JOM Forum: Theory Testing Is Theory Generation

Abstract

In this paper, we propose that theory-testing research offers just as much potential for generating theory as theory-building and theory-elaborating research, the two variants typically associated with theory generation (Ketokivi and Choi 2014; Lee et al. 1999). Responding to Bendoly and Oliva's (2025) call for searching meaningful theoretical pathways for research contributions, we suggest that theory-testing research has always constituted a meaningful pathway to theoretical contributions when it extends beyond merely applying theory to challenging, expanding, and elaborating it. These extensions can lead to significant adjustments in bodies of knowledge over time as research programs progress.

To understand the generative aspect of theory testing, we must distinguish it from theory application. When we apply theory, the objective is usually to address a practical problem, without the interest of contributing to an ongoing theoretical conversation. In empirical operations management (OM) research, the application of factory physics offers an illustrative example: Researchers apply concepts such as Little's Law and laws of variability to improve factory productivity (Schmenner and Swink 1998). In this context, theory consists of the relevant applicable laws that are treated as given, which makes theory effectively axiomatic from an epistemological point of view (Popper 1935/2005, 51). ¹

In stark contrast to theory application, the fundamental idea in theory-testing research is to place the theory itself under empirical scrutiny. Accordingly, theory is no longer treated as self-evident and certain but propositional and conjectural, subject to revisions (Lakatos 1970; Popper 1963).

As an example of theory-testing research, consider Williamson's (1971) question “Why do firms integrate vertically?” This question gave birth to transaction cost economics (TCE), one of the most influential and established research programs on organizational boundaries (Santos and Eisenhardt 2005). The theoretical essence of TCE is succinctly captured by the discriminating alignment hypothesis: “Transactions, which differ in their attributes, are aligned with governance structures, which differ in their costs and competencies, in a discriminating (mainly transaction cost economizing) way” (Williamson 1996, 46–47). Importantly, this statement is not meant as axiomatic but conjectural, as the word ‘hypothesis’ implies: Whether actual governance decisions align transactions and governance structures in a “mainly transaction cost economizing way” is to be settled empirically.

Consider Walker and Weber's (1984) seminal TCE-based study that examined the make-or-buy decision in the final assembly of automobiles. TCE-as-conjecture becomes salient in the discussion section where several TCE's central propositions are called into question based on the empirical analysis. For example, the finding that “the effect of transaction costs on make-or-buy decisions was substantially overshadowed by comparative production costs” (Walker and Weber 1984, 387) is inconsistent with TCE's original central proposition that transactions will be aligned with governance structures in “mainly transaction cost economizing” (Williamson 1996, 47, emphasis added) way. When the qualifier “mainly” is interpreted as conjectural and malleable, empirical research not only tests but also informs theory. Walker and Weber's (1984) findings suggest that while transaction costs are relevant, they constitute only a portion of total costs, which are decisive in make-or-buy decisions. Such findings, and many others, have expanded TCE's focus over time from transaction costs to total costs. Another more recent development is that instead of focusing on costs, researchers have incorporated the revenue side into the comparative analysis as well (Ketokivi and Mahoney 2020). More generally, reviews of empirical TCE literature (e.g., Macher and Richman 2008) demonstrate how TCE as a theory has developed significantly over time, mainly through the broadening of its scope.

TCE illustrates a general and essential characteristic of theory-testing research: When theory is taken as conjectural, testing theory also generates theory through marginal adjustments. Such adjustments link individual theory-testing research efforts to a broader theoretical conversation and, consequently, enable the accumulation of theoretical knowledge and theory progress. We do not witness similar accumulation in knowledge communities where theories are merely applied. ²

Theory-testing research is often described as hypothetico-deductive (Mantere and Ketokivi 2013). We submit that the label “deductive” is accurate for theory application but inaccurate for theory testing; for the latter, the descriptively accurate term is hypothetico-abductive. In this section, we seek to establish this by comparing reasoning in theory testing versus theory application.

To understand the role of abduction, we need to distinguish between two central reasoning tasks in theory-testing research: connecting theoretical and observational statements (the theorist's concern) and connecting observational statements with data (the statistician's concern) (Meehl 1990, 116). The statistician's concern is comparatively straightforward, and there is no difference between theory application and theory testing: The statistician's concern is addressed using the established tools of statistical inference, that is, a combination of deductive and inductive reasoning. Differences are found in how the researcher addresses the theorist's concern (Figure 1).

