The Pursuit of Innovative Theory in the Digital Age

Abstract

Grover & Lyytinen (2015) urged to reassess the Information System (IS) field’s exclusive dependence on reference theories and to engage more in blue-ocean theorizing. From its inception, such need has been latent in the field, because it deals with novel, fast changing, complex, and systemic phenomena that is hard to account with received theory. We note in this essay that the need for innovative theorizing is heightened given the unprecedented, pervasive digitalization of contemporary society, accelerated by ongoing COVID-19 pandemic. In this essay, we scrutinize further the idea of blue-ocean theorizing and review the characteristics, impediments, and merits of developing innovative theory. We define endeavors toward such theory as collectively endorsed cognitive processes which increase variance and novelty of theoretical accounts of IS phenomena. These push to deviate from the field’s established theoretical (canonical) core by relaxing six assumptions that guide dominant, legitimate forms of the field’s theorizing. We identify and review institutional barriers that curb the development of innovative theory. In conclusion, we offer guidelines for how the field and its stakeholders can productively engage in developing and evaluating innovative theory.

Keywords

theory blue-ocean novelty variance digital phenomena complexity epistemic scripts institutional barriers publishing

Academics lack perspective. In a debate on whether the world is round, they would argue, 'No,’ because it’s an oblate spheroid. They suffer from ‘the curse of knowledge’: the inability to imagine what it's like not to know something that they know. Steven Pinker.¹

Introduction

In our 2015 article in the MIS Quarterly, we argued that Information System (IS) research has become formulaic and needs fresher approaches that rely less on the encumbrances of reference disciplines (Grover & Lyytinen 2015). 6 years later, as keen observers of the tidal wave of “digital transformation” debate we feel even stronger about this position. The reliance on domesticating external theories has been valuable for the field to understand a myriad of effects of the design, adoption, and use of information systems across multiple settings and contexts. While this has increased the field’s legitimacy, created platforms for cumulative research, and improved our citation numbers and impact factors, we feel that we are at a point of diminishing returns on all these fronts. To tackle as a community, the relentless onslaught of buzzling digital phenomena, we need to expand our epistemic stance and scripts on how we approach theorizing. Our position in the original piece was straightforward: we need to reduce our dominant reliance on reference theory and engage directly with emerging and complex phenomena (descriptive/prescience research) by constructing novel and bold abstractions (models) to understand these puzzling observations (blue-ocean theorizing).

For most of the time in our field, the puzzling observations have centered on singular pieces of information technology (IT) and their effective, local deployment (adoption, use, impact, implementation) within an organization(s) across levels (individual, team, unit, organization). Our abstractions were informed dominantly by theories borrowed from neighboring disciplines, many of which were well suited to frame questions around effects of incremental IT deployments within each level. However, despite the intellectual merit of leveraging these frames, we posit that they are frequently unreflectively adapted, and fail to advance our understanding of emergent IS phenomena. Often, these approaches do little more than enhance the external validity of borrowed theory and, even more ominously, force the field to exogenously introduce weak IS constructs adapted from borrowed theories rather than engaging in nuanced ways with bustling IS phenomena. In consequence, they constrain rather than advance “good” IS knowledge. A platitude of incoherent platforms of mid-level models has resulted on which the field subsequently has dissipated its effort and energy with decreasing returns.

Several prominent voices in the IS field have, over time, raised concerns about modes of theorizing in the field and its worrisome state (Lyytinen and King 2004). Sometimes, these are couched around the urge to solidify a “core” in the field. Sometimes they are offered as critical reviews of the benefit of “reference theories.” Sometimes they complain of the lack of clear field “identity” or address the eternal tension between the “rigor” and “relevance” (see Appendix A for a summary of past arguments). A minority view has argued that the field has made sufficient contributions and its theories are just fine (Straub 2012) or state that the overemphasis on theory in general has been detrimental to the field’s progress (Avison and Malaurent 2014).

Overall, the community appears to strongly share a view that its current modus operandi in theory building is unsatisfactory. The field needs “better” theorizing to prosper, but there is little or no consensus on ways for achieving this. At the same time, the urgency for change is increasing with birth of new breeds of digital phenomena couched in faddish terms such as platforms, IoT, machine learning, and so on. These phenomena differ from “boxes” of discrete technologies being deployed within well circumscribed organizational context. They come with puzzling observations and demand abstractions that cannot easily be retrofitted with reference theories. Further, digitization is generating an endemic push to increase the fidelity of theories that now must deal with exceedingly complex human enterprise buttressed with novel ways of using digital technologies. A case in point is recent debates around socio-material imbrications, and affordances and constraints.

Given the recent tidal wave of digital phenomena, scholars across management fields have started to question, debate, and defend the validity of their field’s received theorizing (e.g., Benner and Tushman (2015) in strategy; Puranam et al. (2014) in organization theory; Nambisan (2017) in entrepreneurship; Grover and Lyytinen (2015) in Information Systems).² The need for self-reflection is truly compelling for the IS field due to its socio-technical origins. The field needs to formulate alternative “embedded” constructs for describing, accounting, or explaining digital technology enabled or infested individual, organizational, managerial, industry level, or societal phenomena. This calls for finer-grained, innovative theorizing and increases in the conceptual and methodological variance in the field’s intellectual edifice. We frame next this essay as a debate and argue for the following: given the nature and currency of digital phenomena, the IS field stands to benefit from innovative theory. Recent digital phenomena due to their non-traditional character call for new theorizing unbounded by conventional, received reference theory framing and related logics. Our target audience are stakeholders of the IS field as represented by its gatekeepers and scholars. Our working definition of innovative IS theory is that it is novel and idiosyncratic to IS phenomena, which by its constructs and their conceptual relationships increases variance on how we observe and account for focal IS phenomena. We see both novelty and indigeneity to digital IS phenomena as necessary conditions for innovative IS theory. The novelty implies deviation from existing theoretical frames. This can originate from many sources, but necessarily entails the presence of a creative mind in observing and abstracting from the phenomenon as something different. The indigeneity implies that the theory is specific to understanding IS phenomena and warrants the field’s ownership of the intellectual merit. These both emphasize the importance of creativity and circumscribing to theories that strive for greater fidelity to account IT phenomena.

