Insufficient theoretical contribution: a conclusive rationale for rejection?

Have you ever received a rejection letter that goes something like this?

The manuscript presents an exciting empirical study of an important and timely phenomenon. However, the reviewers, who are all experts in the area, fail to recognize a theoretical contribution on a par with what one would expect from an article in a premier journal such as EJIS.

If you have, you are not alone. In fact, one of the most common reasons for rejecting submissions at EJIS and other prestigious journals in our field is insufficient theoretical contribution (Venkatesh, 2006; Straub, 2009). It seems as though reviewers and editors sometimes use a vague reference to insufficient theoretical contribution as an indisputable reason for rejecting a submission that they do not like when they cannot quite put their finger on why they dislike it; a ‘polite brush-off for papers with various kinds of shortcomings’ as Hambrick (2007) eloquently puts it.

To some extent, theoretical contribution, or, rather, lack thereof, seems to trigger a gut reaction – it has become a mentality rather than a quality criterion. Certainly, prospective authors have the right to know the reasons for rejection and editors and reviewers could be better at detailing their specific concerns in a developmental spirit. This is indeed an important area for improvement at many journals. However, what I will address in this editorial is not how better to explain why a certain paper is lacking in the theoretical department, but rather to question the idea that insufficient theoretical contribution is always a bad thing, and a conclusive rationale for rejection. What if insufficient theoretical contribution could make room for something else that allows a particular paper to shine – something that would see it offer truly significant implications? Perhaps one could even expect to find such papers in a journal that explicitly welcomes ‘submissions with a critical and empirical view’, as highlighted in the EJIS Instructions for Authors.

To qualify for publication in a top journal, a paper must make a substantial contribution to knowledge. However, a contribution to knowledge is not necessarily a theoretical contribution. Actually, with the recent introduction of Theory Development as a distinct submission category at EJIS, a reasonable question to ask is to what extent we still expect theoretical contributions from papers submitted under other categories.

In a typical research paper published in a top information systems (IS) journal, one would expect to find an explicit discussion about its theoretical contribution, followed by implications for research and practice. Below I will argue that for certain papers, what needs to be emphasized is, rather, a discussion of the empirical contribution, followed by possible implications for theory. Another hallmark of articles in top IS journals is that they typically start with a literature review that focuses on theoretical contributions and theoretical models (Rowe, 2011). In addition to identifying a research gap, such a review often results in the development of a research model or theoretical framework. As I will show below, this approach may seriously hamper strong empirical contributions. In the following, I make a deliberate distinction between theoretical implications in relation to theoretical contributions on the one hand, and in relation to empirical contributions on the other, and explain why such a distinction can be useful. I also provide tentative definitions of some central concepts that will be helpful in articulating why less focus on the theoretical contribution can be desirable. I do not claim these definitions to be ‘correct’ beyond the scope of this editorial, and other people may choose to use the concepts differently.

Research contributions and implications

In a comprehensive treatment of what constitutes a theoretical contribution, Corley & Gioia (2011) draw on Sutton & Staw (1995) to define ‘theory’ as ‘a statement of concepts and their interrelationships that shows how and/or why a phenomenon occurs’. It follows that a theoretical contribution is something that advances our understanding of such concepts and interrelationships. Corley & Gioia (2011) further suggest that in order to be seen as significant, a theoretical contribution needs to show both originality and utility.

The originality, or novelty, of a theoretical contribution is closely related to its theoretical implications, and the two are often discussed in conjunction. To wit, a theoretical contribution must be discussed in relation to existing theory in order to be established as a contribution. Thus, theoretical implications can be seen as a required rationale for the theoretical contribution. However, the theoretical implications of a theoretical contribution are also related to the scientific usefulness of the contribution, and thus to its more wide-ranging implications for research, for example, to what extent the new understanding prompts further theoretical elaboration beyond the current research context. Although scientific usefulness is often regarded as the most prominent aspect of a theoretical contribution, it must also show utility for practice (Corley & Gioia, 2011). Elaborating such implications for practice is especially critical in an applied field such as IS.