In theory application, the theorist's concern is methodologically comparatively simpler. When theory is merely applied, there is no feedback arrow from observational predictions to theory. Furthermore, if theory consists of empirically salient concepts, observational predictions can be deduced from the theoretical foundation (Schmenner and Swink 1998)—hence the term hypothetico-deductive.

The case of theory testing is comparatively more complex, as adjustments to theoretical conjectures do not follow a deductive, computational logic (Mantere and Ketokivi 2013). Rather, adjustments are iterative steps of abductive inferences which adjust conjectures based on often surprising findings (Peirce 1877). As an example, let us revisit TCE's discriminating alignment hypothesis. Its central terms (e.g., transaction, governance structure, competence) are theoretical and must be translated from the language of theory into the language of empirical observation. Given that translation involves several possible, non-obvious interpretations (Quine 1951), the reasoning process cannot possibly be deductive. Similarly, since translation does not involve generalization of any kind, it cannot be inductive either. The only remaining form of reasoning is abduction, which is indeed the reasoning tool by which theory-testing researchers bridge the theoretical to the empirical.

The abductive translation process is generative because it creates new meaning for theoretical concepts (Gadamer 1975). In their make-or-buy study, Walker and Weber (1984) translated TCE's general concept of uncertainty into volume uncertainty and further into unpredictable fluctuations in demand for components in automobile final assembly. This translation created specific and contextualized—in a word, new—meaning for the concept of uncertainty.

The other complicating factor has to do with the feedback arrow to theory (Figure 1). Specifically, testing hypotheses is ultimately a means to the end of testing theoretical conjectures. Empirical evidence that is consistent with the hypothesis constitutes an instance of positive corroboration, whereas inconsistency means negative corroboration (Popper 1935/2005, 264–266). Both kinds not only inform theory but may also lead to adjustments and elaborations.

The feedback arrow to theory makes the reasoning process in theory-testing significantly more complex than in theory-application research because it involves the use of modus tollens. ³ The use of modus tollens becomes particularly complex in the case of negative corroboration: What conclusions do we draw about theory if the evidence is inconsistent with a theoretical prediction?

In his seminal contribution to the literature on theory testing, Lakatos (1970, 133) maintained that in the case of negative corroboration, we are not permitted to direct the modus tollens to the “hard core” of the theory but to its “protective belt” (i.e., measurement issues, data quality, contextual issues, and other problems or oversights that might have given rise to the failed prediction). This is particularly relevant when the theory under scrutiny has amassed a high degree of positive corroboration from past research, or, as Meehl (1990, 108) put it, has “money in the bank.” To suggest that all this money would be forfeited based on just one instance of negative corroboration is both unreasonable and methodologically dubious: There are no defensible methodological principles that permit us to immediately direct the modus tollens to the hard core of the theory.

Reasoning about corroboration is an abductive process. The specific form of abduction used in back-translating the empirical to the theoretical differs from the abduction used in translating the theoretical to the empirical; consistent with Bendoly and Oliva's (2025, 7) terminology, we label these “abduction a posteriori” and “abduction a priori,” respectively. ⁴ Understanding how theory testing is theory generation hinges specifically on understanding these two variants of abduction. The connection from abduction to theory generation stems from the fact that abduction is the only form of reasoning that allows the introduction of new ideas in the conclusion of a reasoning process (Locke et al. 2008).

Bendoly and Oliva's (2025, 7) observation that abduction is a form of sensemaking offers a useful starting point for establishing that theory testing generates theory. Because both the practices and the objectives of our sensemaking are diverse (Weick 1995), so are the forms of abduction: some forms are selective, others creative; some are theoretical, others empirical; some are explanatory, others non-explanatory; some incorporate only observables while others include unobservables; and so on. Given that there are literally dozens of variants of abduction (Hoffmann 2011; Minnameier 2017; Schurz 2008), one must be explicit about the specific form used. In the following, we discuss the use of abduction in the two stages of theory-testing research.

Theory application and theory testing both play an indispensable role in empirical research. In this paper, we have sought to establish that the latter has always had generative potential to shape our theoretical thinking. To realize this potential, we must strengthen our abductive reasoning practices both in the a priori and a posteriori stages of research. Stated in reasoning terms, this involves theoretical-model abductions that extend theories to new empirical contexts on the one hand, and strong inference-to-the-best-explanation (IBE) abductions to modify theory based on negative corroboration on the other. This elaborates the process by which abductive sensemaking enables the creation of theoretical arguments (cf. Bendoly and Oliva 2025, 7), thus offering an important pathway to theory.

Herman Aguinis ([email protected]), The George Washington University, Washington, DC, USA.