We will advance our thesis in four steps. First, we frame our argument and its boundary conditions. Second, we synthesize distinguishing features of the digital phenomena and illustrate how these phenomena are changing the “rules of the game” and raise the need for a new theorizing. Third, we discuss how current research practices, and their epistemic scripts guide theory formulation and legitimation and impede development of innovative theory. For each barrier, we conclude with suggestions to offset these barriers and develop mechanisms to facilitate more innovative theorization for the digital age. Finally, we discuss criteria for evaluating innovative theory.

Context and boundary conditions

The contemporary setting of using digital technologies frames our argument. On the research side, we see a growing popularity of data driven research. This stream called “big data” operates with large data sets obtained through digital means and leverages sophisticated, computational techniques (genetic algorithms, machine learning) to detect “interesting” correlational patterns to make predictions. Not surprisingly, “big data” results growingly populate our leading journals as legitimate knowledge contributions, often “sold” using sophisticated computational methods with unprecedented digital data sets (Grover et al. 2020). Some scholars have even gone further and claimed that big data with strong predictions diminishes or obfuscates the need for theory (Hui, et al. 2017; Geva, el al. 2017). We do not subscribe to this view (Grover, et al. 2020). Philosophically the position is untenable as it throws IS research to a status before Kantian analysis of categories (Habermas 2015).^. In contrast, we subscribe to a position where the theory in both form and purpose remains a basic constituent of the field’s disciplinary knowledge. Theory’s importance to our field is arguably greater than in other management fields (see e.g., Collquitt and Zapata-Phelan 2007; Schlegelmilch 2011; Fontinelle 2019) due the need for continuous sense making, given the field’s fast changing phenomena. Therefore, we need to search for new abstractions that contribute to explaining why, and how, and/or explaining and predicting (if ...then) these phenomena.

On the practice side, we now witness the fourth tidal wave of digitization we can call “cloud infrastructure” following mainframes, personal computers, and the internet. The emergence of “deeply digital” environment enabled by such digital infrastructure grants exciting times for the field. Having observed the field for many years, the current party resembles those we experienced in the 80s with microcomputers and in 90s with internet. Our experience also teaches that this will not last. Rather, the staying power of the field will depend more on what we can say when the party is over: the ability of the IS community to create a true difference to its stakeholders will ultimately depend on the utility of knowledge products we produce including theory with the capability to explain things and narrate change. In the current setting, this ability, however, is constrained by our institutional structures, epistemic scripts and cultures that have brought us where we now stand and dictate how we legitimize knowledge in our research practices.

Finally, we observe two boundary conditions of our argument. First, we subscribe here to a straightforward and traditional view of theory. Cleaning up all variants of theory and getting mired in endless arguments what theory is or not and how it relates to truth or utility etc. is not the primal point of this essay (for references see e.g., Sutton and Staw 1995; Gregor 2006 and their reference lists). For us, a theory seeks to identify, describe, explain, and possibly predict IS phenomena (Sutton and Staw 1995). It and can be deductively or inductively derived and needs to be somehow empirically validated. This is arguably the most frequent conception of theory in the IS field (i.e., 66% in Gregor 2006). We do recognize that for many, a broader conceptualization would cover design science, typologies, phenomenologies, or theories that articulate problems and solutions etc (e.g., Gregor 2006). All these forms of theory are salient for informed inquiries around digital phenomena, but they will not be used here to advance our primary thesis. Our account, however, by implication covers theories of analyzing (1) when theory development results in taxonomies and typologies shaping theories of design and action, and (2) new “kernel” theories that underlie design artefacts. Second, consistent with the mission of the field’s leading journals, we posit that the IS field is geared toward providing “theoretical insights that advance our understanding of information systems and information technology in organizations and society.”³ Any assessment of theorizing in the field needs to be founded on its contribution toward generalized knowledge regarding existing or emerging phenomena within this domain.⁴

The reasons for the need for innovative theory in the age of pervasive digital

The existential question for the IS field now is: are we in a phase where contemporary digitization differs from preceding waves of using digital technologies? And if so, how? Similar questions have provided the raison-d’etre for the community’s research mission over the years while the uses of digital technologies have advanced. To be faithful to this mission, and to argue for differences in spaces for theorizing, the field needs to constantly make the case that the phenomena it deals with are at a point of inflexion. The IT deployment in the past has been introduced in the shape of discrete boxes of hardware and software (e.g., Mainframes, ERP, etc.) and associated research problems have been framed in terms of designing, embedding, and deploying such “boxes” in a myriad of social, economic, and institutional contexts. Studies have focused on the differential (or similar) impacts of such deployments across technologies and settings. Consequently, we have witnessed disjoint streams of research on PCs and end user computing, software tools and decision support systems, databases, and data administrations etc.

