Should More Criminologists “Build Stuff?”
Andrew Wheeler’s recent post “Build Stuff” offers a provocative critique of academic criminology’s apparent disconnection from practical applications. Wheeler argues that criminologists should replace their “ivory tower” theorizing in favor of building more tangible products (e.g., apps; algorithms; interventions) that directly improve criminal justice operations. He laments that much of criminology research, even seemingly applied research like policy and program evaluation, is “boring” and fails to fundamentally change practical implementation.
We appreciate Wheeler’s frustration and his call for greater practical relevance, and we too have recently called for reforms in response to our perceptions of the field’s stagnation (see here and here). Below, we offer three main reactions to his post. First, while “building stuff” can drive scientific progress, so can theory-first approaches and careful observation. Second, solution-oriented research carries its own risks, including premature application of unvalidated findings. Third, we think the “boring” nature of much criminological work stems from deeper methodological issues – what we call a “precision crisis” – that require different solutions than simply building more technological applications. In fact, we think these deeper issues are primarily responsible for turning many of our field’s scientific publications into “boring” papers that serve little purpose beyond that of “Monopoly money” status tokens rather than genuine scientific currency or theoretical “money in the bank”.
Wheeler’s post struck a nerve with us because we’ve been grappling with questions about the nature and purpose of social science and relationship between “pure” and “applied” science since our first week in graduate school in 2004. We entered a sociology program just as Michael Burawoy was promoting “Public Sociology” but then studied under Charles Tittle, who wrote perhaps the most potent critique of public sociology. Upon entering grad school, we were both inclined toward public sociology and, like Wheeler, we wanted to “make the world a better place.”1 During an organized debate in our orientation week, Tittle argued that public sociology deviates from fundamental scientific values and is not the best way to learn about the world – views that initially took us aback. While we’ve both become more aligned with Tittle’s view over time, connections between scientific rigor, progress, and application have remained central to our thinking.
Ultimately, we argue for a pluralistic approach to social science and criminology that certainly recognizes the need to “build” new things, though we do not agree that those new things necessarily need to have direct practical relevance from the start. At the very least, Wheeler’s post spurred us to write a blog to discuss some topics we have also been wrestling with for a long time and have started addressing in recent papers. In a way, we suppose that means we are also “building” a brand, for better or worse.
The Old “Engineering” Approach to Science
Wheeler’s call for building things in criminology has a long history in criminology and social science. In criminology specifically, we’ve seen this approach in initiatives like CompStat (police data-driven management systems), the development of risk assessment instruments like COMPAS, and early intervention programs like the Kansas City Preventive Patrol Experiment, which are all examples of criminologists essentially building practical tools to solve immediate problems.
Beyond criminology, Duncan Watts similarly argued social sciences suffer from an “incoherency problem” caused by persistent emphasis on “the advancement of theories over the solution of practical problems.” Like Wheeler, Watts urged more social scientists to adopt “solution-oriented” approaches that prioritize practical problem-solving over theoretical development. Charles Tittle described such philosophies as “problem-solving” or “engineering” approaches to science.
When a discipline appears stagnant, with slow theoretical progress and/or academic work that appears disconnected from real-world concerns, it makes sense that critics would call for more “practical” work that produces immediate, tangible results. After all, engineering approaches have indeed catalyzed impressive scientific advances. The history of science offers compelling examples of progressive problem shifts following solution-oriented applications. Consider the development of the steam engine, where practical challenges with improving its efficiency directly led to the creation of the field of thermodynamics. This was not merely engineering applying existing scientific knowledge; it was engineering actively generating new scientific understanding by revealing the limitations of prevailing theories of heat.
Even Albert Einstein, the quintessential “ivory tower” champion of theoretical physics, benefited enormously from his immersion in practical patent reviews. During his seven years at the Swiss Patent Office (1902-1909) and before finally being granted admission into the academic ranks, Einstein examined hundreds of applications for mechanical and electrical devices. This exposure to practical engineering problems, particularly those involving electromagnetic signaling and clock synchronization, directly influenced his revolutionary insights about space, time, and simultaneity that became the foundation of special relativity. Einstein himself acknowledged that his patent office work sharpened his critical thinking and provided the conditions necessary for his theoretical breakthroughs. This experience underscores how deep engagement with “building things” (patent applications) influenced Einstein’s theoretical physics. More recently, the practical need to share particle physics information led National Lab scientists to install the first web server in North America, kick-starting the development of the World Wide Web, which revolutionized scientific collaboration and data dissemination. So, yes, the “build stuff” approach to science can work.