As noted in the original discussion above, theory testing is generative because it necessarily involves abduction. Researchers must translate abstract theoretical ideas into concrete, context-specific predictions, a step that is never automatic and often reshapes what those ideas actually mean. They then have to work back from the evidence to theory, asking which explanation best accounts for what they have observed. Apparent support should be handled carefully, because the same evidence can often be explained in more than one way, and apparent failures rarely justify abandoning a theory's core once it has accumulated substantial support. More often, such failures point to problems with assumptions, measures, or scope. Over time, these kinds of adjustments build across related studies, extending what a theory can explain and sharpening its logic. Seen this way, progress in OM theory comes less from inventing new theories and more from systematically improving existing ones through disciplined theory testing (e.g., Aguinis and Cronin 2026). This is a reality that matters for the vitality of the field and, frankly, for scholars working in a publication system that demands a clear theoretical contribution as a requirement for career success.

But, a question I am asked frequently, especially by junior researchers, is: “These general principles about how to make contributions to theory make sense, but… how do I put them into practice, specifically? What actionable recommendations can you give me to implement these principles in my own research?”

To answer this question, decades of methodological research allow me to offer a concise 8-step theory contributions playbook (for details, see Aguinis 2025, 2026; Aguinis and Cronin 2026). Importantly, I demonstrate the practical feasibility and effectiveness of this 8-step playbook. I do this by continuing with the illustrative case of TCE theory as discussed earlier. Specifically, I describe how Crook et al. (2013), which received the Academy of Management Perspectives best article of the year award, made meaningful theory contributions by implementing each of the playbook's steps (albeit some of them implicitly).

Richard Makadok ([email protected]), The Ohio State University, Columbus, Ohio, USA.

When I was 7 years old, my father explained science by opening his old college physics textbook from the atomic age of the 1950s, when folks revered Science with a capital “S.” In the introductory chapter, he showed me a closed-cycle flow chart labeled “The Scientific Method” with four stages: (1) propose a theory, (2) design a study to test the theory, (3) execute the study to collect data, and (4) interpret the study's results to either confirm, modify, or reject the theory, leading back to the first step to repeat the cycle anew. Simple language that a seven-year-old could understand, without fancy terms like deduction, induction, or abduction.

In their forum essay, Ketokivi and Mantere focus mainly on the second and fourth stages in that old scientific method cycle—that is, designing a study to test a theory, which they label as “abduction a priori,” and interpreting the study's results to judge the theory, which they label as “abduction a posteriori.” I doubt their fancy new labels are needed when existing terms like “design” and “interpretation” are readily available, but their instinct to problematize (another fancy term) these two stages seems promising, since both designing studies and interpretating their results are more subtle and less straightforward than they seem at first glance. By admitting these problems, Ketokivi and Mantere take a helpful first step toward finding realistic solutions.

But then what are the next steps? First, even if the eventual goal is normative analysis—that is, articulating how studies should be designed and how their results should be interpreted—it may still be useful to begin with some positive analysis by investigating what choices and tradeoffs, and even errors, real-world researchers make in their daily work of designing studies and interpreting their results. After all, it is usually helpful to clarify a problem before attempting to solve it. Such investigation may reveal hidden pitfalls—that is, dimensions of the design and interpretation problems we do not yet fully recognize—as well as identifying which aspects of current practice are working well or poorly. This investigation could begin by scrutinizing publications for possible disconnects between theory and study design, as the forum essay does with Walker and Weber (1984), and for possible disconnects between results and theoretical interpretations of those results. However, extracting practical implications from such disconnects may require interviewing researchers themselves, to understand the rationale behind their choices, and tradeoffs underlying those choices.

The next step of deriving normative implications demands deeper analysis of tradeoffs. Thomas Sowell (1987) quipped, “There are no solutions, only tradeoffs.” In a world of scarce resources and limited observability, there is no perfect study design, for at least three reasons: First, financial or material tradeoffs occur wherever barriers to observation can only be reduced by deploying more resources (e.g., CERN's Large Hadron Collider), in which case the study's design may be constrained by interests, concerns, and wishes of whatever entities bankroll it. Second, under legal, regulatory, or ethical barriers to observation, institutional review boards may manage tradeoffs, or study design may be constrained by confidentiality requirements (e.g., census, taxation, education, or health records), or perhaps by piggybacking on whatever public data authorities, practitioners, or intermediaries happen to collect for their own purposes. Third, the barriers and tradeoffs are sometimes inherent in the theory itself, due to imprecisely defined conceptual constructs like the forum essay's example of “mainly transaction cost economizing.” Indeed, even physicists still struggle to define fundamental concepts like time and space.

