The need for compelling problematisation in research: The prevalence of the <scp>gap‐spotting</scp> approach and its limitations

Abstract

Every year, the Information Systems Journal (ISJ) receives hundreds of papers for review and potential publication. When a new submission is received, we pay careful attention to the positioning and motivation, and on a related note, to the contribution of the submitted paper. The positioning and motivation of the paper strongly determine how the contribution emerges in the latter half of the paper. They are, therefore, quite salient with respect to how the study is conceived and executed. In this editorial, we draw attention to the positioning and motivation of research that is submitted for publication. We also intend to provide potential authors with insights into our expectations. In our experience as editors, we find that authors quite often neglect the positioning and motivation of their submissions. Indeed, the lack of any detailed treatment is often reflected in the reject letter: “we are unable to discover why you undertook this research”. We commonly find that after a cursory introduction, authors plunge headlong into the literature review and hypotheses development (in the case of a quantitative study) or methodology (in the case of a qualitative study). Following the emergent findings (qualitative studies) or hypotheses testing (quantitative studies), we see a summary and routine discussion of the contribution of the work. It is crucial to realize that papers following this model are unlikely to fare very well in the ISJ review process. Methodological rigor is of course important, but it is not sufficient to guarantee publication. Authors must also deliver a compelling contribution in terms of theory or design (e.g., an artifact). This is where the issues of positioning and motivation become critical, because these considerations ultimately shape both the theory and the contribution. We are not saying that submitted papers at ISJ lack any positioning or motivation. However, they are often weak and poorly presented. Exactly who should care about the research, and why, is frequently ignored. What is very popular is the tendency to highlight “gaps” in the existing literature and then to concoct an argument whereby the submitted study addresses those gap(s). We refer to this as “gap-spotting” research, which has been demonstrated as having severe limitations (Alvesson & Sandberg, 2011). While librarians might care about gaps on the shelf and dentists may be troubled by gaps in your teeth, we suggest that researchers should tread warily where gaps are concerned. The many practitioners of gap-spotting research tend to argue that because something has not yet been done, there is value (a contribution) in doing it. However, this is a fallacious argument. The fact that there is a gap in the literature (e.g., some unanswered question) does not necessarily mean that it is worthwhile to plug it. For example, nobody may have investigated if eating chocolates increases programming efficiency. There may well be a connection (chocolate contains sugar, amongst other things, and sugar provides energy) but is this a connection that is worth pursuing, especially in IS research? Even if we find that eating chocolates is positively associated with programming efficiency, what are the practical implications? Should companies distribute chocolates to their programmers every day? Should people who are chocolate or sugar intolerant shun the career of programmer? Is this the kind of contribution to the IS literature (as opposed to Food Science or Human Resources Management) that we wish to publish? Although this is an extreme and somewhat ridiculous example, it serves to showcase that research should be meaningful in its academic and practical implications and not engaged with just for its own sake. The key concept here is relevance, not only to the practitioner community, but also to the academic community. Academicians will see the value of research only when it needs to be done, and not just when it can be done. The gap-spotting approach often demonstrates that a research can be done, but it does not necessarily mean that it should be done. So, what are the alternatives to the gap-spotting approach when the authors consider enhancing the positioning and motivation of their potential submission? We suggest that a more compelling approach to anchor a study, and thus enhance its contribution, is through the problematisation approach (Alvesson & Sandberg, 2011; Sandberg & Alvesson, 2011). The core idea of a problematisation approach is that we should question assumptions and not take previously established findings for granted. Thus, we must challenge prior research and its trends, theories and findings. We should not be in awe to the idols of the theatre (famous people) or the marketplace (loud-mouthed people) (Bacon, 1620). The critique needs to demonstrate how the outcomes of prior research constrict our understanding of the phenomenon. For example, a stream of literature may have used assumption A and theory T. Problematisation questions whether these choices are limiting, or even valid. Do these choices constrain the development of the literature in that area? If so, can alternate theories and assumptions be presented that address these issues? In short, problematisation would present alternate viewpoints to the existing literature and show how these alternate viewpoints are more appropriate than the previous ones. Of course, this is not an easy task by any means. The problematisation technique necessitates that authors develop their own worldview of the existing literature in their domain and use that worldview to critique existing research traditions in that domain. They then present their own worldview and associated theories/assumptions as a way of enhancing existing research. They need to do this in the context of a specific phenomenon that is amenable to investigation and that is worth investigating, that is, where there are identifiable stakeholders who will care about it. If authors genuinely challenge existing worldviews and develop new ones, their own contribution is less likely to be questioned. The most difficult part of the challenge is to establish their worldview in front of the editorial/reviewer teams, but if that can be