Other Approaches Also Work: The Power of Theory and Meticulous Observation
However, the history of science also demonstrates that progressive problem shifts do not exclusively follow solution-oriented or engineering approaches. As we note in our recent pre-prints (here and here), the so-called “ivory tower” theory-first approach boasts an impressive scientific track record too, as does a meticulously detail-oriented description approach focused on documenting “crucial facts.”
Take, for instance, Charles Darwin’s theory of evolution, which emerged not from attempts to solve practical problems as much as it did from years of careful observation, specimen collection, and theoretical synthesis. Or consider how the field of genetics developed from Mendel’s seemingly esoteric yet remarkably persistent experiments with pea plants, work that had no immediately obvious practical applications but revolutionized the understanding of heredity. The Copernican revolution is a prime example of a theory-first approach, where Nicolaus Copernicus, driven by theoretical dissatisfaction with the complexity of the Ptolemaic system, proposed a heliocentric model based on a reinterpretation of existing data, not new observations. This major conceptual shift laid the groundwork for future advancements.
Meticulously precise observation and the discovery of “crucial facts” have also been foundational. Dissatisfied with the inaccuracies of existing models and degree of imprecision in contemporary measurements, Tycho Brahe famously “built things” – larger, better-calibrated instruments for unprecedentedly precise astronomical observations – because he though better data could help reject the dominant heliocentric theoretical model and support his alternative geo-heliocentric (Tychonic) model. Brahe’s collection of more precise “crucial facts” provided data that contradicted Aristotelian and Copernican cosmology, which was crucial for Kepler’s later development of a more accurate theoretical model based on elliptical orbits. Galileo, using the newly invented telescope, observed crucial facts like Jupiter’s moons and Venus’s phases, directly contradicting traditional cosmological assumptions. Here, “building things” for scientific (observational and theoretical) aims rather than direct practical purposes was essential to scientific progress.
Indeed, as Paul Feyerabend argued, major scientific advances have come through diverse approaches – sometimes through rigorous hypothesis testing, sometimes through serendipitous discovery, sometimes through practical problem-solving, and sometimes through pure theoretical speculation. Despite caricatures to the contrary, his “anarchistic” epistemology was not anti-science but rather a recognition that scientific creativity cannot be constrained to any single methodological approach.
The Dark Side of “Building Stuff”
Moreover, solution-oriented or engineering approaches are neither necessary nor certain catalysts for progressive science, and some applications have left considerable harm in their wake. The history of “applied” social science offers sobering examples of how problem-solving imperatives can distort research priorities and produce ethically questionable outcomes. A blind faith in “scientism,” or the belief that the scientific method alone can solve all human problems, has historically led to disastrous outcomes, particularly when applied without robust ethical scrutiny.
Most criminologists are familiar with the Eugenics Movement in the early 20th century U.S, in which individuals were categorized into superior and inferior races based on “unfit” qualities. Widely accepted by academics and popular media, these bigoted practices conducted under the ruse of “science” led to solution-oriented policies such as forced sterilization and racial exclusion. It was only discredited after the Holocaust, which carried these “scientific solutions” out to their horrifying conclusions. But modern criminology offers plenty of examples of solution-oriented approaches producing contested and potentially harmful outcomes beyond historical forced sterilization programs. Consider, for examples, debates and legal challenges surrounding potentially discriminatory practices justified by “objective” risk assessment tools in criminal justice applications like policing or pretrial detention, or misidentification and other issues arising from criminal justice applications of facial recognition software.
To What (or Whose) Purpose is Criminological Science?
This brings us to an important tension within Wheeler’s argument – the implicit assumption that the proper (or non-boring) job of a criminologist is to build tools for criminal justice agencies. Wheeler celebrates examples like Truleo (police body camera analysis), automated crime reporting systems, and BOLO distribution platforms, which are all technologies designed to enhance the operational capabilities of law enforcement and criminal justice institutions. While Wheeler frames this as simply making criminology “useful,” these particular engineering applications are useful for a particular purpose.
The technologies Wheeler highlights primarily serve to expand the reach and efficiency of criminal justice agencies rather than, for example, addressing root causes of crime or promoting broader social welfare in other ways. This orientation implicitly accepts the current framework of criminal justice as given and focuses on optimizing its operations rather than questioning its fundamental assumptions. We suspect our more critically-oriented colleagues may take some issue with this.
