Is it a problem?

Before we explain some of the causes of big theory’s decline, we must first address whether this is indeed a problem worth discussing. As should be clear, we see high-quality big theory as a good thing for the field, and, thus, we see its decline as a problem. Big theory is the resin that helps connect diverse subfields and topical spaces, bridging myriad case studies together. Such theories foster intellectual curiosity and debate; they energize the field; they provide new frameworks to apply, extend, test, or critique. Such theories are also associated with “big questions,” the types of questions that are not only important for policy but also, more simply, for our understanding of how our world works (Calavita Reference Calavita2002). For many of us, such theories are what made us excited about the field to begin with—the theories that gave some of us “goose bumps” or made us feel compelled to learn more (5). In a large sense, they are a recruiting tool for the field, in addition to an analytical tool for our research. They tell us what it means to be a law and society scholar and what our field has to offer the world. Thus, for multiple reasons, we view the dearth of powerful big theories as a disheartening and disappointing development. We also suspect that this dearth is one of the reasons behind a kind of boredom and even anomie that many scholars in the field feel, as we hear in panel discussions, discussant comments, and private, informal conversations at various annual conferences.Footnote ⁸

It is also important to clarify that our concern is with theoretical stagnation, not with stagnation in the field more generally. By many measures, law and society is a thriving field: its membership is growing, the topics covered have expanded, the research and researchers are more globally representative than they once were, and its ideas and concepts have moved well beyond its primary specialist journals into other journals. We know much more about law, broadly construed, in many more times and places than we did even a decade or two ago.

Against this background, the relative lack of theoretical innovation (as opposed to extension and application) appears even more striking. What novel insights have we learned from this expansion? What theories help us make sense of this diverse and eclectic array of findings? Where are the theoretical frameworks that help us link disparate parts of the field together? Where are the energizing theories that excite the whole field, generate significant debates, and help us to understand the law and legal phenomena in a new light? Given the massive expansion of the field, why are we seeing only a few examples of generative works, sometimes confined to the presidential addresses at the Law and Society Association (LSA) (see, for example, Nielsen Reference Nielsen2024), amidst a sea of works that offer smaller theoretical extensions instead of a whole host of competing paradigms? Are all the low-hanging fruit taken, and is there little left for new scholars to uncover? Without big theory, can we overcome the increasing tendency for scholars to silo themselves into their own subfields (or sub-subfields)? For all of these reasons, we see the decline of big theory as an important, problematic development in need of explanation.

Common explanations for grand or general theory’s decline

The decline of big theory does not stem from current preference (see the commentaries in Savelsberg et al. Reference Savelsberg, Halliday, Liu, Morrill, Seron and Silbey2016) nor from a lack of original ambition. As incoming editor of the Law & Society Review (LSR) in the early 1970s, legal scholar Marc Galanter (Reference Galanter1973, 7) wanted the field to generate “a coherent social scientific understanding of the legal process” (see also Silbey Reference Silbey2000, 870). And, yet, that venture halted at some point. To be sure, the field has changed tremendously over the years: the transformation of the original law and society project, the institutionalization of the field, the internationalization of law and society, and the rise of other national or regionally specific fields of law and society (see, for example, Trubek Reference Trubek1990; Sarat Reference Sarat and Sarat2004; Morrill et al. Reference Morrill, Edelman, Fang and Greenspan2020; Chua et al. Reference Chua, Engel and Liu2023). But that does not tell us why big theory has fallen out of favor or why law and society scholars have become less theoretically ambitious over time. In this section, we explore other scholars’ compelling explanations.

