How do you fix a field?
Imagining a Decadal Survey for the Social Sciences
In previous posts (and papers), I’ve been interested in identifying some of the problems with academic research in my fields. Before you can fix something, you need to figure out what’s actually wrong. But conversations rapidly shift to the question of how do you actually fix it? What steps should we be taking? My response is usually “Hell if I know” because this is a huge and complicated question. There are some interesting proposals on the table (I’m particularly interested in viewpoint diversity discussions, on which I have mixed feelings, and I’ll write about another time). In this post, I want to suggest something I’m not seeing proposed much elsewhere—although it’s related to other trends that recognize there are gaps in the curriculum and are trying to fill them: The Decadal Survey.
In Astronomy and Astrophysics, they have Decadal Surveys. Per the American Astronomical Society, “Once every ten years, the astronomical communities gather panels of experts to set community-wide priorities for the coming decade. These surveys are facilitated by the National Academies and commissioned by the Federal agencies.” As the National Academies website explains, the decadal is about: “What are the key scientific challenges for astronomy and astrophysics in the next decade?” In the most recent decadal (2020), the panel considered the state of scientific knowledge on the big areas of their field, where the holes are (e.g., we’re still tyring to figure out what Dark Energy is and why the universe is expanding), and where the opportunities are, considering that some giant-ass new telescopes are going to be designed and come online (hopefully). They recommended “missions” that will answer certain questions. Now, importantly, it’s not the case that everyone needs to work on the missions they propose or the questions they identify as key. But when you apply for funding, it sure helps your case to say your project aligns with the Decadal Survey’s priorities. We need something like this for the social sciences.
We have huge gaping holes across the social sciences and humanities. We have bloat in some areas and almost nothing in others. Our knowledge is patchy. This is a huge problem, and it’s been exacerbated by the growth of disconnected, incremental research, which fails to build knowledge. It accumulates, but it doesn’t build. In law and society, “legal consciousness” is hugely bloated while other topics (e.g., legal endogeneity) are surprisingly underdeveloped. The misalignment seems to be most clearly a function of how easy people think it is to do the research (with political alignment as an additional, but smaller factor—partly because almost all of our topics are politically aligned these days). But we also fail at basic practical questions like articulating the conditions under which reforms fail and succeed (elsewhere, I have an inventory of conditions under which they fail, based on existing studies, but I have a much sketchier list of conditions under which they succeed, because we don’t seem to study success as much). In criminology, it’s really hard to find good work on predictive factors for recidivism—to be fair, the research design/inferential challenges for this question are really tricky given how much confounding there is. But it’s weird how little good work is on this.
Let me illustrate the lack of systematic coverage in my sub-subfield of prison history a bit more systematically. (This topic is why I got into academia. I can’t say what exactly it is about prison history, I just find it fascinating. It’s the thing I love more than anything else and in recent years the field has gone to shit and I’ve become more and more miserable because I now hate reading in my field. I’m still interested in trying to change things so I can go back to reading interesting stuff that I trust. If that fails, I’m out.)
A few years ago, I wrote a review article about where the field of prison history has evolved since David Rothman’s classic (1971) Discovery of the Asylum. (Rothman’s is book that everyone recommends you start with if you are interested in studying prison history, but it’s now pretty outdated, so I wrote the article as a compliment to his book so you can read the fantastic original but also get a sense of what it got wrong or at least what’s more controversial now, what gaps we’ve filled in, and where a bright new scholar might head next.)
In that review, I noted that, after a lot of action in the 80s and 90s, there has been very little action on the early US prisons lately. (Scholars around the world have started to fill in some of our gaps on the first prisons in other countries, like those in South America, Asia, and Africa; there’s also a continuing debate over what exactly was the first-ever prison, looking at Europe and the US, and answers vary significantly depending on how you define “prison.”) Instead, we get regular contributions looking at the post-Civil War US South.*
*Perhaps as a result of this imbalance (and the apparent refusal to read earlier prison history), there’s a strong impression among lay audiences and novices/interlopers that prisons (and prison labor) didn’t exist before the Civil War (see the 1619 Project entry on prisons, which only focuses on the post-Civil War period, missing an opportunity to talk about the role of slavery in the creation of the first prisons or the type of racism that was a background factor in how incarceration shaped up from the beginning).
Interestingly, this lack of interest in the Revolution to Civil War tracks trends in History as a discipline where, I’m told, it’s really hard to get a job if you study classic topics like the American Revolution or the Early Republic. (And really fascinating, these periods are now right-coded.)