Thus, the realities of scarce resources and limited observability demand some humility about what is possible in study design, and some caution from readers, reviewers, and editors in second-guessing researchers' choices under tradeoffs. One may object to imperfections in the methods Walker and Weber (1984) chose when operationalizing and contextualizing TCE theory for a specific company in a specific industry, but perfection is an inappropriate standard. Inferiority is a more appropriate concern than imperfection. Sowell's quip about tradeoffs trumping solutions dovetails with his favorite question for utopian-minded critics, “Compared to what alternative?” Was imperfect TCE operationalization inferior compared to not measuring the concept at all? Was it inferior to realistic alternatives available at the time of the study, given available access to information and resources? Thus, it is unrealistic to hope that study design is a problem that will ever be “solved” in some absolute sense. Perhaps the best we can hope for is a practical “engineering science” of study design that focuses more on identifying situational pitfalls and helpful special-purpose tools than seeking a universal code of best practices.

The same is also true of interpreting results, where tradeoffs also abound. Here the modus tollens example in the forum essay's footnote 3 suggests an “engineering science” in which the success or failure of empirical prediction B can be interpreted via Bayesian updating of priors for the set of conditions A = {A ₁ , A ₂ , A ₃ , A ₄ , …A _n }, where A ₁ is the validity of the theory itself, A ₂ is the validity of the measurements, A ₃ is the validity of the theory's background assumptions, A ₄ is the validity of the empirical identification strategy, and the remaining A _i are the rest of the protective belt. Of course, this approach would require not only methods to determine priors for the elements of A, but also knowledge (or at least defensible assumptions) about the correlations, interactions, or other dependencies among those elements, so that credit for B's success or blame for its failure gets allocated plausibly.

This approach is more complicated than current practice ⁶ but is further complicated by two problems—the calibration problem of “known unknowns” due to limited observability, and the ignorance problem of “unknown unknowns” due to limited awareness. First, at least some of the known protective belt elements {A ₂ , A ₃ , A ₄ , …A _n } may themselves require calibration studies to determine their priors and/or their correlations or dependencies with each other, in which case many of the tradeoffs from study design—for example, financial, material, legal, regulatory, ethical—apply here too. ⁷ Second, due to inherent tradeoffs between simplicity, generality, and accuracy (Weick 1979), researchers may be ignorant of some protective belt elements {$A_{n+1},A_{n+2},\dots A_{n+m}$}, especially unrecognized background assumptions or boundary conditions, like unawareness of relativity in Newtonian physics. Since discovery of these is often serendipitous, part of interpreting results may always remain more of an art than an engineering science. As my father says, discoveries are either impossible or obvious—impossible until they are made, and then they are obvious.

Morgan Swink ([email protected]), Texas Christian University, Fort Worth, Texas, USA.

Many OM researchers present their work as “theory testing,” either explicitly or by virtue of the paper's structure (i.e., hypotheses before research method). Yet much of what is labeled theory testing research in OM (and likely in other fields) is not really testing at all—it is framing. In my experience (admittedly anecdotal), researchers often bring to a study expectations and even candidate explanations for observed relationships well before any theory is systematically interrogated. Most OM research originates in observations of practice—or in literature describing practice—and is thus motivated primarily by phenomena rather than theory.

Researchers then consult existing theories to identify suitable conceptual frames: to articulate research questions, develop arguments, communicate expectations, and interpret results. This approach represents a different form of “theory application” than that described by Ketokivi and Mantere. They characterize theory application as using a theory's laws to solve an operational problem; in practice, researchers often “apply theory” to solve a different problem—namely, satisfying reviewers' expectations for theoretical grounding.

Rarely do OM researchers begin with a theory and an explicit motivation to confirm, disconfirm, extend, or constrain its core tenets. In practical terms, OM is a phenomenon-driven field, and many would argue that this orientation is appropriate. After all, the “science” of OM traces its roots to early empiricists such as Taylor and the Gilbreths, and the field has advanced most dramatically through industry-driven innovations such as Fordism (mass production), the Toyota Production System, Agile Manufacturing, and related paradigms. Rather than developing indigenous theories, OM researchers have largely borrowed theories from other disciplines (e.g., organizational theory, sociology, economics).

While some view this reliance on external theories as a weakness, it is arguably a reasonable outcome of historical timing. Many of the theories we have adopted predate OM as a distinct discipline—and certainly predate supply chain management. Until the 1980s, “OM” in most business and engineering schools was narrowly defined as production management, industrial engineering, or management science. Research in these areas was dominated by mathematically tractable theories (e.g., inventory theory, queuing theory) amenable to formal proof. Only in the past 30–40 years has OM—and more recently SCM—expanded into sociological and empirical research domains, where proof is inherently elusive.