accomplished then contributory concerns are rendered moot. As a simple example, a study could engage in a nonlinear investigation of some known phenomena. The authors can make a strong case that the existing literature has implicitly assumed and investigated only linear relationships between the constructs of interest. The authors may present their understanding of the phenomenon (worldview) and argue that the phenomenon is inherently nonlinear and not attending to the nonlinearity is constraining the usefulness of knowledge in that literature domain. For example, digitally enabled social networks often support nonlinear processes (Germonprez & Hovorka, 2013) and thus research in this area can challenge linear analyses of social networks and present nonlinear analyses to advance the literature in this area. This is similar to the efforts of Havakhor et al. (2018) who investigate a quadratic model of diffusion of knowledge in social media networks. The importance of challenging prior theories, assumptions, methods, or techniques is particularly salient for IS research. The rapid digitalization of today's world has led scholars to observe that our “core organizing axioms may be challenged or fundamentally changed by the digital revolution” (Benner & Tushman, 2015, p. 498). Given that many (if not all) IS scholars investigate the effect of this digitalization, it is natural that they should reflect whether we need to challenge some of the fundamental axioms of our research. “First, it is important to reiterate that our theories should be problem driven—that is, in some fashion addressing a problem of direct, indirect, or long-linked relevance to practice, rather than narrowly addressing the (theoretical) ‘problem’ of finding the next mediator or moderator variable or filling theoretical gaps simply because they exist. When we focus mainly on the latter, we end up advancing theory for theory's sake, rather than theory for utility's sake” (Corley & Gioia, 2011, p. 22) “In this article, we use this surprising observation—that mobile technology can be consequential for perception and movement even without focal attention—as an opportunity to ‘problematize’ and challenge certain taken-for-granted assumptions that seem to organize our academic and everyday understanding of ‘mobility’ and ‘mobile technology use’” (Hafermalz et al., 2020, p. 2). In this issue of the ISJ, we present four articles. In the first article, Akkermans et al. (2021) focus on reversing a relationship spiral in IT outsourcing (ITO) relationships. Based on a case study involving a European Harbour Authority and its ITO partner, the authors established a process model to describe the innovative ways out of the gridlock vicious cycles engaged in their ITO relationship. In the study, they combined action research with system dynamics simulation to arrive at the novel process theory. This research demonstrates the action research intervention using collaborative service redesign on workflows was effective in reversing the direction of the three inter-locked vicious spirals into virtuous cycles. They then synthesise the observed spirals in a system dynamics simulation model to further elucidate the boundary conditions of the proposed theory established in the action research. In the second article, Ghasemaghaei and Turel (2021) note that while common wisdom suggests that big data facilitate better decisions, it may not always be the case, as big data can also afford and motivate knowledge hiding. To examine this possibility, they integrated adaptive cost theory with the resource-based view of the firm and suggested that the effect of big data characteristics (i.e., data variety, volume and velocity) on firm decision quality can be explained, in part, by data analysts' knowledge hiding behaviours, including evasive hiding, playing dumb and rationalized hiding. They examined this model with survey data from 149 data analysts. Their findings show that big data characteristics have distinct effects on knowledge hiding behaviours. These results were further validated with applicability checks. Importantly, the results can explain inconsistent past findings regarding the return on investment in big data and provide a unique look into the potential “dark sides” of big data. In the third article, Chatterjee et al. (2021) focus on the nonlinear effect of information technology (IT) on organisational innovation. In their paper, organisational IT is represented by harmonious IT affordance (HITA). HITA is a superordinate IT affordance representing the degree of coalignment between the lower level IT affordances of collaboration, organisational memory and process management. The authors theorize and empirically test that the influence of HITA on organisational innovation is fundamentally U shaped (quadratic). This finding has important implications for research on IT and innovation. It reveals that innovation can happen at various levels of IT affordances through an invoking of alternate organisational mechanisms. An important takeaway of this study is that future work on IT and innovation should embrace and build upon nonlinearity as one of the core assumptions driving theorization and empirical analysis. In the fourth article, Tim et al. (2021) discuss how novelties in using digital technology to address societal challenges play a critical role in our collective pursuit of sustainable development. The authors contribute to the growing body of research on digital social innovation and sustainable development by presenting several lessons learned from an in-depth case study on the emergence of “e-commerce villages” in remote parts of China. These constitute a DSI phenomenon that has flourished into a nationwide development program that bridges inequality and alleviates poverty. The authors offer insights and recommendations for policymakers, public and private sector practitioners, and communities in underdeveloped regions to navigate both the potentials and pitfalls of grassroots technology leapfrogging. Specifically, the authors demonstrate that an effective grafting of collective bottom-up actions and top-down interventions can be effective in overcoming the bottlenecks of leapfrogging development and enabling the building of a digitally resilient and sustainable community.

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