First, however, it is important to note that the decline of big theory—especially under the banner of grand or general theorizing—is not unique to law and society.Footnote ⁹ This style of theorizing lost its cachet across diverse fields in the twentieth century’s last decades. For example, its decline is well known within sociology. As sociologists Turner and Boyns (Reference Turner, Boyns and Jonathan2001, 353) have put it, “the term ‘grand theory’ now carries negative connotations as something that failed scholars like Talcott Parsons once did, a half century ago.” Noting the apparent contradiction with the field’s continued “worship” of the classic social theorists (frequently, the core of the sociology degree’s required reading), they explain that “it appears that we like our early masters to be grand theorists, but in the age of specialization, we stand in their shadows rather than on their shoulders.” More than its absence, the outright rejection of big theory has extended to other, interdisciplinary fields as well. As another example beyond law and society, several decades ago, science, technology, and society scholar Stephen Fuchs (Reference Fuchs1993, 948) noted, “[a]t present, the field of science studies is rather indifferent or even hostile toward general theory. It appears satisfied with adding case study upon case study, and then doubting the very possibility of knowledge and representation altogether.” Commentators have made similar criticisms of the field of organizational theory, which some argue has not seen significant theoretical development since the 1970s—simply, smaller-scale extensions—leading to a debate over the health of the field (G. Davis Reference Davis2015; Lounsbury and Beckman Reference Lounsbury and Beckman2015). Taking a different tack, globalization scholars Paul James and Manfred Steger (Reference James and Steger2014, 420) noted that the concept of globalization became popular “at the same time that generalizing theory—or at least ‘grand theory’—lost its pre-eminence in academia,” suggesting that scholars were turning to something like a grand theory (without using those terms) just as classic grand theories had been delegitimized. Thus, we are not alone in this experience.

These trends across the social sciences are well known to, and presumably influence, law and society scholars as they are often situated in multiple disciplinary and interdisciplinary fields. Indeed, in the early 2000s, multiple law and society scholars noted the decline of high-level theorizing across the social sciences and in law and society (see, for example, Calavita Reference Calavita2002; Cotterrell Reference Cotterrell and Sarat2004; Seron and Silbey Reference Seron, Silbey and Sarat2004). As Carroll Seron and Susan Silbey (Reference Seron, Silbey and Sarat2004, 30) explained it, “[o]ver the last decade or so, across the social sciences there has been a turn away from large-scale theory development and abstract modeling to more situated and contextualized analyses of sites of social action.” As law and society scholars incorporate social science into their research, they bring with it other fields’ distaste for grand or general theorizing.

More than importing these objections, however, law and society scholars have likely been responding to whatever changes caused this distaste to begin with. Indeed, a leading explanation that these scholars offered is that social change itself reduced the scholarly appeal of big theory. Drawing on Jean-François Lyotard (Reference Lyotard1984), legal theorist Roger Cotterrell (Reference Cotterrell and Sarat2004, 19) attributed this decline, and the “loss of faith in ‘grand narratives,’” to the advent of postmodernity and all that came with it. That is, scholars now live

These changes, Cotterrell (Reference Cotterrell and Sarat2004) explains, help us understand the cultural turn to the fine-grained, the particular, and the contingent that has dominated much of law and society research (see Seron and Silbey Reference Seron, Silbey and Sarat2004). For Cotterrell (Reference Cotterrell and Sarat2004, 19; internal citations omitted), the decline of grand narratives has resulted in “a new privileging of ‘local knowledge’ and a perception of the failure or pointlessness of all attempts to generalize broadly about social change or social phenomena.” Others describe these changes as a general declining faith in the social sciences as tools for good or tools to uncover truth (see, for example, Trubek Reference Trubek1990). Essentially, we are savvy enough today to recognize, as sociologist and then–LSA president Kitty Calavita (Reference Calavita2002, 6) did, that “there are probably no universal laws because there are probably no universals in a social world that is fragmented and forever shifting.” Instead of remaking big theory to accommodate this complexity, however, scholars tend to avoid anything resembling big theory, perhaps because the decline of grand theory, grand narratives, general theory, and other forms of high-level theorizing has other sources as well.

Grand theory has also declined across the social sciences for empirical, normative, pedagogical, and practical (structural) reasons that are well known to law and society scholars. As early as the 1950s, grand theory was coming under attack for being so abstract as to be virtually useless; calls to use a “sociological imagination” required its exclusion (Mills [Reference Mills1959] 2000). Feminist scholars joined the conversation to denounce high theory as highly abstracted as it utilizes the “fathertongue” that sanitizes women’s “lived experiences” (Smith Reference Smith1990). The move away from grand theories can also be credited to the rise of standpoint theory (P. Collins Reference Collins1986; Smith Reference Smith1990; Harding Reference Harding2009) and a general emphasis on highlighting lived experience, which is central to critical race theory as well and has been exploding in popularity across fields in recent years (see, for example, McIntosh and Wright Reference Mcintosh and Wright2019). Across these arguments, particularities and localization of knowledge are prioritized over theory from above, which critics argued resulted in abstracting or removing people away from their bodily experiences and felt realities.