My conjecture is that increasing global integration and competition, driven by geopolitical and technological change, encouraged OM researchers to pursue broader, observation-based questions about operational practice. In doing so, the field has returned—perhaps inadvertently—to the empiricist roots of its earliest scholars. At the same time, in an effort to maintain scientific legitimacy, we have collectively emphasized theory development as a central research objective.

More than over-dependence on theories borrowed from other fields, what constrains theoretical progress in OM is the lack of competing theories. Our dominant approach—practical research framed through imported theories—has produced a long list of theories, each explaining phenomena within a particular domain, but rarely standing in direct opposition to another. There have been notable exceptions. The 1990s debate over “trade-offs” versus “synergies” in operational improvement provides one example. The rise of behavioral operations in the early 2000s offered another, challenging assumptions of full rationality (though partially reconciled through bounded rationality). Still, most theories in OM persist with little sustained challenge—they rarely die. Without meaningful theoretical competition, the kind of theory “generation” described by Ketokivi and Mantere—largely extension and elaboration—is likely the upper bound of what our field can achieve under current conditions.

Can we reasonably expect OM researchers to generate fundamentally new theories? Given the incentives embedded in our publication review process, probably not. Theory-testing studies (including extensions and elaborations) are generally easier to publish than theory-building efforts. The broadening of established theories—such as transaction cost economics, the resource-based view, or the theory of swift even flow—is undeniably valuable. Such expansions have enriched these theories by incorporating new constructs, domains, and behavioral considerations. However, it may be too much to expect theory testing to yield new theory generation. Importantly, negative corroboration is often the most powerful catalyst for theory development. When methodological flaws can be ruled out, surprising or non-supportive findings stimulate the kind of a posteriori abductive theorizing emphasized by Ketokivi and Mantere.

Yet, as Ketokivi and Mantere also point out, theory development also requires a priori abduction. Two approaches may be particularly promising. First, researchers could be encouraged—especially during hypothesis development—to abductively generate plausible competing explanations and competing hypotheses, rather than relying solely on the logic of a chosen theory (or theories). This would yield stronger and more informative hypotheses, in the sense that empirical results could adjudicate among rival explanations rather than merely support or fail to support a narrow theoretical argument.

A second approach is to postpone hypothesizing altogether. This would require editors in our field to acknowledge that rigorous description can make a legitimate contribution as a precursor to theory development. Editors and reviewers would need to allow greater space for informed speculation—typically discouraged in our field—about interesting, anomalous, or counter-intuitive phenomena uncovered through careful data analysis prior to formal hypothesis formulation. This logic underpins the JOM special issue on “nascent theory,” ⁸ which seeks to create space for research motivated by observation rather than by allegiance to an established theoretical framework.

Efforts such as these may encourage the development of genuinely new theories in OM. At the same time, the OM field should remain committed to our empirical heritage and continue to leverage the strengths of both “practice-oriented” and “practical” research traditions. Doing so will help us avoid the risk of “too much theory, not enough understanding” (Schmenner et al. 2009).

Elliot Bendoly ([email protected]), The Ohio State University, Columbus, Ohio, USA.

Rogelio Oliva ([email protected]), Texas A&M University, College Station, Texas, USA.

Ketokivi and Mantere make a compelling case that research designed with the primary intention of testing theory has always carried generative potential. We agree. Their central argument—that abductive reasoning in both the a priori and a posteriori stages of theory testing enables the creation of new theoretical meaning—is fully consistent with our view that theories are never finished products but exist along a continuum of sensemaking, from vague hunches to detailed accounts of causal mechanisms. In our earlier terms (Bendoly and Oliva 2025), their proposal speaks primarily to research that begins on what we labeled Path A—studies motivated by existing theoretical conjectures and designed to test them—rather than to Path B work that originates in anomalous or intriguing empirical observations. Our commentary therefore concentrates on how their analysis enriches and reshapes our understanding of Path A, while leaving open important questions about the role of Path B in theory development. We are particularly gratified to see how their elaboration of abduction a priori and a posteriori develops the connection between abductive sensemaking and the creation of theoretical arguments that we identified as a meaningful pathway for research contributions. Their analysis of how Walker and Weber (1984) translated TCE's abstract concept of uncertainty into context-specific meaning illustrates precisely the kind of generative reasoning we had in mind.

That said, we see opportunities to sharpen, deepen, and extend the argument in ways that matter for OM specifically.