But engineering applications conducted under more “progressive” banners also are not without issue. Consider, for instance, the rapid and widespread adoption, monetization, and institutionalization of “implicit bias” testing and training before the science was properly established (see, e.g., here, here, here, and here). Or, similarly, consider how academics who promoted “ban the box” movements to reduce barriers to employment for previously incarcerated individuals might have institutionalized ineffective policies and perhaps even unwittingly exacerbated racial discrimination against law-abiding racial minority job seekers. These rushed translations from early research findings to policy interventions occurred largely because the research seemed to offer technical solutions to racial biases in policing or post-release employment barriers. Now, those scientific literatures face serious conceptual, practical, and replication-based concerns, yet their policy applications may have carried substantial fiscal and social costs on the way to becoming deeply entrenched in institutions.
Uncritical “engineering” applications, whether they serve traditional law enforcement goals or supposedly progressive reform agendas, risk causing more problems than they solve - particularly when our relevant scientific knowledge is limited, as is often the case in social science. As such, the implicit argument that the proper job of a criminologist is to “build things” (whether for the security/control state and/or for progressive causes) raises significant ethical implications for a field that directly impacts human rights and liberties.2 One proposed solution, offered by Jennifer Doleac, is to “fail fast” – that is, try different things and rigorously evaluate them in order to prevent prolonged failed policy. While that is a mindful approach, we think that the risks extend beyond criminologists single-handedly creating harmful policies to also encompass broader scientific concerns – that a prominent focus on “building stuff” may constrain our imagination about what problems are worth solving, what (or whose) interests “scientific” research should serve, and careful consideration about what we really do and do not know (and thus can even imagine effectively building without eliciting dire unintended consequences).
Detour: Are Scientific Papers “Just A Distraction?”
Before getting back to what we think criminologists might do to make social scientific output more useful and less boring, let’s take a brief detour to address an additional issue raised in Wheeler’s post: He argues that scientific publications “are not what matter,” that “papers are a distraction,” and the “applications are what matter.” He claims that the “biggest waste currently in academic criminology work is peer reviewed papers” and that “[o]ur priorities as academics are totally backwards” because “[w]e are evaluated on whether we get a paper published” rather than on “whether we make the world a better place.” In no uncertain terms, he states: “Papers by themselves do not make the world a better place.”
Wheeler’s frustration with academic criminology’s insularity and irrelevance is understandable and, in many ways, justified. With the exponential increase in scientific publications, we think our field (like many others) has certainly produced too much low-quality research that serves little purpose beyond individual career advancement and institutional status.3
With that said, we think it is worth deviating a bit here to defend mass publication and the “manuscript culture” of academia, which may have been essential to revolutionary scientific progress and, by fostering replication efforts across increasingly expansive scientific communities, even to the invention of science itself. The invention of the printing press exemplifies how building technological tools can radically transform scientific knowledge and practice. It enabled exact reproduction of charts and figures, facilitated rapid dissemination of observations, and allowed for the systematic comparison and verification of data across different copies. In doing so, it democratized knowledge and even fundamentally changed how knowledge was created, verified, and challenged beyond historical dissemination of existing authority-based knowledge. Meanwhile, written documentation of research methods, findings, and theoretical arguments allows for cumulative knowledge building across generations of scholars. It enables replication, criticism, and refinement of ideas in ways that purely applied projects cannot. Though our students often find them boring, the tedious work of literature reviews, methodological refinements, and theoretical elaborations provides the conceptual infrastructure upon which scientific knowledge accumulation and practical applications ultimately depend.
Dismissing this infrastructure as useless or merely a stage for academic careerism risks discarding the scientific wheat with the prolific paper chaff. In short, papers by themselves are not useless. However, we agree with Wheeler’s underlying sentiment that a paper is not an end-in-itself. Rather, a paper’s contents should determine its worth – via its contributions to rich observational description, logically- or empirically-based theoretical improvements, descriptions of severe tests of theories, descriptions of effective or ineffective applications, and ultimately to scientific understanding. As our blog and preprints demonstrate, we also celebrate emerging forms of publication beyond traditional academic journal articles. Useful (and frequently less boring) scientific communication today extends beyond the status-dominant peer-reviewed journal to encompass preprints, blogs, podcasts, conference presentations, and collaborative platforms, and continued efforts to “build” new scientific communication forms may be essential for overcoming structural constraints imposed by traditional scientific publishing forms.