As we shall discuss more below, there has also been a growing recognition of the micro–macro divide or the way in which theories may appear true at the macro level but do not hold up on the micro level and vice versa. However, whereas some other fields saw this conflict creating a need to explore connections between the two levels (see, for example, Kemeny Reference Kemeny1976; R. Collins Reference Collins1988), in others, it has been viewed as evidence of big theory’s failure. Relatedly, we know that many of the classic and foundational social theories were simply empirically wrong. Scholars have demonstrated multiple factual errors in classic grand theories, and many of their hypotheses have been falsified.Footnote ¹⁰ Although others have argued that we can still learn from and update these theories rather than abandoning them entirely (see, for example, Garland Reference Garland1990; Rojas Reference Rojas2017), it has become easy for some scholars to dismiss classic grand theories and even the project of grand theorizing. Moreover, graduate students are not taught how to theorize at the grand level (Swedberg Reference Swedberg2014)—arguably, a legacy of C. Wright Mills’s ([1959] Reference Mills2000) distaste for grand theory (Tarifa and Zhupa Reference Tarifa and Zhupa2014).

Combining both empirical and normative concerns, there is also a growing recognition that classic grand theories were Eurocentric and employed colonialist thinking (Go Reference Go2020). Many grand theories were concerned with the changes wrought by modernity (circa 1750), primarily on Europe and often in comparison to those societies that appeared (to white Europeans) perennially premodern. These biases—for example, seeing Indigenous societies as simplistic and primitive and European society as complex, civilized, and advanced—are partly responsible for some of the empirical falsehoods underlying these theories. However, for some scholars, these biases are also normatively problematic, further tainting the grand theory project. Grand theories are seen as employing not only inaccurate thinking but also outmoded, inappropriate thinking and assumptions. Indeed, the fact that classic grand theory is associated with long-dead, white, European men (W.E.B. DuBois was long excluded from the list of classic theorists) is sometimes viewed as problematic and further reason to dismiss the enterprise. Particularly as the last decade saw the rising practice of “decolonizing” our syllabi, which well-meaning scholars often defined as adding women and people of color to a syllabus (for an Indigenous critique of these and related symbolic practices, see Tuck and Yang Reference Tuck and Yang2012), teaching what was perceived as inaccurate, outdated classic grand theory became highly debated or even a liability.Footnote ¹¹

Finally, even if scholars wish to participate in the increasingly discredited enterprise, there are practical (and increasingly structural) reasons for scholars to avoid creating their own high-level, grand theories. For one, high-level theory is not necessary for a scholar to have a strong career or construct popular research as middle-range theory has become a powerhouse for theoretically minded scholars. Popularized by Robert Merton (Reference Merton1967) as a bridge between grand theory and detailed empirical study, middle-range theory allows scholars to pursue theoretically informed empirical research—our field’s gold standard today. Middle-range theory allows scholars greater flexibility to take into account the unique contexts of their research sites or highlight mechanisms that link broader context to the fine-grained particular, a possible bridge between the macro and the micro (see, for example, Morrill and Mayo Reference Morrill, Mayo and Susan2015, 20–22). This style of research is of course safer: it both engages with higher-level theories, giving it a certain amount of status in the field, and makes a theoretical contribution, albeit a small one. But safest of all, by being carefully detailed and heavily grounded in empirics, it is harder to argue with. The resulting “rich and nuanced” theoretical contribution “lack[s] the possibility of being refuted” (Besbris and Khan Reference Besbris and Khan2017, 148). By contrast, a higher-level theory runs the risk of being “nibbled to death” by scholars pointing out the myriad exceptions to an otherwise compelling theory—a point that historian and former LSA president Lawrence Friedman (Reference Friedman1986, 779) made nearly four decades ago but is still true today.

Middle-range theory’s ability to help scholars satisfy the reigning preferences for theoretically informed empirical research is related to other career considerations—namely, (increasingly) high-speed productivity. As Seron has noted, “[t]he pressures of academic production have been ratcheted up to a level that does not encourage the time it takes to read widely, reflect, and pause before entering the publishing cue—and, this all begins in graduate school itself where one is expected to have top tier publications prior to entering the job market” (Savelsberg et al. Reference Savelsberg, Halliday, Liu, Morrill, Seron and Silbey2016, 1032; see also Liu Reference Liu2015). Against these standard pressures, we can add the additional space and time needed for innovative theorizing. For many scholars, the resources needed to get there may not be worth the cost, particularly if there are few incentives to theorize at the grand level.