However, such piecemeal approach has grown problematic in our quest to understand the current wave of digitalization. Ontologically, all digitization operates with bit-strings that embody both material (e.g., software in an Echo speaker) and non-material objects (e.g., data of songs) configured to create value (Faulkner and Runde 2019; Piccoli et al. 2020). This also makes all digital technologies inherently infrastructural—they are combinatorial, relational, and constantly evolving and converging (Hanseth and Lyytinen 2010; Tilson et al. 2010). Now digital infrastructures constitute the fabric of most organizational processes, tasks, and things and people’s everyday behaviors. Their uses penetrate human life, experience, products, business processes, and civic society. We call such state of digital technology use the age of pervasive digital. Due to the reflexive nature of digital technologies (Yoo et al. 2012; Nambisan et al. 2017) we also now have more data about how these technologies are being used or how these uses can be directed, harvested and deployed (Zuboff 2019). Yet, given the state, can and should the field continue to theorize using a box metaphor and draw on its existing theoretical “core”? Will this approach serve well the field’s need to describe, understand, and explain the pervasive digital environment and its impact? We note five attributes that suggests that the impact in the age of pervasive digital will be different (see Baiyere et al. 2021 for parallel arguments):

1. Digital technologies are general-purpose and provide a growing set of functions and properties (speed, scale) in the transfer, storage, and processing of information. The current change in the scope and scale of digital technology operations is unprecedented in the evolution in scale and flexibility.

2. Manifestations of digital technology functions organized into virtualized hardware and abstracted software service stacks are now infrastructural and afford unparalleled combinatorial design spaces that open unprecedented design options to pursue innovation.

3. Manifestations of digital technology functions foster new connections and patterns both within and across the material and social world and their temporal and socio-technical imbrications at unprecedented scale and scope.

4. Manifestations of digital technology functions offer semiotic and social plasticity across organizational layers creating multi-level, complex, and dynamic socio-technical change and behaviors.

5. Manifestations of digital technology functions come with fresh economic foundations and logic by offering infinitesimal marginal costs with nearly unlimited scalability.

The uniqueness of these attributes makes it difficult to directly apply reference theories to explain and understand such phenomena. They demand openness and originality in theorizing. The demand of originality comes from the fact that we deal now with phenomena which differ from what we know in the past (such as the combinatorial value of digital objects), and the need to deal with known phenomena (such as teams) in new ways, given pervasive digital (Davis 1971). It also calls us to see the significance of phenomena recognized in the past that have remained poorly accounted, such as learning from use or generativity. So, the demands for originality in theories attribute known phenomena with new types of relationships, not reckoned with in the past, or theorize with a higher fidelity to new, unrecognized phenomena.

Instead of depending solely on social relationships, digital pervasive phenomena intertwine the social and material in unprecedented ways. Now technology constitutes an inherent part of organizational phenomena and the social cannot be separated from its digital mediation. Socio-technical is not about social being shaped by technical, or vice versa—rather social is technical (see Cecez-Kecmanovic et al. 2014). Because of this, IS theory’s scope and constructs cannot be reduced to accounts of pure organizational phenomena with clean social relations build on top of material world. De Vaujanay et al. (2018) show, for example, that the classic idea of social regulation does not hold when regulation is exercised through digital artifacts. Similarly, “hybrids” of human and machine learning call for theories that go beyond classic theories of organizational learning (Levitt and March 1988; Nickerson et al. 2020). Current pervasive digitalization emerges through combinatorial designs founded characterized by complexity, plasticity, and new economics. They erect novel social formations and behaviors not seen before. Examples abound from product innovation (Lyytinen et al. 2016; Nambisan et al. 2017; innovation communities (Nambisan et al. 2017), high frequency trading networks (Nickerson et al. 2020), or large-scale social communities (Malhotra et al. 2021). These, and other digital phenomena, cannot readily be explained by received theories due to their holistic and transformational impact due to their scope, form, and scale (points 1–5 above). Deeper penetration of digital into organizational life, its malleability and programmability, and its exponentially growing speed and analytic power and decreasing cost will question the validity of received theories that assume limited information processing speed and flexibility, scarcity in storage and transmission, and associated hierarchical forms of social exchange. Minimally, they call to revise assumptions and logic parameters of received theories. These features create also challenges in data collection and analysis that rise from the exponential complexity of the phenomena and concomitant endogeneity problems. Received methods are likely to not work to get into the heart of the matter. Innovation models that presume centralized forms of governance must yield to decentralized governance as well as come grips with generativity and the presence of “unexpected” innovations as people connect in chaotic manner (Lyytinen et al. 2016; Nambisan et al. 2017). Uses of digital technologies and applications can be combined into rich digital trace data pools, which give rise to create embedded socio-digital constructs instrumental to understand complex digitally mediated phenomena.

So, the primary effects of pervasive digitalization for innovative IS theory are profound. The resulting theory may not be blue-ocean, but it needs to challenge the immutability of received theories by proposing alternative, significantly revised versions, and boundary conditions. In these cases, the typical one-way interaction between the theories and phenomena needs to be framed as two-way interactions (Grover and Lyytinen 2015). Rather than treating the theory as sacrosanct, theories need to be treated malleable that yield to the original traits of the pervasive digital phenomena. For example, concepts of economic exchange and contract are well established in transaction cost economics. But the presence of digital mediated forms of recording, executing, and changing contracts enabled by block chain technologies is likely to require alternative ways of accounting for the governance of economic agents.⁵

We can conclude that as social and material worlds become pervasively digitized and are transformed which shapes, for example, organizing mechanisms and processes and their institutional envelopes, this raises the need for innovative theory attentive to the unique character of pervasive digital which received theories do not account, explain, or predict. We should also ask: why does the IS field struggle to produce such innovative theory, and what we can do to facilitate it?