So, we want criminology’s collective papers to be less boring and more useful, too! But we wonder about the degree to which more criminologists building stuff is a scientifically promising or even desirable solution. Ultimately, those new tools should be evaluated, at which point we may find ourselves returning full circle to “boring” papers reporting potentially weak or vapid results of those evaluations. In our view, it is not so much the published paper that is the problem here. Rather, we believe the field needs a more fundamental rethinking of what is routinely reported in our papers - that is, of what constitutes rigorous scientific knowledge. Our recent work identifies specific issues and suggested targets for reform that could make criminological research both more scientifically robust and more genuinely useful for practical applications.
Beyond “Monopoly Money” Publications
Returning to Wheeler’s call for more criminologists to “build stuff,” we think an even more widespread adoption of the already-popular engineering approach to criminological science risks overlooking ethical responsibilities and motivations of social scientists as well as the nature of scientific progress. As Feyerabend and others have cogently argued, science advances not by methodological fetishism but through diverse approaches, and any attempts to privilege a single methodology over others risks impoverishing rather than enriching our understanding. So, instead of simply telling criminologists to “build stuff,” we wish to encourage a more thoughtful integration of different research approaches.
More fundamentally, we believe criminologists should collectively identify core questions we genuinely want answered and confront the constraints imposed by our current theoretical and research approaches on answering them. Ultimately, this confronts us with what we might call a methodological pluralist’s dilemma: We want to embrace diverse research approaches (theory-building; applied work; descriptive studies) because the history of science shows that breakthroughs come from many directions, but we also want to avoid philosophical relativism and embrace rigorous standards that maximize the chances of scientific progress rather than mere proliferation of equivalently useless studies.
We should note that our methodological pluralism stems from our understanding of the history of successful sciences and our uncertainties regarding whether the social sciences generally, and criminology specifically, can ever be considered “successful” like other disciplines (e.g., physics and biology). Additionally, it is likely this very pluralism that kept us from putting our own ideas on the problems of criminology into writing for so long, and it is why those ideas do not necessarily lend themselves to clear solutions for how to do criminology better.
Back to Building our Brand
In our recent preprints, we argue that criminology struggles with a “precision crisis,” leading to a proliferation of “Monopoly money” publications rather than genuine scientific currency. This means much of our knowledge is based on imprecise descriptions, vague theoretical predictions, and analytical practices that obscure data. To move beyond this and make criminological research truly impactful and perhaps less “boring,” we need to reimagine the form of what constitutes social scientific knowledge.
Here are some examples that we advocate in our papers:
Prioritize Precise Quantitative Description of Fundamental Empirical Regularities. Instead of documenting vague directional correlations, criminology should focus on precise, quantitative descriptions of concrete phenomena at the unit level – that is, actual counts, rates, and distributions. Imagine a theory predicting the exact number of burglaries in a neighborhood with specific characteristics, rather than just “more crime.” Deviations from such precise predictions would be true anomalies demanding theoretical refinement, much like Kepler’s precise laws of planetary motion constrained Newton’s theory of gravity. This is the “money in the bank” of science.
Subject Theories to Risky Tests and Focus on Anomalies. To achieve genuine scientific progress, theories must be subjected to genuinely “risky predictions” that are specific enough that many potential empirical outcomes would be inconsistent with the theory. Our current reliance on weak statistical tests and the “crud factor” (the phenomenon that “everything correlates to some extent with everything else” in social science) makes it easy for vague directional predictions to appear significant, creating an illusion of theoretical support. For example, Jon’s re-analysis of a self-control study, which showed an impressive aggregate correlation, revealed that the theory failed to predict correctly for nearly 40% of individual cases. These systematic anomalies, typically invisible in aggregate reports, are crucial for driving theoretical development.
Embrace Critical Measurement Science and Logical Derivation Chains. The translation from abstract theoretical concepts to measurable indicators is often the weakest link in our “logical derivation chains.” As Paul Meehl argued, imprecise theoretical constructs, problematic auxiliary theories about measurement and sampling, and unchecked analytical assumptions create “loose derivation chains” where empirical failures provide little diagnostic information. We must meticulously document these derivation chains and critically examine whether our standard psychometric models adequately represent complex traits, rather than assuming measures simply “work.”
Rethink Data Generation for Precision and Discovery. Advancing beyond standardized effect sizes requires strategically generating data designed to reveal complex patterns and enable precise description. Criminal behavior demands data with temporal, spatial, and behavioral granularity beyond what most datasets provide. Studies should be designed to capture specific patterns that clearly distinguish between competing explanations, rather than merely supporting vague directional hypotheses.