Another practical and structural consideration is the influence of funding and policy concerns on what scholars study. Law and society scholars have long cautioned about the influence of top-down exogenous forces on the field. Sarat and Silbey (Reference Sarat and Silbey1988) warned of the “pull of the policy audience,” which can influence not only what topics scholars choose but also how they understand the law, what methodologies they use to study it, and what type of theories they posit. We would add that writing for policy audiences—which these days means not only work commissioned or funded by governmental actors and non-governmental organizations but also studies that lend themselves to news coverage or that are useful for activists and advocates—does not lend itself to high-level theory, which can appear less relevant than an empirical result on some timely, narrowly defined practical question. Additionally, as Joachim Savelsberg, Ryan King, and Laura Cleveland (Reference Savelsberg, King and Cleveland2002) have illustrated in several studies, funding mandates can also shift the focus of and theories used in academic research; through funding opportunities, dominant political preferences can seep into research (see also Savelsberg, Cleveland, and King Reference Savelsberg, Cleveland and King2004). We would again add that funding mandates, with their focus on documenting and solving specific (funder-defined) problems as well as their tight timelines for results, do not lend themselves to high-level theory, nor do they require it. Finally, as higher education becomes more dependent on newsworthy research findings and fundable research programs, scholars may be subtly and not so subtly encouraged to think smaller.

It is worth noting that there may also be higher-level structural reasons for our field’s move away from big theory—namely, the maturation of the field itself (Fuchs Reference Fuchs1993). Essentially, we have spent several decades in a period of “normal science”—that is, of accumulating knowledge instead of identifying revolutionary new insights that change how we previously researched (Kuhn [Reference Kuhn1962] Reference Kuhn2012). As then-editors of the LSR Timothy Johnson and Joachim Savelsberg (Reference Johnson and Savelsberg2016, 6) put it, there has been “a shift” in the law and society field “from scholarly entrepreneurs to bureaucrats, from innovators to normal science scholars, and from generalists to specialists.” Indeed, although normal science has not dominated all of law and society’s subfields (Dudas Reference Dudas2004), it does seem to have descended upon law and society overall. As with middle-range theory, it is easier and safer—encouraged even (see, for example, Rubin Reference Rubin2021b)—to solve small-scale, and, therefore, manageable, theoretical or empirical puzzles, which is the staple of normal science, according to Thomas Kuhn ([Reference Kuhn1962] Reference Kuhn2012), an endeavor that does not require high-level theorizing. Again, this situation is not unique to law and society as other fields are maturing, changing, and facing similar pressures. Across the social sciences, “a new timidity is evident” (Turner and Boyns Reference Turner, Boyns and Jonathan2001, 353), most clearly found in “the proliferation of over-specialized theories” rather than in big theory (376).Footnote ¹²

The field’s maturation creates another structural contribution to big theory’s decline: as the range of knowledge grows, it becomes harder for scholars to keep up, encouraging them (by necessity) to focus on smaller and smaller slices of that knowledge instead of integrating across larger swaths of knowledge (see also Luker Reference Luker2008). Recall the point stated earlier that generating big theory requires reading a diversity of works, often in more than one discipline, and is thus more time expensive, which also means fewer publications: as the literature grows, reading widely becomes even harder, and big theory is further dis-incentivized. Indeed, a recent study reviewing research in multiple fields found that “growth of knowledge,” and the resulting increased burden in keeping up with it, results in less “disruptive” or innovative work (Park, Leahey, and Funk Reference Park, Leahey and Funk2023). We would argue that it is not just the burden of keeping up but also, in combination with the pressure to publish, the tendency to choose easier pathways to publication. We can see how this tendency further encourages scholars to think small: increasingly, scholars motivate their studies by reference to an empirical gap in the literature—that is, by the novelty of the context or population under study rather than by the theoretical contribution. In the pressure to publish amid a sea of articles, it is far easier to claim empirical, rather than theoretical, novelty. But the empirical novelty claimed often becomes smaller and more specific; it is harder (but more exciting) to generate innovative theory that spans empirical settings, but such work is not encouraged by a time-strapped, competitive environment. Together, these structural explanations may thus explain not only big theory’s decline but also its continued disappearance, and they are consistent with the general perception of theoretical stagnation in multiple fields.