Seven practices IMPEDING innovative theory development and HOW to OVERCOME them

Like all true scholarly work, innovative theory cannot be constructed ad hoc, but needs to be cultivated in a diligent manner in an environment that recognizes, fosters, and rewards such craft (Rivard 2020). This is achieved only through an epistemic and institutional change in how knowledge claims are put forward, assessed, and deemed in our field. Hence, the indigeneity of the processes necessary to produce innovative theory is as important as the product itself. So, why do we not cultivate practices that can promote innovative theory building in our research? We next analyze the constraining effect on the supply side of reference theories and analysis methods, which are incommensurate with the need for creativity and novel forms of abstraction that form the part and parcel of innovative theory development. It is admittedly easier to advocate and talk about innovative theory than to “walk the talk” and engage in the hard work of doing it. However, such practices can be cultivated if the field is committed to such pursuit (Weick 1989). We next discuss two primary approaches to achieve this. The first addresses on the supply side the institutional constraints of theory development in the form of five institutional barriers. The second part addresses on the demand side two barriers associated with assessing theory during publishing.

Five barriers for innovative theory development

The five barriers below form a part of shared institutionalized epistemic scripts guiding research and justifying beliefs concerning research legitimacy and value (Grover and Lyytinen 2015). While all IS scholars may not sustain all of them, they are widely shared. We have frequently experienced all of them as authors, reviewers, and editors. We categorize these barriers into three areas based on the type of inhibiting effect on (1) theory building; (2) use of reference theories, and (3) theoretical imagination.

Constraints on theory building

Barrier 1: construct development is subservient to “serious” theory work

Building innovative theory requires that all elements of theorizing—observations, constructs, and logic—are done at the high level of rigor with novelty. If any of the elements, be it constructs or logic are missing or confounded, then theory building turns into a process where the received theories are mined to explain the phenomenon. For any innovative theory building effort, the first challenge is hence that the theory constructs are made distinct, precise, and clear because without such careful and diligent, construct development theory building remains speculative. This calls for strong conceptual development, instrumentation, and operationalization of the “building blocks” which build a foundation for innovative theory development. Therefore, we need to start with innovative constructs that are not exogenous (i.e., from a distal theory) but embedded within the unique digital pervasive phenomena. Unfortunately, the field’s major journals do not invite or encourage construct development involving novel conceptualizations and operationalization.⁶ There is a dearth of constructs, which we call socio-IS integrative constructs and which form building blocks to explain pervasive digital phenomena. Therefore, to develop innovative theory we need to specifically encourage development of embedded socio-IS integrative constructs.

Barrier 2: Descriptive studies are not valued unless informed by reference theory-based framing.

Good theory can only be erected on solid descriptive foundations that get to the depth of the phenomena and do not gaze at arms-length through the lens of the reference theory. This assumes constant rework on descriptive theory (Carlile and Christensen, 2005). Only continued iterations through description, abstraction, synthesis, and puzzle-solving will spirally move above the nuanced look of phenomena and build innovative theories. The bottom of the process calls for representational fidelity to the phenomenon. Yet, the benefit of such rigorous contextual description is widely ignored in our field as shown, for example, in our review of how IT artifact has been treated (Grover and Lyytinen 2015, see Appendix B). The presence of complex technological mediation, if covered at all,⁷ is expressed at mundane lists of technical properties (“boxes”) or features of the systems, or it is highly contextualized in some pockets of qualitative research⁸.

Building good theory of pervasive digital phenomena requires constant, messy, and contradictory observations, which can be next categorized and connected in manifold ways. With the world being a living laboratory for experiments on emergent digital phenomena, only mundane observation work allows detecting novel concepts, relationships and/or deviations in focal behaviors. Good descriptions can be couched in pre-theory abstractions of stylized facts that synthesize the patterns of the description. These show how things change over time, or how things relate to one another at specific times points and so one (Helfat 2007).⁹ Armed with such descriptive facts and inductive conceptualizations, which remain undervalued in IS research, richer, localized theory can be built that then can postulate novel causal linkages or regularities for testing. Anomalies (Kuhn 1996) unaccounted by reference theory are also made visible and salient through systematic observational work. Overall, without systematic, local, descriptive, and inductive theory building the gaps between our experience-based observations and reference theory continue to be filled by speculation, idiosyncratic narratives, and generic constructs offered by reference theory. Therefore, to develop innovative theory we need to encourage and value rigorous descriptive inquiries and field work.

Barrier 3: Belief that big data analytics obfuscates the need for innovative theory

Innovative theories are often derived inductively by mining large data corpus to derive stylized descriptions. But this will, at most, reach the half-way house to innovative theory. The challenging part of theorizing is to lift the stylized patterns to a higher conceptual, generalizable level, which is rarely done. The problem is becoming more acute as “big data” informed work proliferates. The heightened availability of huge data pools of tactical data, combined with innovation in computational methods, affords new types of data analyses. Here, the focal phenomena are often concrete and practical, and they yield narrow operational findings and predictions. Recently published studies of this genre in our top journal, for example, probed whether the length of an online product review produces higher prices in auctions; or whether the use of an app tracking steps and calories leads to better health outcomes. Naturally, these findings matter for specific contexts as better tactical decisions can be made. But they offer little theoretical insight. On most occasions, the studies treat the technology nominally, or as a tool in the data scraping, continuing the field’s tendency to undertheorize the IT artifact.

