A New Label on an Old Idea Is Not a Contribution

The number that stayed with me after reading Sun et al. (2025) was not a sample size. It was the word "triadic." They argue that a contribution needs novelty, rigor, and relevance. Not two out of three. All three. A new label on an old idea, they write, does not count. I kept thinking about how many IS papers I had read that clear one or two of these bars and call it done.

Then I went back to Gregor and Hevner (2013). Their contribution matrix sorts design science work by whether the problem is mature and whether the solution is mature. Invention means a new solution for a new problem. Improvement means a better solution for a known problem. Exaptation means taking a known solution and adapting it to a new problem. Routine design means a known solution for a known problem, and it does not count as a research contribution at all. In their survey, most published DSR work fell into improvement and exaptation. Pure invention was rare. Routine design was absent from the top journals, at least.

But here is what I noticed when I looked at behavioral IS research through this matrix instead of design science: a lot of what gets published as "theoretical contribution" is improvement wearing invention's clothes. Take a model that has existed for three decades, swap "perceived usefulness" for "perceived AI usefulness," add a moderator, test it with survey data from undergraduate students, and claim you have extended theory. You have not. You have renamed constructs and changed the context. The mechanism is the same. The why is the same. Whetten (1989) would ask: where is the theoretical glue? What is the why that justifies why these constructs relate in this new way? If the answer is "because TAM says so," you have not contributed new theory. You have applied old theory to a new context and called it an extension.

Sutton and Staw (1995) made this point from the other side. They listed five things that are not theory: references, data, variable lists, diagrams, and hypotheses. Each can accompany theory, but none replaces the argument. I think about this every time I see a paper whose entire contribution is a new variable list with "AI" or "blockchain" or "GenAI" appended to construct names. The diagram changes. The hypotheses change. The why does not change. The mechanism does not change. That is not theory. That is relabeling.

The problem is not that improvement is bad. Gregor and Hevner are clear that improvement is a legitimate contribution type. Better solutions for known problems matter. The problem is that improvement gets marketed as invention, and the marketing works because reviewers often do not ask the right questions. Burton-Jones et al. (2021) give us a way to ask better questions. They propose four theorizing strategies for the field: replace, reformulate, extend, and envision. Replace introduces new constructs to substitute for inadequate ones. Reformulate applies new logics to existing constructs without abandoning them. Extend adds boundary conditions to cover new contexts. Envision adopts new ontological assumptions about how the world works. These strategies are ordered by ambition. Extending is the most common and the least disruptive. Replacing and envisioning are the rarest and most disruptive. The field publishes mostly extensions, and that is fine if the extension genuinely adds a mechanism or a boundary condition. But extending TAM by swapping "perceived ease of use" for "perceived ease of collaborating with AI" is not a theoretical extension. It is a contextual variation with a new label.

Baird and Maruping (2021) are my favorite example of reformulation done right. They argue that when IS artifacts become agentic, when systems act on your behalf rather than being operated by you, the foundational construct of "use" no longer captures what is happening. Users delegate tasks to agentic systems. They appraise whether the system can handle the task, distribute subtasks between themselves and the agent, and coordinate interdependencies. Delegation is not an extension of use. It is a reformulation. If you extend TAM to cover agentic AI, you flatten precisely the mechanisms that make agentic IS theoretically distinct.

This distinction between extending and reformulating is where most contribution inflation happens. An extension adds a moderator or a boundary condition to an existing model. A reformulation changes the logic. The first is easier to do and easier to publish. The second is harder and riskier. Reviewers tend to prefer incremental extensions over reformulations because extensions are easier to evaluate: you can compare the model before and after the moderator and see whether the fit improved. Reformulations require a different kind of evaluation, one that asks whether the new logic explains something the old logic cannot. I think this is why the field rewards improvement more than invention, and why so many papers end up in the improvement quadrant while claiming the invention label.

Sun et al. (2025) give the quality check. A contribution must balance novelty, rigor, and relevance. Novelty means genuine novelty in constructs, mechanisms, methods, or artifacts. Rigor means methodological soundness. Relevance means practical impact. Each one alone is insufficient. Novelty without rigor is speculation. Rigor without novelty is competent replication. Relevance without either is consulting. The field has papers that are novel but not rigorous, papers that are rigorous but not novel, and papers that are both but not relevant to any real problem. Sun et al. are saying: you need all three, and the fact that this needs to be said out loud tells you something about the state of publishing.

I see this in industry too. Every enterprise AI vendor claims their platform "transforms" the organization. Most of the time, the transformation is digitization of an existing process with a thin AI layer. The process does not change. The decision rights do not change. The organizational structure does not change. The technology changes, and nothing else does. This is the same pattern as the papers. A new technology label on an old theoretical mechanism is not a contribution, and a new AI label on an old business process is not a transformation.

The practical consequence is that organizations spend billions on technology that promises novelty and delivers improvement. Then they wonder why the ROI never appears. The IS research field has the same problem at a smaller scale. We publish papers that promise invention and deliver improvement. Then we wonder why the IT artifact keeps disappearing from our own research, why Sarker et al. (2019) found that 56 percent of IS papers treat IT as a peripheral variable rather than a theoretically active element.

The Burton-Jones et al. (2021) strategies also include something more radical than reformulation. Envisioning means adopting entirely new ontological assumptions. It means asking not "how can I extend this model?" but "what would a completely different way of seeing this phenomenon look like?" This is where design science research earns its place. Gregor and Hevner (2013) put invention in the quadrant where both the problem and the solution are new. That quadrant is nearly empty in most journal volumes, and I think it is empty not because researchers lack ambition but because the review process is hostile to it. Reviewers evaluate novelty against what they already know. Invention, by definition, does not look like what reviewers already know.

Whetten (1989) offers a final test. He says a theoretical contribution should be evaluated by its scope and its degree. Scope means how broadly the theory applies. Degree means how deeply it explains. The best contributions are either broad in scope or deep in degree, preferably both. A paper that extends TAM to a new context increases scope marginally but does not increase degree at all, because the mechanism is unchanged. A paper that reformulates use as delegation increases degree significantly by identifying new mechanisms, even if the scope is narrower. I know which one I would rather read, and I know which one the field needs more of.

The question is not whether improvement is valuable. It is. The question is whether we are honest about what kind of contribution we are making. Gregor and Hevner's matrix, Burton-Jones et al.'s strategies, and Sun et al.'s triadic standard are all asking researchers to be precise about their contribution type, to match their claims to their actual novelty, and to hold the bar at three requirements, not two. Delegation theory showed that reformulation produces better theory than extension. The rest of the field should take that as a signal, not an exception.