Thesis: the grand theories of mass incarceration and the punitive turn

It is well established that punishment and society in its current form (for example, since its founding in the 1990s) took as its main focus the rise of mass incarceration and its attendant policies (see, for example, Garland Reference Garland2018). Beginning in the 1970s, incarceration rates across the United States began rising, eventually leading to levels that were historically and internationally unprecedented (Garland Reference Garland2001b). More internationally focused scholars sought to explain a growing punitiveness (in policies, rhetoric, and incarceration rates) perceived across various Western and, especially, English-speaking countries, particularly the United Kingdom and Australia. Whether focused on the United States or certain Western countries, scholars referred to these changes more globally as the punitive turn, the punitive revolution, or the new punitiveness (see, for example, Pratt et al. [Reference Pratt, Brown, Brown, Hallsworth and Morrison2005] 2013; Savelsberg Reference Savelsberg2018). For many scholars publishing around 2000, there was a clear shift in how punishment functioned across the Western world, what some called a new “postmodern” or “late modern” style of punishment (see, for example Simon Reference Simon1995, Reference Simon2001; Garland Reference Garland1996; Lynch Reference Lynch2000a, Reference Lynch2000b; O’Malley Reference O’Malley2000; Pratt Reference Pratt2000a, Reference Pratt2000b; Vaughan Reference Vaughan2002). One early account bears special mention due to its longevity and influence: Malcolm Feeley and Jonathan Simon (Reference Feeley and Simon1992) described what they saw as the “new penology” in which risk management and general managerial tendencies had taken over important facets of the criminal justice system, leading to a shift from diagnosing and treating troubled individuals to controlling and managing risky populations.

Explaining these puzzling phenomena became the central focus for scholars across a range of disciplines—sociology, criminology, political science, anthropology, and law—including many law and society scholars. In the late 1990s and early 2000s, punishment and society scholars developed multiple influential accounts that are as close to grand or general theories as most scholars get in recent decades—what we are calling “big theory” given their ambitious explanations of nationwide or international penal trends linked to social phenomena at a similar scale. Feeley and Simon (Reference Feeley and Simon1992) explained the new penology by reference to significant changes in society at large, including shifts in the economy, labor market, poverty levels, and (relatedly) systems of discipline available to control the expanding “underclass.” Likewise, turning to social theory, David Garland (Reference Garland2001a) offered his theory of the “culture of control,” arguing that large-scale changes affecting the Western world (but especially the United States and the United Kingdom)—including globalization, economic changes, political changes, growing crime rates, and growing uncertainty generally—made governments incapable of protecting their citizens from crime (and other social harms) and delegated the work of crime control to citizens. Citizens, now especially wary of crime, invested in (superficial) crime prevention strategies. Governments, meanwhile, simultaneously overcompensated for their own weaknesses by overperforming superficial crime control functions such as incarceration and greater police presence (for an international account of the role of existential anxiety and punitiveness, see J. Young Reference Young1999; for a theory that incorporates environmental threats with other existential threats, see M. Davis Reference Davis1998). Similarly, Loïc Wacquant ([Reference Wacquant1999] 2009a, Reference Wacquant2009b) argued that large-scale changes in Western societies (especially but not only the United States), including the decline of the welfare state, led to an increase in joblessness and poverty, leading political and social elites to respond with harsher criminal justice policies and restricted welfare policies (and new, more punitive workfare policies) to contain and control this undesirable and politically dangerous population (see also Beckett and Western Reference Beckett and Western2001). In these and other accounts, the United States was viewed as the site with the most powerful social causes and, therefore, the largest penal effects—mass incarceration and its epiphenomena.

Focusing more on the United States itself, scholars beginning with Katherine Beckett (Reference Beckett1997) developed theories that explained how political changes within the country, following the successful civil rights movement, led politicians to use crime politics as a tool to get elected: politicians could use crime control as a dog-whistle to curry favor with racist white voters. Building on this idea, Simon (Reference Simon2007) also showed how the success of “tough on crime” politics for politicians spilled over into schools, workplaces, and families, shaping the expectations for management and leadership and ultimately changing the policies, choices, and practices that structured American lives.

Toward the end of this fertile period, the rate of big theoretical accounts slowed. Even so, one group of scholars continued to take seriously the idea of a significant change that needed explanation. However, instead of using mass incarceration as a dependent variable to be explained, they saw it as an independent variable whose effects needed to be documented and theorized. Thus, these scholars demonstrated the effects of mass incarceration on racial inequality in the country (and the policies that created and sustained it) (Western Reference Western2006); the life course of undereducated Black people, the hardest hit group (Pettit and Western Reference Pettit and Western2004); incarcerated people’s neighbors, children, and families’ material and social circumstances (Clear Reference Clear2007; Wakefield and Wildeman Reference Wakefield and Wildeman2013); voting and elections (Manza and Uggen Reference Manza and Uggen2006); and the labor market (Western and Beckett Reference Western and Beckett1999). In doing so, they linked a substantial penal trend to other aspects of society, now with the causal arrow pointing away, instead of toward, mass incarceration.