A commonly agreed-upon definition of an ‘empirical contribution’ is hard to find. I suggest that it can be understood in light of the above definition of a theoretical contribution. An empirical contribution can then be thought of as a novel account of an empirical phenomenon that challenges existing assumptions about the world or reveals something previously undocumented (cf. Rowe, 2011). Here, ‘novel’ refers to either the phenomenon or the account, or both. An empirical contribution thus reveals insights into a phenomenon, and does not have to rely explicitly on any a priori conceptualizations – although it typically does to some extent (Thomas & James, 2006). Similar to a theoretical contribution, an empirical contribution needs to show both originality and utility, and give rise to implications for both research and practice.

As opposed to a theoretical contribution, the originality of an empirical contribution is not intrinsically tied to possible theoretical implications. One can, at least in principle, provide a rich account of an empirical phenomenon without theorizing about the findings. Instead, theoretical implications of an empirical contribution materialize outside of the immediate research context, and thus cannot be specified in full detail; they are effects that are beyond the control of the researcher, and depend on how the research is subsequently taken up by others. A piece of research can be ‘theoretically interesting even if it is not theory-driven’ (Baker & Pollock, 2007, p. 305). Consequently, it is certainly possible to speculate about potential theoretical implications in the sense of implications for research by pointing out future research directions. Notably, an empirical contribution is not the same as an implication for practice, although an implication for practice can be enacted, observed and treated as new empirical data, and thus constitute an additional empirical contribution. This is a typical pattern of action research, for example.

It follows from this that implications for research and practice (as typically detailed in IS research papers) should not be confused with theoretical implications of theoretical and empirical contributions. An implication for research may be an identified need to investigate a phenomenon further. An implication for practice may be an identified need to address an identified practical problem.

The problem

The relationship between theory and empirical facts is often described in terms of generalization from empirically observable facts to theoretical statements, validation of theoretical statements through observation of empirical facts, or some combination of the two. Theory and empirical facts thus go hand in hand. On the one hand, theories help to organize our thoughts, explain phenomena, ensure consistent explanations, improve our predictions and inform design. On the other hand, empirical data is required to develop and validate theory and to motivate and evaluate designs. However, there is no intrinsic reason for each piece of published research to go full circle and claim a substantial theoretical contribution. On the contrary, there are strong arguments for ‘theory-light’ papers (Avison & Malaurent, 2014) that focus on empirical contributions and defer claims to theoretical contribution until later, possibly by other researchers (Hambrick, 2007).

For good reasons, theory and theorizing are at the heart of the scholarly enterprise (Weick, 1995). Theory development has even been characterized as ‘what sets us [academics] apart from practitioners and consultants’ (Gregor, 2006, p. 613). However, a one-sided focus on theory may downplay possibly significant implications of empirical contributions. For example, emphasizing the theoretical contribution effectively precludes pretheoretical research, that is, empirical research that reports findings for which no existing theory can account (Miller, 2007). Such facts could potentially stimulate the search for an explanation (Hambrick, 2007), and thus eventually lead to significant theoretical implications. The quest for a theoretical contribution may also lead to unhealthy behaviour in which researchers are tempted to fit their data into a theoretical framework such that facts that may contradict the theory are omitted so as not to expose gaps – what Sutton & Staw (1995, p. 381) refer to as ‘hypocritical writing’. Strict adherence to a theoretical framework may also distract researchers from identifying truly exciting empirical phenomena in the first place (Avison & Malaurent, 2014). Such theoretical blinders may reduce a brilliant research idea into something uninteresting with obvious conclusions. In other words, applying a well-known theory to a new phenomenon may serve only to replicate already well-known findings and prevent the researcher from seeing things differently. Furthermore, in an effort to convince reviewers of an important theoretical contribution, authors may overreach by ‘deriving sweeping conclusions that outstrip the data’ (Geletkanycz & Tepper, 2012, p. 259). Treating ‘theory as king’ (Straub, 2009; Avison & Malaurent, 2014) at any cost can easily turn a potentially strong empirical contribution into a ‘contorted, misshapen, inelegant product, in which an inherently interesting phenomenon has been subjugated to an ill-fitting theoretical framework’ (Hambrick, 2007, p. 1349).