Develop and Test Computational Models of Theories. Formal computational models can force theories to be precisely specified and enable rigorous comparison between theoretical predictions and empirical observations. Instead of simply testing if “strain correlates with delinquency,” building a computational model requires specifying precisely how, for example, different types of strain interact with coping resources over time to produce specific behavioral outcomes, thus generating genuinely risky and falsifiable predictions at the unit level.
In other words, we’re just as open to Wheeler and like-minded scholars “building” more effective policing solutions as we are to critical scholars “building” critiques of those solutions or alternative approaches themselves. To us, the key is maintaining scientific rigor regardless of the practical direction. Interestingly, throughout our recent papers, we have pointed to exemplars (or “strong links”) where some of these precision principles have been realized in the criminological literature. Wheeler’s own academic work is among these examples.4 But so too are esoteric measurement papers that have little apparent practical utility at this point. To the extent that Wheeler and his colleagues or other criminologists were motivated to do this rigorous work through their desire to “build things” and “make the world a better place,” we are all for it. Yet, we are also for rigorous research from scholars guided solely by their curiosity.5. Ultimately, only posterity can provide us with an answer to which of these (or other, if any) approaches will improve our understanding of the social world and/or “make the world a better place.”
Conclusion: Building a Progressive Criminological Science
Wheeler’s call for criminologists to “build stuff” reflects genuine frustration with a field that often feels disconnected from real-world impact. We share that frustration, but we believe the solution requires more than simply shifting from theory to applications. As we’ve argued, scientific progress has historically emerged through rigorous work conducted by variably motivated scholars adopting diverse approaches to scientific inquiry. Rather than privileging any single methodology, we think criminology might thrive from principled methodological pluralism, where we embrace multiple research approaches while maintaining rigorous standards for what constitutes genuine scientific progress.
With that said, we also think a “precision crisis” in criminological science represents both the core challenge and our best opportunity for improvement. By recognizing how our conception of scientific knowledge has been constrained by historically contingent statistical practices, we can identify concrete areas for reform. A promising path forward might entail generating high-resolution data; developing formal computational models of theories; prioritizing precise description of concrete phenomena; and subjecting theories to genuinely risky tests. It might also require moving beyond standardized effect sizes and significance testing; approaching measurement with more critical scrutiny; and attending to theoretically essential anomalies that are often obscured or dismissed as “error” by standard measurement and analytic approaches.
While we do not suggest that criminology can or should become physics, we maintain that the field can achieve considerably greater precision and cumulativity than current practices yield. The field’s future depends not on choosing between theory and practice, but on developing more sophisticated ways of connecting them in service of scientific understanding. As we argue, a more precise criminological science is not merely an academic ideal; it is a prerequisite for developing genuinely evidence-based policies and interventions that can effectively address crime and its complex causes – that is, for truly realizing Wheeler’s goal of “building things” that work.
Footnotes
After graduating from the same university as Jane Addams, Jon entered graduate school with aspirations to study race and ethnic inequalities and ultimately teach others about them in a community college setting. Jake’s undergraduate training in criminology was primarily from Michelle Inderbitzen, one of the major proponents of public criminology.↩︎
Of course, there is a dark side to “pure” science as well. The more we know about something, the more we can do with it - that includes evil and amazing stuff. While the atomic bomb is a popular example here, another is Haber’s catalyst process that both helped feed the world and led to development of chemical warfare).↩︎
See Adam Mastroianni’s blog post “Science is a Strong Link Problem” for an argument for why the mass of publications might not be as big a problem for scientific advancement as some of us may think.↩︎
In addition to his main argument about criminologists pursuing building things, Wheeler has also argued for criminologists to become better trained in the basic principles of software engineering. This echoes Richard McElreath’s insight that quantitative social science inherently involves “building an analytical pipeline” – often without proper training from professional software developers (See McElreath’s lecture “Science as Amateur Software Development”). This may be where we most agree with Wheeler’s practical focus, and also where we see ourselves falling short in our own work.↩︎
Abraham Flexner’s classic essay – “The Usefulness of Useless Knowledge” perhaps best exemplifies this approach.↩︎
Reuse
Citation
@online{brauer2025,
author = {Brauer, Jon and Day, Jake},
title = {Should {More} {Criminologists} “{Build} {Stuff?}”},
date = {2025-06-14},
url = {https://reluctantcriminologists.com/blog-posts/[15]/build-science.html},
langid = {en}
}