The last gasp of big theory emerged later, for a few years, when a small group of scholars focused on the apparent decline of mass incarceration and its underlying policies like tough-on-crime politics, which were often linked to the intervention of the economic recession and the growing cost of these entrenched penal policies (Clear and Frost Reference Clear and Frost2014; Gottschalk Reference Gottschalk2014; Aviram Reference Aviram2015; Dagan and Teles Reference Dagan and Teles2016). Again, the focus was linking large-scale penal developments to large-scale developments in society generally.

Antithesis: the empirical case against big theories of punishment

Starting almost at the same time as the big theories mentioned above but more significantly by the late 2000s and 2010s and continuing into today, multiple strands of research have questioned these earlier theories and the assumptions on which they were built, including their grandness and generality. Complexity, often used as a vehicle to challenge or simply sidestep the need for high theory (see also Healy Reference Healy2017), became the watchword of this new genre. For these later scholars, the true picture was more complicated and nuanced than such earlier theories could allow or account for. These newer studies identified important limitations in earlier accounts and greatly extended our understanding of penal trends and phenomena. Their critiques fall into multiple categories, including identifying penal variegation, geographical or jurisdictional variation, and gaps between theory and practice, but they are united in undermining some of the assumptions or claims of the earlier big theories. While these studies made important theoretical contributions to the field, and they reflect some of the best punishment and society work published in the last several decades, they are indicative, in our opinion, of a move away from big theory. Rather than offering new causal accounts, they offer more detailed descriptions of penal change.

Little synthesis: a case of stalled academic dialecticism

With these useful critiques of the generalizing theories of mass incarceration and the associated punitiveness, scholars could generate new theories that complicate earlier narratives but still generate general theories of penal trends. Under a healthy academic dialecticism, we should see a new (synthesis) stage characterized by this sort of productive combination of the two earlier stages of big theories (thesis) and the critiques thereof (antithesis). However, punishment and society scholarship currently lack the expected proliferation of synthetic theories that blend the two approaches to research. Instead, we are stalled in the critique phase, offering more (and more elaborate) accounts of punishment at the micro and meso level (often showing errors in earlier macro-level accounts) without returning to research at the macro level that enables big theory.

Importantly, while there is no proliferation of such theories, there are a few exceptions in which punishment and society scholars have produced high-level synthetic theory—that is, offering general accounts of macro-level phenomena while recognizing the messy complexity at the micro and meso levels. Michael Campbell and Heather Schoenfeld (Reference Campbell and Schoenfeld2013) created a political sociology of punishment that blends the state-level approach with temporal trends at the national level to account for changes in US penal policies over the last half century (see also Schoenfeld and Campbell Reference Schoenfeld and Campbell2023). Looking at penal trends across the country over US history, Philip Goodman, Joshua Page, and Michelle Phelps (Reference Goodman, Page and Phelps2015, Reference Phelps2017) offered an “agonistic” account: using Bourdieusian field theory (see Page Reference Page2011, Reference Page, Simon and Sparks2012), they show how penal change results from shocks to the penal field that shift the resources and influence of various penal actors, each with their own goals and motivations for promoting one penal policy or another. Their account thus reconciles how such conflict over penal policy, which often shapes the messiness at the micro and meso levels, can exist when the national picture seems so coherent. Ashley Rubin (Reference Rubin2015, Reference Rubin2019) applies neo-institutional theory to penal policy, arguing that temporal and spatial variation in penal trends, as well as gaps between penal policy and punishment in practice, can be explained by diffusion trends of what she calls “penal templates.” Using examples throughout US history, Rubin demonstrates that these templates are innovations that begin in some states, often at times of great social upheaval that is visible at the national level, and spread to other states around the country. Even those states that do not necessarily need such tools adopt them anyway to secure their legitimacy by conforming to penal trends. This work thus theorizes how social changes can have an impact, but it is mediated by field-level dynamics (see also Rubin Reference Rubin2021a).

