Innovative theory in the digital age: Clarifying our positions

The authors in their response offer two cautionary notes of a naïve reading of the paper, namely (a) a need to re-emphasize the value of attending to the cumulative tradition, and relatedly (b) a risk mobilizing IS scholarship toward clickbait research. These are both perhaps reflective of weaknesses in our exposition, not our argument as such. We thus welcome the option to address the threats of such misreading. We do agree with the excellent points the authors make regarding the dangers of such a misreading of our text. At the same time on both points, they extrapolate our ideas to positions we never intended to put forward. We, in fact, vociferously oppose not leveraging our rich extant literature around IT and digital and are viscerally opposed to the idea of fashion driven clickbait research. The fact that the authors raise these as possible ways to use our paper to warrant research in and around digital, is concerning and indicates that we need to clarify our position. In this response article, we address authors’ specific claims (in bold italics below) with the intent to (a) clarify our position on the message so that there is less space for misinterpretation, and (b) reinforce some points the authors themselves are making. It is our hope that by reading our response the readers will benefit from this dialog on “theorizing around digital” and this dialog helps us collectively advance theorizing in productive directions.

G&L see the (digital) shift as an opportunity to generate important and impactful theories—unencumbered by the tired, old, poorly-fitting theoretical perspectives from the bygone industrial age.

We never claim that reference discipline theories are useless because they originate from a bygone industrial age. In fact, we are great admirers of these theories and how these theories have been instrumental in contributing to explaining aspects of information system use and their effects in organizations and advanced the quality and status of IS research. We do claim, however, that these theories are not ours in the sense that they originally addressed different questions and phenomena and in consequence their usefulness in a changing world is diminishing. Our core message is to reduce our primary dependence on these theories as intransigent inputs into our work and to be open to modifying them based on digital phenomena.

However, looking at work in the field over the last decade, we get the sense that they are overstating the field ’ s slavish devotion to reference theories.

The authors are partially right. There was a time (arguably through 2015) where most of what we would call behavioral IS research invariably drew from some theory housed in reference disciplines. This fact is also backed by evidence in our appendix where we offer synthesis of two of our studies where we examined the field’s dependence on reference theories. In recent years, the “slavish devotion” appears to have indeed declined (though the verdict is not fully in) as the field’s scholars have increasingly started to explore novel and somewhat unprecedented phenomena. In many cases, this exploration benefits from the access to big data and new computational analytic techniques. Given what we state in our paper, we welcome this as a positive trend. However, we still experience considerable slavish and unreflective following of reference theories. Our point is to weaken such strong path dependencies in our theorizing and rather use reference theory as one of many inputs injected with our imagination and creativity (abstract thinking skills) to study digital phenomena.

G&L explicitly dismiss traditional reference theories as no longer fitting this new phenomenon: “ Recent digital phenomena due to their nontraditional character call for new theorizing unbounded by conventional, received reference theory framing and related logics ” (p. 2). In doing so, they also implicitly dismiss the cumulative tradition of IS scholarship.

We are surprised by this inference. Our thesis is, indeed, to reduce the shackles of reference theories, which by definition do not originate from the IS discipline. However, we never suggest that IS literature should not be leveraged, or that even that theories from outside the field should not be read, interpreted, and applied, or that we should not build cumulative traditions around specific themes arising from pervasive digitalization (such as what is the structure and boundaries of the firm). In fact, as we posit, while digital phenomena have a unique character, we can and need to learn from traditional theories focused on pre-digital phenomena for example addressing adaptive usage, media synchronicity, etc. We, for example, marvel at the powerful transformation of old and tired media richness theory (a reference discipline theory) which was for a long time considered immutable in our studies, when it was extended and modified based on a careful conceptual analysis of contemporary IT-based communications technologies into media synchronicity theory. This case is what we see as an appropriate use of reference theories where we create a two-way relationship with digital phenomena and reference theory. We need more of such triangulation.

Regarding cumulative tradition, our position is the opposite what is the authors seem to suggest. We argue that data driven research that is now growing in incidence is often dependent on corporate data sets that are idiosyncratic to the focal phenomena. Without continued abstracting to a family of general problems, it will stand isolated and fragmented and will fail to contribute to the cumulative tradition. We make the case for such abstraction in the context of big data elsewhere (Grover et al., 2020) and it needs not be repeated here. Our whole case is to advance generalizable socio-technical research of a special family of socio-technical systems where digital is now a pervasive critical mediating technical element. We emphasize the need to go deeper into the socio-technical interactions within such systems with better constructs (this applies to old socio-technical concepts originating from open systems theory, too). We indicate in our paper that to evaluate innovative theory in such context, we need to ask whether “the theory generates 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?”

A naïve reading of their paper may serve as cover for increasing work that chases new phenomena while ignoring what we already know—what we refer to as “ clickbait ” research. The second and more important problem is that it risks overlooking the opportunity that the strong foundation of prior IS scholarship affords for informing other fields.

We were taken aback by the use of the disparaging term “clickbait.” If clickbait implies that we need to deal with contemporary digital phenomena emerging at an unprecedented pace, then we agree. If it means endless chasing of technology fashions and selling every possible new technology as a “snake oil” without theoretical reflection we disagree. In our essay, we strongly imply that the field needs to be current and topical (in Grover and Lyytinen (2015) we call it “pre-science”); the theories we produce need to have fidelity with the phenomena.

