Q: the main fields that intersect with this topic are history, anthropology, sociology, Science and Technology Studies, Human-Computer Interaction, engineering, and computer science. You are trained and well-read in zero of those fields, right?

A: I mean, yeah. That’s a major pitfall that keeps me up at night. When I conducted the first version of the WIRED project, I’d read very little in any of these subject areas — mostly just Fred Turner’s From Counterculture to Cyberculture and Bruno Latour’s Science in Action, really. I have wandered waaaaay outside my disciplinary boundaries.

I’ve tried to patch the disciplinary hole just by reading a ton of books. I’ve read about 120 books in these subject areas since I completed the 2018 study. I’d estimate there are another 20-30 that I desperately ought to read just so I don’t totally embarrass myself. And that isn’t a great patch, since familiarizing myself with the major contributions from these fields isn’t nearly the same as being conversant in any of them.

I had a similar concern when I wrote The MoveOn Effect. That was a book that squarely fit into no single subfield. It was sort-of political communication and sort-of social movement studies and sort-of interest groups. I worried that each subfield would reject it as a shallow-at-best contribution. Instead it was broadly accepted as a cross-disciplinary contribution from someone in conversation with, but not belonging to, those subfields.

My hope is that the History of the Digital Future project will eventually encounter the same reception. But, yeah, it certainly could go the other way. The smart, safe career move would’ve been to just keep writing about the organizational layer of American politics. There’s a chance that I’m shipwrecking my entire career here.

Q: Okay, let’s talk about methods, then.

A: I’ve tried to keep the research design intentionally simple. It’s a bit of a kludge, and very transparent. That’s the formula for digital research that I laid out in my 2012 methods piece, “Social Science Research Methods in Internet Time.”

To state it plainly, I’m just reading every issue of the magazine, chronologically. I’m taking notes as I go, then pausing at intervals to review the notes, inductively draw out themes, and write about those themes. I’m also tracking specific topical throughlines — noting every feature article on the future of [journalism, virtual reality, politics, dating, music, etc]. Once I’ve read through the entire back catalog again, I’ll assemble all articles from an individual throughline and read those chronologically to further explore the common tropes and repeat predictions that appear across time.

That’s what I did in 2018, at a breakneck pace and with far less background knowledge of relevant scholarship and historical circumstances. I’m replicating the same process in 2022-23, at a pace that will allow me to be more thorough, inductive and reflective.

I’m also adding a simple descriptive-quantitative component to the study. In order to provide readers with a window into the changing status of the magazine itself, I’m recording (1) the total number of pages in each issue (it varies from less than 100 to over 400 over the years), (2) the number of advertisements in each issue, and (3) the types of products that are being advertised.

The quantitative component isn’t going to tell us anything world-changing about the history of the digital future. But I think it’s going to be helpful for illustrating how the magazine, and the tech discourse it embodies, changes across time.

I used to joke that all of my research methods are indistinguishable from dares. Anyone could do what I’m doing. But it seems like a lot of effort. Most people wouldn’t. I also think its important that I’m doing it all myself. I wrote about this back in 2013, while I was gathering data for my second book. The act of routinized research is also a cognitive commitment, creating the time and space to generate new ideas and evaluate which patterns are worth further study.

Q: You were going to write a third book on the Online Progressive Engagement Network (OPEN), finishing the netroots “trilogy.” Why didn’t you?

A: Yeah, I was. I wrote about OPEN in 2013 for The Nation, after I was invited to observe their first in-person gathering. I attended four other OPEN meetings in subsequent years. My friend Nina Hall was studying them as well, and published an excellent book about the network last year.

I ran into a couple of problems with that project. One was simply logistical — my ideal methodological approach would have been to conduct field research in several countries over the course of several months. That’s a great idea if you have a lot of research funding and no parenting responsibilities. After my first kid was born, the window for that type of intensive international research effectively closed for me.

But the other problem is, I think, my primary weakness as a social scientist. It’s the downside of letting my research agenda be set by curiousity about things-I’m-wrong-about. One I arrive at answers that seem good-enough-to-me, my interest in the topic seriously wanes.

The best social scientists are meticulous in designing research that actively tests competing hypotheses and provides convincing proof to skeptical peers. It can take months to arrive at a good-enough descriptive hypothesis, but take years to develop the methods and data that effectively test that hypothesis.

I’m a descriptivist. My comparative strength has always been in the early descriptive work — poking around, asking questions, tracing processes, and identifying spots that defy existing expectations.

There are a ton of interesting comparative puzzles in the OPEN network. But, after writing Analytic Activism, I felt like I mostly understood how that collection of groups operate. Studying how the netroots model has morphed and adapted as it spread across countries/continents/cultures/political and media institutions is a really interesting topic. But it isn’t the style of research that I’m particularly well-suited to. I hope to return to it someday, but only once I’ve identified the next set of questions that I need it to help me answer.