Most recently, two scholars have turned to international comparisons rather than historical change to make sense of American penal exceptionalism. Lisa Miller (Reference Miller2016) compares the United States, the United Kingdom, and the Netherlands to explore the role of different political institutions in mediating the impacts of social changes on penal politics and policies. Garland (Reference Garland2020) theorized that the extreme levels of punitiveness in the United States reflect a globally unique combination of weak social controls (leading to high levels of violence) and a preference for strong penal controls (which are weak preventers of crime). These theories represent some of the few exceptions in which scholars attempted high-level theorizing in the last decade or so.

Notably, Garland (Reference Garland2018, 14), the field’s founder, is optimistic about these developments, seeing emerging theories as just the beginning. Pointing to the work of Campbell and Schoenfeld (Reference Campbell and Schoenfeld2013) and Goodman, Page, and Phelps (Reference Goodman, Page and Phelps2017), he explains that “second-generation scholars are beginning to take stock and explore the broader consequences of their historical research, developing new syntheses and rethinking more general historical narratives and sociological accounts in the light of them” (Garland Reference Garland2018, 14). But it is notable, given the growth of the field, that, in his survey of where punishment and society has gone, Garland could only point to a handful of scholars doing this work.

Despite Garland’s optimism, we argue that, given the massive growth of the subfield, there should be far more scholars and theories to point to rather than a handful of exceptions. Indeed, the insights that scholars have raised over the last decade or two, which trouble the earlier grand theories of mass incarceration, should have provided enough inspiration to establish far more new grand theories that take those critiques into account. Such new theories could also move beyond theorizing mass incarceration. Significant changes have taken place that could be theorized at the macro level with grand theoretical narratives, including the (heterogeneous) drop in incarceration rates, the return of tough-on-crime politics, the (relatively) widespread or at least newly visible calls for decarceration or abolition, the greater public awareness of mass incarceration, the international exportation of penal policies and practices, the growing overlap of immigration control and criminal justice, and the nascent popularity of Scandinavian-style prisons within the United States (and other countries). Nor are these developments too new for theory development: while some of these changes are still fairly recent, others are entering their second decade, suggesting that scholars have had ample time to theorize them. What explains the proportional dearth of such theories within the subfield of punishment and society?

Beyond exceptions: treating complexity as a challenge, not a roadblock

We argue that critiques of the last two decades, in combination with the other factors we highlight above, have effectively made contemporary scholars overly hesitant to return to big theory: punishment scholars have effectively made the case that punishment is a complex social institution and that it is difficult to theorize in generalizable ways (Garland Reference Garland1990, Reference Garland2018). It is not just a general distaste for grand theory and its associations with long-dead colonialist European men or a general turn away from general theorizing; in a context in which demands for research are higher and the expectations for theoretical payoffs are lower, the incentives to demonstrate how big theories are wrong far outweigh the incentives to generate new big theories. While the first phase of punishment and society research witnessed scholars generating big theories relating penal and social change that were reminiscent of the grand theories of old, the subsequent critiques have doubled down on penal complexity and the problems with big theories. Increasingly, scholars have turned to analyzing smaller scales where empirical and theoretical accuracy stands a greater chance of success. The result is much smaller, incremental improvements in the tradition of normal science rather than the exciting, but risky, high-level theories. Instead of taking a big swing that could be generative for the field or that may miss big, scholars are taking smaller swings that are more likely to achieve modest levels of success without doing much to move the field forward (for example, offering more details and nuance but not changing our understanding). In a subfield that is so focused on micro- and meso-level phenomena and middle-range theories, often disconnected from each other or a larger framework, we wish to see more work like that generated by some scholars aiming for complete theories pitched across levels (including the macro level) and intended to be more generalizable as discussed above (see, for example, Campbell and Schoenfeld Reference Campbell and Schoenfeld2013; Goodman, Page, and Phelps Reference Goodman, Page and Phelps2017; Rubin Reference Rubin2019; Garland Reference Garland2020; Schoenfeld and Campbell Reference Schoenfeld and Campbell2023). Ultimately, we urge scholars to view the complexity of punishment (and legal phenomena generally) as a challenge to theorize rather than backing away in defeat.