To build stronger innovative theories, inductive approaches, whether qualitative or quantitative, need to transcend the study context and its narrative and strive to bolder generalization.¹⁰ This urges scholars’ to abstract in ways that reach beyond what can be predicted locally. By using this generalized mode, the IS scholar can leverage computationally intensive techniques by following a process akin to grounded theory where the scholar samples data, generates tentative taxonomies of (local) constructs, and identifies tentative salient relationships to generate an abstracted structural or process models (Berente et al. 2019). Rai (2017) calls this “abstracting to archetypical problems” so that the linkages from the local data toward broader knowledge impact are established. Such abstraction is tough, as the common demand is to incorporate detailed accounts from the data as to make the story “stick” by making the story credible and interesting. Abstraction is ultimately about inclusion by exclusion. It demands prudent skills of pruning: dropping out nuance as to broaden the account toward mid-range concepts and patterns that increase the study’s generalizability (Healy 2017). This is iterative process of thought experiments, data triangulation, and abstraction, which arrives at coherent and fruitful abstractions capturing the essential novelties of the phenomenon. Most doctoral education programs to our knowledge do not engage in educating students for such processes. The ways in which such studies are reported typically hide the complexity and challenges associated with such process. Therefore, to develop innovative theory we need to fight tendency to add more nuance to tell an interesting story and pushing up the abstraction chain (from patterns to theory).

Constraints on reference theory use

Barrier 4: reference theories are treated as immutable mobiles (Keen 1980)

Most published studies in the field’s outlets adopt unconsciously non-Popperian logic: if the study draws upon a reference theory, then the theory’s logic cannot and should not be falsified. Theories are treated mobile across fields and immutable within the field. However, as Grover and Lyytinen (2015) observed the theories build path dependencies, resulting in dispositions that resist novel theorizing. The knowledge in the theories becomes ossified as the community builds on this intellectual investment, resulting in the “lock-in” of constructs, logics, and dominantly linear and recursive configurations of the theory. The received theory dictates the driving questions—while alternative, substantive questions that are sensitive to the novelty of the pervasive digital phenomena remain unattended, even though such phenomena might seriously challenge the theories’ assumptions, boundary conditions, constructs, and logic (Kieran 2017). Applying these theories to the pervasive digital should be guided by a different question: what the new phenomena can do for the theory in contrast to asking what the theory can do with the phenomena/data? This calls for us to treat the theory as malleable so we can relax theory assumptions, change boundary conditions, and reconfigure its logic. If we do not dare pose such questions, we will fail to inject novelty into our theorizing and remain obedient testers, who corroborate received theories. For us, however, increasing external validity achieved by testing a theory in a new context offers far less than building theories that explain the uniqueness in the IS context. Therefore, to develop innovative theory we need to increase investments to falsify rather than corroborate reference theories. Barrier 4 is especially constraining in that it entails a family of 3 specific tendencies and expectations that we have institutionalized. These tendencies refer to the choice of reference theory (tendency A), the models we study (tendency B) and the results we publish (tendency C).

Tendency A: We deploy reference theories with high verisimilitude to focal digital phenomena.

A typical approach to theorizing in the IS field is to “choose a theory with high verisimilitude with the observed phenomenon.” This appears logical and a beneficial way to economize theory building. Not surprisingly, it is also something commonly valued by the field’s journals, editors, and reviewers. This creates a strong coherence between the focal phenomenon and the adopted framing and in addition to an intuitively clear framing provides precise constructs and logic. However, if the initial framing of the problem is highly similar to the frame offered by the theory, this will preclude most innovative elements if theorizing (Fauconnier and Turner 1998). For example, how can we be innovative, if we examine outsourcing governance (market vs. hierarchy) using TCT which assumes exactly the same frame? This leads essentially to testing of the reference theory—already established knowledge—within a new context. In contrast, a search for theories with an alternative framing can push theorizing to unexpected directions and increases the likelihood of choosing a novel way of seeing the phenomenon, that is, creating a context where one sees “X” as “Y” (Davis 1971).

For example, if we apply transaction cost theory (TCT) to explain organizational outcomes due to effects of pervasive digitalization this is likely to happen. One principal claim of TCT is that asset specificity increases transaction costs and promotes hierarchical governance (Williamson, 1994). The typical organizing frame for TCT is that market participants (organizational buyers and sellers) engage in transactions whose properties influence subsequent governance forms. Yet, if we look at, for instance, marriage relationships—TCT would not be the theory that seems to “fit.” However, in revisiting the major claim of TCT above, it can be stated as “the more one party invests in a dyadic relationship, the more control that party wants over the relationship.” This can now be applied analogously to the marriage context to explain marital conflict! It offers an innovative theory for the phenomena. Breaking out and imagining alternative organizing metaphors which frame the phenomena differently or modify the framing of a theory to a new frame has a higher likelihood of producing theory with novelty while still having a higher likelihood of possessing greater fidelity with the emerging phenomenon. Radical theorists search for inspiration and guidance typically from distal models, metaphors, and ideas to avoid the “nearness trap” which imprisons the scholar to explain the focal phenomenon with established frames.¹¹ Given the cross-disciplinary interest in digitalization, working with researchers across a variety of disciplines offers one way to avoid nearness trap and have a productive yield. Therefore, to develop innovative theory we need to choose theories and metaphors that do not closely fit with the current framing of the pervasive digital phenomena.