However, the authors seem to imply another interpretation of the term which is closer to the latter. The term “clickbait” suggests that there is no need grounding the study in the literature—or leveraging previous abstracted insights. It is true that to understand new phenomena, we struggle always with proper vocabulary and how to “read” theoretically the new technology features and their potential uses. To push such process further, we need creativity and ingenious abstract thinking from the brilliant minds of our field. Our message is that we need encourage this creativity in our journals rather curbing it by being locked into institutional practices that weed it out by requiring every theoretical idea to be tested in the same paper. ¹ “Clickbait” also implies that we propose a complete rejection of the prior literature. Absolutely not. Even most dull reference theories can be important. But in doing so, we encourage a more flexible linkage between the theory and phenomenon. This implies using the theory along with other creative inputs and being willing to modify the theory by fostering two-way interactions between the theory and phenomena. We even give examples of how such a two-way interaction can be created (eg media synchronicity theory from media richness theory, and move to the middle from transaction cost theory). These theories are now indigenous to the IS field and are widely referenced. As such, they serve as exemplars for the type of theorizing that we encourage, which would in our opinion, enhance the IS scholarship that informs other fields!

The potential traps that we see arising due to this include chasing phenomena and ignoring commonalities with what we already know. At best, we risk recreating existing knowledge with new terms, which denies the field from building an edifice of knowledge….. At worst, this could inspire chasing any new phenomenon as novel and being entirely phenomenally driven— in essence, clickbait research…. If this is misconstrued, we may end up with a plethora of theories claiming to be novel because of the newness of a phenomenon without due recourse to what has come before or due diligence in first examining to what extent prior or distal theories capture the phenomena.

This would be an issue if we argued for a derivation of theory solely from the emerging phenomena. This would create local silos of theory tied to a contextual phenomenon and not to the literature. Our argument is the contrary, that we should not only do this. In fact, elsewhere (and briefly in this paper) we allude to big data research and its reluctance to abstract and link to general problems—which inhibits cumulative tradition. So, we agree with the authors and are very much in favor of establishing connections with the literature (including reference theories). Our case is to pursue a more flexible approach of how to use theory and blend it with individual creativity to formulate theories of genuine, fluid, and pervasive digital phenomena. So, our message is that we need to loosen the structures that have served us well in the past but now seem to be pushing us in rigid directions of scripted theorizing.

GTM has been criticized for what is seen as a tabula rasa approach, where the researcher is a “ blank slate ” ….. Similarly, we caution researchers to be well-steeped in the existing tradition to understand how any emerging theoretical perspective goes beyond existing knowledge.

We agree. The last thing we want the field to do is to think that creating idiosyncratic theories (or models) that are unique to a company or context. There must be backward and upward links. Even when focal digital phenomena are novel, it will share many touch points to existing literature and reference theories that can be creatively leveraged to shape the contours of innovative theory.

A place where the authors might quibble with our stance is if we encounter new digital phenomena. We believe that we should conceptualize and develop the proper constructs to study it. Retrofitting established reference theory constructs (with minimum modification, as we currently do) is not productive when the phenomena are truly novel (ie every hammer sees a nail). These concepts can be derived from the literature when it offers salient ways to read and make sense (or fail to make sense) of the new phenomena. However, we are also strong believers in building constructs through deeper engagement with the focal phenomena (eg descriptive or grounded study) to calibrate new constructs that can be used to build innovative theory. Our contention is to draw from literature, theory, descriptive study, and inject creativity in building and testing innovative theories that explain and predict digital phenomena.

While we agree that researchers should not be shackled to the application of existing theory to describe new phenomenon, this does not mean that existing theory has no role. Existing theory serves as a language to make sense of phenomena and signal discourse with a community of conversant.

This is tricky. While reference theory provides firm structure, by being too dependent on that structure (constructs, logic, relationships) we end up testing repeatedly the old theory in a new context (Grover and Lyytinen, 2015). In contrast, by eschewing existing theory, we end up with isolated islands of interesting work. We argue for constantly balancing this tension by a creative use of existing theory which we can call a loose, two-way coupling. In fact, we have a section in the paper that argues for more two-way interactions between reference theory and the phenomena.

Problematization requires that prior research and existing knowledge be first represented and organized in order to establish a compelling context for a contribution that reflects the status, consensus, and assumptions of previous work.

We could not agree more. Taking this a bit further, we argue that problematization should be done on both the research side (benchmark with existing knowledge) as well as on the practice side (clearly describe what compelling problem is being addressed).

Given the tremendous opportunity that large, diverse datasets and computational techniques present researchers, forcing all researchers to problematize existing theory would be an unnecessary requirement if we wish to explore new patterns with computational methods. But by relaxing the need to problematize, this does not mean the cumulative tradition should be ignored. Advocates of exploratory research still require that researchers engage with theoretical perspectives.

This is indeed fully aligned with our argument concerning big data research (Grover et al., 2020), where we caution on the need to create links to build theory. We caution against “clickbait” research where the convenient access to big data sets, often covering tactical data, and applying some “cool” esoteric computational technique is shown to produce solutions to problems that are mainly company specific. Without cultivating necessary theoretical links (eg by abstracting to the archival problem), and identifying boundary conditions this kind of research is likely to remain an island.

To conclude, we hope that this response clarifies and reinforces our paper’s position. We agree with many of the authors’ points about threats of misreading. We hope that this clarification reduces the likelihood that readers will misinterpret our message as they suggest. We especially want to reinforce their core points on the importance of cumulative tradition and not falling into the clickbait trap when we theorize about emergent digital phenomena.