Likewise, (not mentioned in my review, since it was focused on the earlier period,) there’s very little these days on 20th-century developments (big houses + correctional institutions) until you get to mass incarceration, which is where the action among historians has skyrocketed. Indeed, the few accounts engaging the period before the 1970s are usually about how that period laid the foundation for mass incarceration (Rebecca McLennan’s is a nice exception, but that’s from 2008, before the bulk of historians discovered prisons, or “carcerality”).
And yet there is a lot more work to be done on the early period of prisons (roughly the late colonial period/Revolution through the 1920s). New York, Pennsylvania, and Massachusetts tend to be overstudied while other states tend to go under the radar (if they are studied, it’s usually in dissertations or books that don’t make a big splash). There has been very little work on frontier states both historically (there are a handful of books on states West of the Mississippi) and recently (a book on “caging” in Los Angeles came out in 2017).
The bigger issue isn’t just the periodization spottiness, but also the topical distribution. There are also huge topics that need to be explored: race and gender are the big focus of prison history books now, but more basic questions about the difficulties of implementing prisons, the politics that went into prison adoption and prison placement (including the multifaceted resistance to prisons), the realities of prison regimes and prisoners’ daily lives, the prison economy and facets of prisoner labor, the role of religion (outside of the Pennsylvania System, which is hugely overstated and somehow has sucked up all the oxygen in the conversation), the fate of other punishments after prison adoption, the national and international discussions about prisons/prison policies, etc. There is about one book on some of these topics (e.g., by Graber, Miron, Shorb in the early 2010s), but they seem to stay in the margins of the field (in comparison to stuff on gender and race) and we don’t have a fully fleshed out understanding of variation across space and time on these topics.
And if you think it’s just historians who aren’t being systematic, look at sociology: so far, I’ve coded 80 AJS abstracts from 2000-2025 on crime and criminal justice topics (out of 93; I’m coding articles in a random order). 31 of these articles are historical projects. Of those focused on the US, the most popular time periods are late-modern (roughly 1970s to present, n=7), which makes sense—it’s our most recent major transformation era. The second most popular is the post-slavery/Jim Crow era (n=6) (usually I’d say post-Civil War or early 20th Century, but these papers are explicitly about the role of racism and the way they are described in the abstracts is usually about the end of slavery and/or the role of Jim Crow). One other paper is primarily focused on the post-Slavery/Jim Crow period, but it starts in 1840, so technically gets into the pre-Civil War period. Only one paper looks at the pre-Civil War period, and that’s a study that looks at the whole length of US history (focusing on antimiscegenation laws). There are three papers that look at the late 19th and early 20th C and two that look at the mid-20th C (and aren’t primarily focused on race, but two of them are on immigration or colonialism). There’s also one on the early modern period about piracy and one about violence in early 19th C France, in addition to some multi-country analyses from the late-modern period. That is incredibly patchy.
And it’s not just the period focus, but the topical monocropping. The studies about 19th-century prisons/carceral practices are all focused on incarceration/control of Black prisoners/criminals (sometimes, but not always, in comparison to White prisoners/criminals). For completeness, here are the topics (using language from the abstracts as much as possible) for US-focused papers on the 19th and early 20th C:
Extraordinary state interventions to avoid lynch mob violence between 1880 and 1909 in the American South
Lynchings and racial group boundaries, categories, and identities promoted by the southern Democratic Party at the turn of the 20th century and on which the emerging Jim Crow system rested
Origins of felon voting bans, many of which were passed in the late 1860s and 1870s
Post-Civil War convict leasing in Georgia
Early 20th C incarceration rates relative to cotton yields in Georgia
Racial inequality in incarceration in northern and southern states in relation to increasing rates of African-American migration to the North between 1880 and 1950
Black incarceration from 1840 to 2020 compared to the historic prevalence of slavery; special focus on Reconstruction and Jim Crow (1870–1940)
county and state “dry laws” banning alcohol from 1890 to 1919 relative to presence of/proximity to immigrant and urban populations
the Ponzi scheme perpetrated by Samuel Insull’s utility empire in the 1920s and 1930s and related investigations
early 20th C police militarization traced to colonialism
Going back to the Decadal idea, a Prison History Decadal could identify a series of substantive questions about the creation, adoption, implementation, and institutionalization of prisons and then authorize a “mission” to do a massive project (requiring multiple scholars) that will cover certain basic features of every state. Instead of our piecemeal focus that really comes down to individual authors’ interests, we could have a more systematic understanding of early prison history and probably learn some things we didn’t know about before (I have a current study on one such under-explored state and I’m finding things that are similar and things that are very, very different from what happened in other states and it’s fascinating).
This Prison History Decadal doesn’t mean scholars need to drop what they are doing and only work on this project. Instead, it means that interested scholars could plug into the project, make their proposal, and get funding to do the work. And if scholars are already doing something along these lines, they would need to apply for the funding and keep doing what they are doing. The result would be a more systematic overview of prison history—something that would let us test hypotheses or generate new hypotheses about how a really important institution became embedded, despite serious odds (early prisons were deeply controversial).