Tendency B: We build operational models, not theoretical models

Since our journals demand a taste of “solid” empiricism, the inclination of authors after choosing the theory is to adopt its broad theoretical constructs and then rapidly narrow them into testable, mid-range, testable models. Examples of such testable empirics are beliefs about technology, intentions related to technology, or the cost of using technology. Engaging theoretically with these beliefs is rarely done such as how user’s possible conceptualizations of technology shape their use, or how the scale or speed of use affect organizational responses. This explains why the IS field is littered with numerous, incommensurate models tested over time in an ad hoc manner. This observation can be explained eloquently with Oswick et al.’s (2011) analysis of how to use theories across domains. They distinguish between radical traveling theories (such as TCT, Agency, TRA, etc.), domestic innovative theories (what we above called abstract innovative theories within the field), orthodox domestic theories (narrow, mid-range models originating from reference theory tested within each field) and novel traveling theories (“quirky” theories developed in field work that can move to other fields). The current status quo of theory development in our field is to borrow radical traveling theories from other disciplines and then domesticate them into orthodox domestic theories (mid-level models). Such theoretical reasoning pattern is mainly an outcome of institutional expectations related to publication (expressed below in barrier 5): a theoretical model needs to be tested in the same published study. Apart from precious few theoretical studies, most of which are more “review” than “theory,” the vast majority of IS work demands empirical testing of hypotheses derived from theory;—the field has therefore erected a strong bias against domestic innovative theories.

As noted, we need to falsify radical traveling theories. Rather than treating radical traveling theories as sacrosanct and framing focal phenomena to their conceptual straitjackets, we should focus on the potential influence of focal phenomena on subsequent theory building. Yet, such directions are rarely followed, because the propensity is to lower the abstraction to improve the testability in the research study even when it deals with original, distinct phenomena. Consequently, we now test the same theories against each new technology with largely similar results while pushing more interesting results of testing failures to file drawers (Scargle 2000). Any effort to resist this tendency and engage theory with focal phenomena will foster innovative IS theory.

There are a few credible examples of innovative domestic theory in the IS field. For instance, media synchronicity theory (Dennis et al. 2008) synthesizes unique attributes of contemporary digital technologies and uses those attributes to expand and reconfigure media richness theory. The theory offers constructs unique to the digital phenomena and related media uses. Similarly, the “move to the middle” thesis by Clemons, et al. (1993), uses the phenomenon -information technology’s propensity to broker as well as integrate buyers and suppliers—to extend transaction cost economic explanations and predict the limits of supplier influence present in market-based relationships. However, such examples are far too few. The significance of engaging in tentative theorizing before jumping into the canons of testing is apparent by just looking at one important metric—the citation count exceeds 1000 for both articles. Therefore, to develop innovative theory we need to engage in two-way interactions between pervasive digital phenomena and reference theories.

Tendency C: we publish only significant results

Due to the established canons of testing, we have a proclivity to publish only findings of statistical significance. We ignore the important information contained in results that falsify hypotheses deduced from reference theories by the non-significance of the null test. When this is the case, we fail to push boundary conditions of the theory and evaluate why it may no longer work with pervasive digital phenomena (Busse et al. 2017). In such cases, unsupportive tests need should be interpreted as signals of how far the reference theory can “travel” and to what extent we need to treat it as immutable. It is, in fact, in such failed tests where the evidence of the anomalies is established. As IS scholars, we should cherish such findings and use them to challenge established theory and engage more in critical theory evaluation that promotes developing innovative theory. Generally, this is a wicked problem, which Busse et al. (2017) call a dynamic search for theory boundary conditions. Therefore, to develop innovative theory we should draw on anomalies derived from failed (published) tests of reference theories.

Constraints on theoretical imagination

Barrier 5: philosophical foundations remain incommensurate and should not be mixed during theory development

Most IS scholars by training or identity are locked into a singular and inherited philosophical standpoint, which informs the choice of the type and/or level of theory. Yet, mixing qualitative and quantitative research, interpretive and positivist research, variance and process and systems models, design and behavioral science or levels (see e.g. Burton-Jones et al. 2014; Venkatesh et al. 2013; Venkatesh et al., (2016); Ortiz-Guinea and Webster, 2017)—provides necessary and valuable tensions that can spark innovative theory. Addressing such tensions provides a more holistic and nuanced framing of the novel phenomena. To benefit from tensions resulting incommensurate ontological or epistemological positions or levels, scholars can break out from processes that operate like a train, starting from the station of philosophical assumptions and running forward on the rails of reference theory and supporting methods as to arrive at the final station of significant research results. For instance, quantitative research, typically associated with hypothetico-deductive reasoning, can be effective in building theory by fitting alternative quantitative models to data to identify alternative logics that explain how focal constructs relate and what these constellations of relationships theoretically mean. Similarly, a scholar by presenting complementary variance, process and system models around the same phenomenon can build superior explanations with richer theoretical accounts of focal phenomena. Therefore, to develop innovative theory we need to push philosophical tensions and balance polarized and incommensurate insights.

Change theory treatment during reviews

We observe two demand side barriers: 1) the expectations concerning the content and structure of research articles; and 2) how criteria to evaluate theory are applied in publishing.

Barrier 6: theory. Literature and empirics need to Be integrated in research articles

Rarely are innovative theory papers allowed to stand on their own merit in the review process. We shackle IS scholars with a requirement expressed by the most of our top-level journals to “ground” theoretical development with a sweeping literature review, and/or to demonstrate its veracity with a rigorous research design, data collection and analysis.¹⁴ The former, common in “theory and review” papers, eschews theoretical creativity in that it calls to ground whatever theory the scholar pursues with the established reference theory—diluting its impact. The latter demands rigorous testing in the same study (see tendency B), which narrows imagination and scope, and placing high burden on measures, testing, and analysis in lieu of theory development. The burden of both generating and testing a theory is often an insurmountable task for most aspiring theorists.¹⁵ Therefore, to develop innovative theory we should break up the institutionalized research paper genre and loosen the tight link between theory and evidence via grounding in literature or testing through data..