A further example, at the heart of our own discipline, is design science research (DSR). When Hevner et al (2004) placed DSR firmly on the mainstream IS research agenda, one of the basic tenets was that it would allow the publication of descriptions of innovative IT artefacts. Although such artefacts were supposed to draw on existing kernel theories, they were essentially envisaged as empirical contributions. To quote Hevner et al (2004, p. 87), ‘Most often, the contribution of design-science research is the artefact itself’. However, it has proven difficult to publish novel design artefacts as purely empirical contributions without substantial theoretical contribution (Gregor & Hevner, 2013; Goes, 2014). According to Pries-Heje & Baskerville (2013), the resultant wrapping of new science in old science may lead to ‘confusion and identity reversal’ (p. 7). Reviews that acknowledge a novel design artefact but, due to lack of theoretical contribution, dismiss it as design practice rather than design science are clear indicators of such confusion. Notably, a theoretical DSR contribution does not require the instantiation of any actual artefacts (Gregor & Jones, 2007). On the other hand, ‘it is absolutely not a requirement of successful design science manuscripts to have an explicit tie to theory’ (Goes, 2014, p. vi). It all seems to boil down to whether one regards DSR as ‘research that aims at theoretical contributions through design’ or ‘research with design as the topic of investigation’ (Kuechler & Vaishnavi, 2008; Iivari, 2014).

DSR involves the design of socio-technical artefacts (Gregor & Hevner, 2013). Thus, to make a contribution, a DSR artefact must be explored in relation to its organizational and social context and be understood as the result of a creative process – a purely technical focus would be outside the scope of most major IS journals. Accordingly, an empirical DSR contribution could, for example, be a rich description of an artefact and its rationale in relation to anticipated use, a rich description of the design process leading to such an artefact, or an empirical account of the artefact in actual use. A theoretical DSR contribution, on the other hand, would probably package prescriptive principles as a design theory applied to a class of artefact or develop a predictive theory of artefacts in use. Viewing the role of IT artefact design only as a means towards theoretical contribution is akin to the one-sided focus on theory outlined above. Such a focus may result in lost or poorly described design details. It may even effectively prohibit the publication of potentially important DSR artefacts.

A possible way forward

Interestingly, many scientific disciplines frequently publish studies that do not stress theoretical contributions at the expense of empirical contributions. Medicine is perhaps the most significant example in which, for example, studies may report on how patients respond to a particular drug or treatment. When several such studies have been published, patterns begin to emerge, which may serve as a foundation for theorizing (Egger & Smith, 1997). Fields closer to our own also frequently publish papers with primarily empirical contributions. We see, for example, media studies reporting on the use of social media in various contexts (e.g., Larsson & Moe, 2012) and software engineering studies reporting on the use of particular development practices (e.g., Kim et al, 2014) without referring to any grand theory in order to explain findings or predict outcomes. A common denominator is that they focus on describing interesting empirical phenomena that may eventually have theoretical implications. Importantly, imposing a theoretical framework on such studies may lead to at least two undesirable effects. First, the empirical account would be unlikely to be as rich because only facts relevant to the chosen theory would be reported. Second, it may create a sense of theoretical belonging of the findings that may militate against the use of the findings in future studies with different theoretical affinities – ‘with low-inference descriptions, researchers will agree more readily’ (Sandelowski, 2000).

Altogether this suggests that without disregarding the importance of theoretical contributions, empirical contributions deserve to be acknowledged as important building blocks in the scholarly enterprise. If we choose to regard empirical contributions as being on a par with theoretical contributions rather than as subordinate (in a given study), then we can think of contributions as existing on a continuum – less emphasis on theoretical contributions provides space for more elaborate empirical contributions, and vice versa. One can also conclude that you cannot have one without the other. A theoretical statement needs to be validated through empirical observation (unless one subscribes to a purely rationalist view). Conversely, a rich empirical account would need to be somehow summarized and abstracted in order to answer a research question with precision, and is thus never devoid of theory. Empirical findings need to be interpreted and related to theoretical concepts and previous research, but the aim does not have to be a substantial theoretical contribution.