Q: your main intellectual contributions have come from bridging practitioner and social science perspectives. You’re not a coder or an entrepreneur. Your practitioner knowledge here basically amounts to “well, I’m an Xennial. So I remember living through a bunch of stuff.” What makes you the right person to do this project?

A: That’s another major concern, for sure.

My one-cool-trick is basically just critical reflection. In my first two books, that meant thinking about how the tactics, strategies, and organizational behaviors of “netroots” organizations differed from the organizing traditions I had been schooled in.

Studying the history of the future has a similar feel to it, because futurism is never actually about accurately predicting the course of events. It’s about influencing them. Futurists fashion a story about the past and present that leads to a proposal for what we ought to do or value in the future. Some of them are engaged in a thinly-veiled ideological endeavor. Others are trying to marshal funding or attention. Still others are offering a warning.

One thing I’m actively avoiding in this project is a Philip Tetlock-style exercise of evaluating who is “best” at predicting the future. Tetlock’s Expert Political Judgement was a phenomenally successful book, and it remains an interesting read. But I think Tetlock didn’t take the political economy of expert prediction seriously enough. The people he interviewed in his book repeatedly told him “the predictions you are calling ‘wrong’ are intended do something else entirely.” I don’t think he took those responses seriously enough. By comparison, I found Dan Drezner’s book, The Ideas Industry, much more helpful in revealing the political economy of thought-leadership — the actual incentive structures Tetlock’s experts were responding to.

There’s a version of my project that could look a lot like Drezner’s. I could study the “tech intellectuals,” and observe how institutions like the TED network arose to provide powerful incentives for entrepreneurs and evangelists who preached the gospel of Moore’s Law. I’ll likely devote a chapter of the book to that topic, or write a stand-alone piece on it.

But what I most want to do is critically reflect on the predictions themselves. We’ve heard variations on the same promises and warnings about the future of technology and society for almost 30 years now. We rarely take the time to learn from the dashed expectations of 2008 or 2015. There are persistent blind spots in our rendering of the digital future. And while the political economy of the tech-version of the ideas industry helps to explain why those blind spots exist, I think there’s a worthwhile separate project that just patiently wades through the old futures and effectively names what the blind spots are. That, most of all, is what I’m hoping to do here.

Q: And what do you think you’ve found?

A: A lot, I think? So much that I’ve taken to writing weekly substack essays just to sketch the themes and the boundaries.

There’s the slowdown of internet time. There’s the church of Moore’s Law. There’s the ideological foundations of techno-optimism. There’s the Internet’s three original sins. I’m pretty sure all of the talk about digital disruption has overlooked a major phenomenon of institutional fragility. Then there’s a ton about venture capital as a system of financial bubbles, and the language of tech disruption serving as cover for a political project of regulatory arbitrage.

And there’s also the increasing power of tech over time. The techno-optimist investors and entrepreneurs of 2023 are ideologically very similar to their counterparts in 1993 and 2003. But they have dramatically more money and power. Tech has become central to all social systems. So that increases the magnitude of their mistakes. It means their ideas and political projects deserve more robust attention and criticism.

The present is a lot like the past, but magnified.

Q: why not study climate politics instead? Why this?

A: I often think back to a conversation I had years ago with Micah Sifry. We got talking about climate politics after I had had just enough whiskey to reveal myself as, basically, a climate doomer.

I’m an old climate activist. My friends and I fought hard, for years, under the belief that we had maybe a ten-year window to stave off the worst effects of climate change. That was over fifteen years ago, and I’m not convinced we were wrong about the timing. The best solution to climate change in time travel. We should have done more, back then. We tried, and we failed. I have regrets. (This isn’t how I would phrase this for public consumption. It is how I think about it with a specific quantity of whiskey though.)

After I’d finished my rant, Micah asked me a question that has stuck with me ever since: “how can you study what you study if you really think it’s so hopeless?”

It’s one of those questions that no one had asked before. The answer seemed obvious to me. “I study the intersection of politics and technology because that’s where I’m most often wrong. If I’m right, then it’s hopeless. But I’m frequently wrong! I focus attention where I’m wrong, and try to explain what I learn in ways that can be useful, because that’s where my hope lies.”

I’m studying old tech predictions, the history of the digital future, because I’d desperately like to be wrong about the trajectory of climate politics. And new technologies tend to co-occur with the fuzzy terrain at the edges of my map of the political world.

So the book is a critical project, but also a deeply hopeful project. I think we can understand the present and the future better if we learn from the past. I think we can do a better job of building a better tomorrow by studying how yesterday’s tech promises diverged from reality.

I’m going to finish rereading the whole back catalog in 2023. I’ll turn it into a book manuscript in 2024. And then I’ll go find another puzzle that I don’t understand, and I’ll work to figure that one out too.

In the meantime, I’ll keep writing about it on Substack. The best way to figure out what I’m figuring out is to write about it.