Barrier 7: misplaced parameter values to evaluate innovative theory

We need to ask how can we evaluate something, which is more alien, varied, and heterogeneous during our review processes? In line with this we can roughly categorize approaches to theory assessment using March’s (1991) classification: 1) exploitative theory evaluation, which builds on received theories with the goal to refine and improve validation and prediction thereof, and 2) explorative theory assessment which evaluates to what extent theory increases the field’s conceptual and empirical variance. Innovative IS theory lies somewhere between the two approaches and hence innovative theory development needs to draw on both approaches of theory assessment. Yet, calls for innovative theory will lean more on require adjustment of assessment criteria. But how do we advance rigorous type (2) assessments as these are not commonly discussed in journal’s review criteria other than broad expectations of novelty and theoretical contribution?

To understand how to assess innovative theory let us denote the intellectual merit of the proposed theory as its α-value.¹⁶ This principally conveys the theoretical power of the abstract-takeaway offered and its potential future significance. If we call the quality of (empirical) validation as the article’s β-value, through α and β, we have largely captured the overall contribution of the paper and to what extent it captures both variance in the exploration and exploitation. The α-value is typically best assessed by open-minded senior editors who have demonstrated competencies in theory development. Many editors do little during the review to improve significantly the original α-value other than clarifying the theoretical positioning through focused literature review.¹⁷ The β -value is enhanced through subsequent data collection, analyses, and integration of the literature as a response to reviewers’ sharp-eyed scrutiny.

Commonly, the review processes of today focus primarily on enhancing the β -value while introducing a small change to the mostly inelastic α-value. If the goal is to promote innovative theory, there are two ways to approach α value as a decision parameter that promotes innovative theory: treat α and β values as a) freely substitutable, or b) conditional. If freely substitutable, papers with higher α-values are permitted more leeway on the validation side, while papers with lower α-values will place higher demand on improving β value. This heuristic is followed by most editors with articles with a moderate α value and a higher β values. Indeed, a large bulk of the published work fall here. But articles with higher α value and lower β value are rare. These papers often don’t get recognized in the review process and end up getting rejected—as the onus among most reviewers is placed on the β value and the failure to meet methodological thresholds.

When we treat the two as conditional, papers need to be assessed initially for a higher α-value threshold. Those that meet the standard can be accepted as long as they meet a minimum threshold value for validity (β). This approach encourages strongly explorative theorizing but is rarely done currently. The challenge with conditional thresholds is that it places significant responsibilities on editors to establish and assess the critical threshold for α-value. This requires broad editorial experience, highly flexible mindset, and sensitivity to understand novel digital phenomena and a willingness to take risks in evaluating the paper.

In both cases, either opting for higher α and lower β or treating α as conditional calls for new review criteria to assess α-value (Table 1). Therefore, to develop innovative theory we need to promote acceptance of innovative theory paper by accepting articles that substitute higher α-value for lower β-value or applying conditional α-values. This requires a shift in mindset among editors (and reviewers) recognizing the seven barriers laid out in this article.

Table 1.

Evaluating innovative theory.

1. Does the theory offer a platform for research on unique, identifiable digital phenomena, that is, does it offer promising and stable abstractions with longevity?

2. Does the theory generate credible claims supported by available observation patterns, that is, is there a feasible path to stable and efficient operationalization to build effective, cumulative knowledge claims?

3. Does the theory create a constellation of coherent, inter-related concepts and logics that differ from received theories with a potential to offer fresh insights to understand the focal digital phenomenon?

4. Are the theory’s concepts idiosyncratic to the IS field, that is, do the constructs and logic recognize unique character of pervasive digital phenomena? How is the idiosyncratic character demonstrated?

5. Is the theory abstract enough to engage with the digital phenomenon and yet useful in generalizing claims of focal phenomena to other contexts?

6. Is the theory, if supported, amenable to the promoting effective interventions to manage, mitigate or cope with the pervasive digital phenomena?

7. Does the theory have the potential to change the direction and organization of the discourse in the topic?

Conclusion

We have argued above that developing innovative theory is desirable and necessary given the pervasive digital environment. If we accept this position, the challenge is how can we foster such theorizing. Our thesis above that we need to relax several institutional expectations that undergird dominant theory work and its evaluation. This calls to challenge many institutional, unreflective biases that entrench our theory work. Only this way can we unleash the latent creativity in the field and build innovative abstractions of the unique phenomena that characterize pervasive digitalization. This does not require us to give up current forms of research including extensive borrowing of theory. But we can do it better—with greater fidelity given to our novel phenomena, and less sanctity given to the borrowed theory. Given the pervasiveness and speed of digitalization, accelerated by the pandemic, and its poorly understood impact—it is critical to foster flexibility in our theorizing. We believe that this will facilitate our ownership of the intellectual regime where digital technologies and human enterprise interact; other fields will have ample reasons to look to us for deeper insights at this critical junction.

Footnotes

Declaration of conflicting interests

The author(s) declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author(s) received no financial support for the research, authorship, and/or publication of this article.