Returning to the larger field of law and society

We have illustrated the problem using the subfield of punishment and society, but this situation is not unique to punishment and society, although, as a subfield, it may be easier to see. Across law and society, a similar dynamic has taken place, although with proportionately fewer attempts (over the course of law and society’s history) at general theories of law and beginning much earlier than in punishment and society. Even writing multiple decades ago, legal historian Lawrence Friedman (Reference Friedman1986, 779) summarized it well: “Grand theories do appear from time to time, but they have no survival power; they are nibbled to death by case studies.” Moreover, theoretical frameworks that have been popularized in law and society and that have generated the most research—for example, legal consciousness, legal pluralism, legal cynicism, procedural justice—tend to embrace the micro level rather than the macro level and prioritize messy variation rather than offering more general theories (for exceptions that aim higher, see Laurie Edelman’s [Reference Edelman2016] theory of legal endogeneity and the theory of relational rights put forth by Laura Beth Nielsen [Reference Nielsen2024]). In some law and society subfields, critique may be less common than applications and minor extensions of existing theory without the creation of new theoretical frameworks. The result in some cases is that, instead of interesting and energizing debates between competing perspectives, we see a kind of watering down of the original theory in less incisive applications of the original, as Silbey (Reference Silbey2005) noted of the highly popular legal consciousness framework two decades ago (for an exception, see K. Young Reference Young2014; Young and Chimowitz Reference Young and Chimowitz2022). Indeed, Silbey’s call for contemporary legal consciousness studies to move beyond the experiential level and to tether consciousness to the continuation of hegemony, as earlier studies did, which could have enabled big theory, has largely gone unheeded (Heyer, Rubin, and Talesh Reference Heyer, Rubin and Talesh2025). Indeed, some legal consciousness scholars defend this development, noting that the untethered version has enabled the extension of the concept to more diverse populations and settings, thereby enabling its explosive growth (Chua and Engel Reference Chua and Engel2019). This pattern is common in other fields like sociology “where concepts become less and less specific as they are applied to more and more disparate research projects” (Besbris and Khan Reference Besbris and Khan2017, 148). As in sociology, when new extensions to existing theories emerge in law and society, they resemble a kind of Zeno’s theory, with progress becoming increasingly incremental.

As we have illustrated with our case study of punishment and society, complexity and nuance have become the watchwords of these new studies, which carve out novel variation rather than crafting theoretical integration. Indeed, the legal consciousness literature offers a useful example of the same dynamic that we show in the punishment and society subfield. Most such research is incremental, enumerating the many different legal consciousnesses that exist, the different ways in which they shape and are shaped by identity, the many ways in which people resist the law (often without meaningful success), and the many norms that prevent someone from mobilizing the law (Chua and Engel Reference Chua and Engel2019). Where are the bold claims? Where are the full-fledged theories that unite the many different consciousnesses, identities, strategies, and norms and that explain how they fit together or work against each other, under what conditions, and why?

Indeed, it is worth pausing and asking whether law and society does not lend itself to big theory. Given the history of the field and the greater role of legal realism with its middle-range focus than grand social theory, one could argue that law and society is not conducive to big theory, perhaps explaining the dearth of grand theory that many important law and society figures have bemoaned, as illustrated above. However, we argue that there is nothing inherent to law and society that should make big theory repugnant or less useful. Instead, analyzing social and legal change—both whether and how law can bring about social change or how social change impacts the law (see, for example, Rosenberg Reference Rosenberg1991; McCann Reference McCann1994; Edelman Reference Edelman2016)—which is such a key consideration in the field, lends itself to big theory. Meanwhile, those subfields focused on the micro level, like legal consciousness, could contribute to these theories by linking up micro-level developments with macro-level developments at a broader scale instead of carving out more variation in narrower contexts.

Because so few scholars are rising to meet that challenge, however, the field has become rather lopsided with much more work focused on the middle range, often explicitly or implicitly motivated by criticizing prior big theories, than on generating complete theories, let alone big theories. To be sure, there will always be fewer big theories than applications, extensions, or critiques. This ratio represents a balanced field or a healthy intellectual ecosystem: as noted above, an important function of big theories is to generate debate in the field. A related function is to create a set of hypotheses or expectations to test in diverse contexts, creating research agendas for other entrepreneurial scholars, especially junior scholars looking for a gateway project into the field. A properly functioning academic dialecticism offers the excitement that follows the emergence, initial application, and tweaking of new theoretical frameworks and, ultimately, the competition of multiple frameworks. But, at some point, the field becomes saturated, and the pace of new insights slows, each becoming too incremental to generate excitement, and the field is no longer a healthy ecosystem. As the field becomes increasingly lopsided, producing more of the same, often within specific silos, it can become rather tedious and, ultimately, dangerous for the field. That situation is what we have called a case of stalled academic dialecticism, which we argue characterizes our field.