Two EJIS submission categories lend themselves particularly well to empirical contributions: Ethnography/Narrative and Empirical Research. In a sense, ethnographies and narratives are perfectly suited to making empirical contributions because they can be seen as providing archetypes for in-depth research, rich empirical description and engagement in the field (Myers, 1999; Rowe, 2012). However, empirical studies other than ethnographies and narratives may also produce important empirical contributions. Interpretative case studies (Walsham, 1995; Avison & Malaurent, 2014) spring to mind as an obvious example. Another example is Yin’s (2014, p. 49) notion of the ‘revelatory case’ in which ‘the case study is […] worth conducting because the descriptive information alone will be revelatory’. DSR studies can present artefacts as substantial empirical contributions that can become building blocks in a journey towards theoretical contribution that goes beyond what can be achieved in a single paper – ‘Demonstration of a novel artifact can be a research contribution that embodies design ideas and theories yet to be articulated, formalized, and fully understood’ (Gregor & Hevner, 2013, p. 341, Footnote 4).

Most if not all of the relatively few existing publications in IS that offer significant empirical contributions employ qualitative research approaches. Miltgen & Peyrat-Guillard (2014) provide a recent example through their qualitative assessment of attitudes towards privacy, personal data disclosure and protection, using focus groups across several European countries. Although partly submitting to traditional theory contribution parlance, their study illustrates well how an essentially descriptive study can challenge existing assumptions and beliefs in a positive way without elaborate theoretical accounts. However, as indicated above, significant empirical contributions are not restricted to traditional qualitative research. On the contrary, DSR, surveys, experiments and randomized controlled trials are also viable candidates. In an earlier editorial (Ågerfalk, 2013), I pushed for the use of mixed methods and paradigms to embrace diversity in IS research. In keeping with that spirit, I would like to suggest that mixed research designs are perhaps particularly well-suited to making significant empirical contributions because they allow for elaborate combinations of rich empirical material and large data sets.

Conclusion

In this editorial, I set out to explore whether lack of a theoretical contribution could actually be something positive for the development of our field. My conclusion is that it can. Importantly, though, I am not arguing that theoretical contribution is unimportant or that our top journals should not foster theoretical development – quite the opposite. What I argue is that we should acknowledge the value of strong empirical contributions, even at the expense of theoretical contributions in the short term. An important aspect of doing this is to distinguish between theoretical contributions and theoretical implications. Empirical contributions may have more far-reaching theoretical implications than many self-proclaimed theoretical contributions.

From an editor’s point of view, I would thus welcome a future in which we spend more of our precious journal pages on exploring original and useful empirical contributions than on arguing theoretical contributions that are tenuous at best. After all, ‘it is a critical role of top journals to publish more enigmatic papers’, as Rowe (2011, p. 492) puts it. Paraphrasing Hambrick (2007, p. 1350), I would like to suggest that instead of always looking for a strong contribution to theory, reviewers and editors should be promoting papers that are likely to stimulate future research with the potential to alter IS theory and practice, that is, papers with potential theoretical implications but not necessarily already established theoretical contributions. Note that this is not to do with rigour vs relevance; a significant empirical contribution is always the result of rigorous research.

To summarize, I would like to offer the following advice to authors and reviewers/editors.

Authors: If your paper is making a truly significant empirical contribution, emphasize that contribution rather than bolstering and over-selling a possibly contested theoretical contribution. Be careful not to confuse empirical contribution with implications for practice. However, make sure that you explore the theoretical implications of your findings. In doing so, refrain from drawing far-reaching (and far-fetched) conclusions, as it is likely they will only suggest a limited applicability for future theory development based on your work. You do not have to begin the paper with a literature review section. Situating the empirical contribution in the relevant scholarly discourse may be more effective towards the end of the paper.