ORCID iD

Varun Grover

Notes

Author biographies

Varun Grover is the George & Boyce Billingsley Endowed Chair and Distinguished Professor of IS at the Walton College of Business, University of Arkansas. He has published over 300 refereed journal articles in IS. He has consistently been ranked among the top five researchers globally, based on his publications in top journals, citations (49,000) and h-index (of 99). Recently, Thompson Reuters recognized him as one of 100 Highly Cited Scholars globally in all Business disciplines and a Stanford University study ranked him 6th (out of 17,971 authors) in the IS discipline. He is Senior Editor for MISQ Executive, Editor of the Journal of the AIS Section on Path Breaking Research and has served as Senior Editor for MISQ (2 terms), the JAIS (4 terms), among others, and as Associate or Advisory Editor for 13 journals (including JMIS, ISR, JSIS, ISJ). Dr. Grover's current work focuses on the impacts of digitalization on individuals and organizations. He has received numerous awards for teaching and research and is an AIS Fellow and AIS LEO recipient for lifetime achievement.

Kalle Lyytinen (PhD, Computer Science, University of Jyvaskylä; Dr. h.c. mult) is Distinguished University Professor at Case Western Reserve University and a distin-guished visiting professor at Aalto University, Finland. He is among the top five IS scholars in terms of his h-index (96); he has the highest network centrality among the IS scholars. He AIS Fellow (2004) and the LEO Award recipient (2013), and the former chair of IFIP WG 8.2 “Information systems and organizations”. He has published over 400 refereed articles and edited or written over 30 books or special issues. He has won best paper awards from AoM, AIS/ICIS and other societies and served as SE or editor to all IS journals and several leading organization theory and innovation journals. He conducts research on digital innovation and its dynamics and organizing, complex design work, requirements in large systems, and emergence and growth of digital infrastructures.

IS Views on Innovative Theory.

Authors	Problem with current IS theory	Field Success	Recommendations for the field
Benbasat & Weber (1996)	Too much reliance on reference discipline theories	Based on a unique body of knowledge	Cultivate a novel paradigm and manage diversity between not within disciplinary fields
Baskerville & Myers (2002)	IS consumes theories from other disciplines but its knowledge products are of little interest to those outside the field	Have a wider constituency of knowledge stakeholders	Redirect research to make IS research widely available and relevant to other disciplines
Benbasat & Zmud (2003)	Lacks unique IT or IS components	Have a unique identity reflective of unique IS/IT constructs within a nomological network	Open the “black box” of IS as to provide unique contributions to understanding of IS phenomena
King & Lyytinen (2006)	Does not serve praxis well	Balance theory and practice. Retain plasticity in theorizing and empirics	Theory can only serve as a means to effective praxis by producing strong results with salience
Truex et al. (2006)	Uninformed borrowing of theories with little regard for assumptions	The quality of theory resulting from reflexive adaptation of outside theories	Adapt theories by carefully considering the focal theory’s fit with the current phenomena and context
Weber (2012)	Difficult to assess high quality theory	Recognize when and how to enhance theories or discard them	A set of criteria to modify existing theory or build new theory as to improve its validity or salience
Avison & Malaurent (2014)	Too much emphasis on “rigorous” theory of a certain type	Publish alternative forms of contributions rather than focus exclusively on theory	Change publication norms to recognize contributions lighter on theory but making alternative contributions
Gregor (2006)	Ability to identify and justify surprising ideas and new findings	Strong theorizing around focal phenomena central to the field’s success	Focus on features of theorizing process and epistemological issues
Markus (2014)	Prevalence of weak theory or overly narrow definitions of theory and theoretical contribution	Broaden problems and reduce trivial research to contribute to stronger theories	Include theory of the problems and theory of the solution categories to address larger societal issues in IS
Burton-Jones et al. (2014)	Overly restrictive in its singular use of one perspective like variance, process, or system	Enrich and engage with more flexible theoretical perspectives that go beyond singular perspective	More flexibly integrating elements from different perspectives results in richer ontological representation of theories about the same focal phenomenon
Straub (2012)	Lack of native theories in IS is not true	Based on influential theories on focal IS phenomena	Need better scientometric studies on knowledge creation and transfer within and across IS
Grover & Lyytinen (2015)	Relies on references theories in a scripted manner leading to avoid novel theorizing or careful local empirics of novel phenomena	Based on strong indigenous theory that deals with novel aspects of digitization	Broaden contributions that foster novel, blue-ocean theory and descriptive theory
Markus and Rowe (2018)	Confusion due to a lack of understanding about causality in theory	Deeper understanding of alternative causal structure	To understand IT impact IS scholars must engage in varied forms of causal theorizing

Appendix B

The status of IS theorizing.

	Assessment			Conclusion
Extent to which theory is changed within the field	No change or minor change	Moderate change	Extensive change	In most cases theories are borrowed and tested without much change in constructs or logic
Percentage of studies (n = 251)*	57%	31%	12%
Extent to which IT is theorized	IT not theorized—treated as nominal or as a proxy	IT is an artifact that is used as a tool or a computational capability	IT is considered holistically in a socio-economic context	Limited theorizing of IT which is exogenous in most studies
Percentage of studies (n = 251)*	58%	29%	13%	Limited theorizing of IT which is exogenous in most studies
The use of transaction cost economics in IS	TCE is largely tested on IS phenomena	TCE is moderately changed to adapt to IS phenomena	TCE is substantially changed based on the IS phenomena	IS largely draws from TCE uncritically, using its constructs (as is or modified) and logic to study Is phenomena
Percentage of studies (n = 96)+	65%	33%	2%

*Theory-based articles randomly selected from MISQ, JMIS, and ISR from 1998–2018.

⁺Articles drawing from TCE identified in the basket of 8 journals (and Management Science).

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