Now think about a Decadal for sociology. A major criticism people have mentioned is the patchiness of what is studied, especially what I call monocropping inequality studies. Race, gender, and sexuality are getting big attention these days, while religion (outside of “Christian nationalism”), military/war, and science/biology are not getting a lot of attention. The ASA’s suggested Intro to Sociology syllabus actually has a really nice description of the field’s major topics and questions. A Decadal Survey could even start with that layout and then have experts come up with key questions for each major topic (e.g., Institutions — Family, Institutions — Education, Institutions — Market, etc.). You can and should have questions on race, gender, and sexuality for each of these areas, but the key is they would be one of a dozen or more questions rather than the main question. Because there is far more to the world than just race, gender, and sexuality….
And importantly, the Decadal would be encourage question-driven projects. There’s a slowly growing trend of scholars starting with their argument instead of with a question. Sometimes it’s subtle and slopply, like starting your abstract with your finding instead of your question (and then never stating your question in your abstract), even if it’s somewhere in your paper. As an editor though, I saw a lot of manuscripts that didn’t have a research question—and in some cases, it wasn’t just a failure to articulate a question—I mean, they weren’t driven by a question. (Nor were they literature-intervention papers, where you can do that; these were empirical studies, except they weren’t true studies because they were leveraging evidence to support an argument.)
I also like the idea of vetting proposals. As an editor, I also saw a lot of projects that never should have seen the light of day. There were major research design flaws that were fixable if only the scholar had pre-circulated their project plan (or maybe they did and their advisor just wasn’t very good). Putting together a proposal, getting it vetted, and then competing with others would help with that. Scholars could still pursue their project even if it doesn’t get funding, but at least hopefully they will have gotten some feedback in the meantime (in exchange for the chance to get funding).
And the Decadal would tie all of this to resources. At the end of the day, when we talk about reforming academia, we need to take incentives seriously. Right now, the incentives are misaligned. But it’s also a good time to fix them because funding is seemingly so scarce. There is so much discussion about government intervention, but a safer way to do that would be to make funding priorities set by a panel of experts and then make money available to pursue those priorities.
And the Decadal doesn’t need to take up all the oxygen in the room. There wouldn’t be enough funding to fund everyone, so there would still be a chance for folks to pursue their weird/awesome niche projects (maybe even through other funding mechanisms), like a random study on early modern piracy or a study on fish markets that somehow unearth some useful piece of generalizable wisdom. I would hate to have a system that said you can only do this type of work (it’s why I’ve not jumped ship to a think tank—I want to be the final arbiter of what work I do). But it would help keep the field more balanced and less slapdash. And I hope doing so would improve the quality as well (since we’re getting some studies that aren’t just repetitive—the nth study on topic x—but just aren’t very good, but somehow they are getting published anyway).
It would also be nice for early career scholars looking for projects because there would be ready-made research questions and clear literatures laid out for them instead of having to come up with their own project (a gift for those trying to identify that first project).
So my proposal for fixing the field is to initiate a Decadal Survey, ideally with funding from the NSF or NAS. But even without funding, it would be a useful exercise. It’s a nice moderate proposal rather than some of the more extreme proposals out there. It wouldn’t fix everything (we have a lot of different problems, so we probably need a lot of different fixes). And it wouldn’t fix things quickly—there’s a lot of bad stuff that’s been institutionalized that will take a while to fix.
Am I optimistic that my proposal will change things massively? No. Why? Enough people in the field have to want to change—have to recognize that there is a problem and agree, at least to some degree, about its outlines. In sociology, I’m not sure there are enough people who feel that way, and they tend to be around retirement age or closer to retirement than to the start of their career.
We also don’t have a strong pipeline—at the level of graduate admissions and new faculty hires for the last decade or so, we’ve increasingly selected on activism/a commitment to “social justice” (with a rather narrow meaning). People who got in for the love of research are really struggling—grad students especially. And the training they are getting is far more mixed than in previous generations—some of it is far better and some of it is far worse. So I do not have high hopes for the next generation of scholars—we’ve left them in a bad spot, but they are also the future of the field.
And we might need to think bigger—we no longer have the monopoly on knowledge or expertise, and given our behavior, nor should we. If we’re going to do better, we need to think carefully about what is unique about universities and what we uniquely have to offer—where’s our edge?
But perfect can’t be the enemy of the good. We need a variety of fixes to combat a variety of problems in the field. This idea would hopefully help institutionalize systematicity and something akin to a scientific mindset.
(I’m rushing this post because I have to go drop off my dog and head to the airport, but I wanted to get this out. Apologies for the typos!)