Reviewers and editors: Do not assume that the authors should be aiming for a noteworthy theoretical contribution, even if they say they are. If the paper, in your view, is making a strong empirical contribution but lacks a theoretical contribution, help the author to see this, and suggest how to reformulate a questionable theoretical contribution into potential theoretical implications that can lay the groundwork for future theory development by these authors and others.

One may argue that what I have created in this editorial is nothing but a straw man; that we knew this already, and all we need to do is to pay more attention to how we as authors present, and as editors and reviewers appreciate, research contributions. Nevertheless, I hope that what I have proposed will help to increase awareness of these issues and ideally trigger a discussion on possible implications for editorial policy. As for the question of whether or not EJIS requires theoretical contributions from papers submitted under categories other than Theory Development, the answer is ‘yes’, at least to some extent. It is hard to think of a strong empirical contribution that has not made any attempt to interpret the findings and position them in relation to other studies. Similarly, a DSR artefact typically has to be motivated and explained in relation to kernel theories and a conceptualization of the problem it addresses (Baskerville & Pries-Heje, 2010; Gregor & Hevner, 2013).

I admit that this editorial has over-simplified complex phenomena and deliberately avoided several possibly contentious issues. Nonetheless, I hope that the intended message to authors, reviewers and editors has been clear: try not to get too hung up on the theoretical contribution (or lack thereof), and focus instead on novel and useful ideas that can help advance our understanding of IS.

In this issue of EJIS

This final 2014 issue of EJIS comprises seven articles. The first article ‘Paradigm lost … paradigm gained: a hermeneutical rejoinder to Banville and Landry’s “Can the Field of MIS be Disciplined?” ’ by Nik R Hassan, University of Minnesota Duluth, revisits the seminal paper by Banville & Landry (1989) and provides an updated view of scientific progress for the IS field. Drawing on Gadamerian hermeneutics, the author analyses Banville and Landry’s characterization of IS in the light of Kuhn’s notion of the scientific paradigm and articulates a number of implications for our understanding of IS as a contemporary scholarly field. The article concludes that IS need not be in a perpetual state of fragmentation. However, this would require IS scholars to reach agreement on the basic elements that characterize the IS field and refrain from primarily defining ourselves in relation to reference disciplines.

The second article, ‘The competitive impact of information technology: can commodity IT contribute to competitive performance?’, is presented by Gabriele Piccoli, University of Pavia, and Tsz-Wai Lui, Chinese University of Hong Kong. The article reports an empirical study of 165 U.S. hotels utilizing self-service check-in kiosks over a 2-year period and draws on data from 3465 self-service transaction records. The impact of this technology-enabled incremental channel on the competitive performance of the hotels is analysed by testing the interaction between IT resources and complementary strategic resources. The results point to the importance of synergistic interaction between organizational resources and IT assets in shaping the competitive influence of IT-dependent strategic initiatives, which challenges the view of ‘IT as a strategic commodity’. The study also demonstrates that sustained competitive advantage is not to be found in any one single component of the IT-enabled strategic initiative, but instead in the interactions among them.

The third paper, ‘No time to waste: the role of timing and complementarity of alignment practices in creating business value in IT projects’, is co-authored by Armin Vermerris, Philips IT, Martin Mocker, MIT Sloan Center for Information Systems Research and Eric van Heck, Erasmus University. The study focuses on operational practices that facilitate business and IT alignment in IT projects and the impact of such practices’ timing and complementarity on achieving alignment. The study cross-analyses six IT projects in three telecommunications companies. The results suggest that achieving high level of IT business value requires high levels of communication, shared understanding, management commitment and IT investment evaluation in each phase of the IT project value creation process. The results also point to complementarity among the alignment practices in the different phases and to the critical importance of adopting such practices at the early phases of IT projects.

The fourth article, ‘A “sweet spot” change strategy for a least developed country: leveraging eGovernment in Bangladesh’, is presented by Shirley Gregor, Australian National University, Ahmed Imran, University of New South Wales and Tim Turner, University of New South Wales. Springing from the need to design and carry out an intervention that would assist Least Developed Countries’ (LDC) adoption of e-government, the study investigates the sweet spot change (SSC) strategy for LDCs, that is, the point of maximum leverage and focus of change efforts. Using an action design approach, the researchers worked with AusAID and partner organizations in Bangladesh in a multi-phased project that aspired to reduce knowledge gaps among key decision makers. The study brings forward four key SSC strategy principles: (1) identifying and acting on the sweet spot, (2) engaging influential stakeholders, (3) embedding local knowledge and (4) tailoring the intervention to suit the particular LDC.

The fifth article, ‘An empirical investigation of technology readiness (TR) among medical staff based in Greek hospitals’, is contributed by Christos Melas, Technological Educational Institute of Crete, Leonidas Zampetakis, Technical University of Crete, Vassilis Moustakis, Technical University of Crete and Anastasia Dimopoulou, Penteli General Paediatric Hospital of Athens. The study examines the level of technological readiness (TR) for information and communication technology (ICT) usage among medical staff by formally identifying TR profiles, and modelling preference TR variations relating to computer use, computer knowledge and computer feature demands. On the basis of a nationwide Greece study with 604 responses from physicians and nurses, the survey results show that TR profiles of medical staff in clinical settings match the TR profiles of the general population. The study suggests important managerial implications, such as targeting the introduction of technological innovations first towards ‘explorers’ to avoid discomfort and insecurity.

John Veiga, Univeristy of Connecticut, Marcus Keupp, Swiss Federal Institute of Technology, Steven Floyd, University of Massachusetts and Franz Kellermanns, University of North Carolina bring us the sixth article of this issue, ‘The longitudinal impact of enterprise system users’ pre-adoption expectations and organizational support on post-adoption proficient usage’. Through a survey of financial analysts’ self-reported pre- and post-adoption proficient usage, the article examines why some Enterprise System (ES) users become proficient utilizing most of the ES features while some do not. The study shows that new system users who are internally motivated by stronger intentions to use the ES do so in ways that enhance their cumulative knowledge acquisition and increase their usage proficiency. Beyond internal motivation, users’ external motivation, driven by performance outcome expectations, also plays a role in enhancing usage proficiency. Intention to systematically integrate a system into work routines was also found to have a significant role in enhancing proficient post-adoption usage. Finally, when system adopters encounter higher levels of organizational support, the indirect influence of pre-adoption expectations on proficient usage is significantly higher. When actual usage is low, higher levels of organizational support lead to even lower levels of proficiency.

‘Internet adoption by the elderly: employing IS technology acceptance theories for understanding the age-related digital divide’ is the final article of this issue, authored by Björn Niehaves, Hertie School of Governance and Ralf Plattfaut, University of Muenster. Drawing on UTAUT and MATH, the article tackles the issue of age-related underutilization of IT by exploring which existing model best explains Internet adoption for the elderly. A multi-channelled survey was instrumented to collect data from 65+ year old in Germany, with 150 usable responses. The study concludes that both UTAUT and MATH can explain Internet adoption by the elderly. However, MATH has a slightly higher explanatory power while UTAUT has greater feasibility (lower number of measured items). Extending these two models with the four socio-demographic variables of gender, income, education and age can increase the explanatory power of both UTAUT and MATH.

Acknowledgements

I am grateful to Kieran Conboy, Ravi Dar, Mats Edenius, Alan Hevner, Frantz Rowe, Mark Silver, Jonas Sjöström, Claes Thorén and Robert Winter for helpful comments on this editorial. I would also like to thank Myriam Raymond for assisting with the article summaries for this issue of EJIS. Finally, I would like to thank the associate editors of this issue for their most appreciated support: Régis Meissonier, Aurelio Ravarini, Andrew Sears, Bernd Stahl, Xiaofeng Wang, Robert Winter, Ryan Wright.