Guest article by Steve Vargo, Christopher Lovelock Career Contributions Award Recipient 2020.

I feel very privileged to be named this year’s recipient of the Christopher Lovelock Career Contributions Award. Even the current pandemic, which precluded the possibility of the normal (and preferable) presentation in the company of friends, could not detract from the honor.

It does not seem that long ago (a little over 20 years) that I was finishing my Ph.D. and beginning to attend Frontiers in Service conferences and witnessing many of my academic “heroes” receiving this award. I was honored to be in the same room with them and never considered the possibility of being on the same award list someday. Afterall, I was just a guy from Oklahoma at the beginning of a mid-life career change, who was trying to “figure some stuff out.” 

Since that time, I have been extremely fortunate, finding that my questions and at least some of my answers were resonating with others, resulting in my research collaboratively developing impact. Consequently, I have had the good fortune of being invited to travel and present my ideas and to make new friends around the world. Recently, I have found myself reflecting on how all of this good fortune came to be. It certainly was not because of a clear vision and well-thought-out plan. 

There are lots of factors, including a great deal of luck. What follows are a few of the things that seem to have contributed. Some I have learned from others; a few I stumbled on myself; others are based on shared insights from colleagues about what has contributed to the success I have enjoyed. I direct these primarily to early-stage scholars, though hopefully, they are useful beyond that target. 

Ask “big,” interesting, theory-focused questions. 

It seems to me (and, I know, many others) that there is an ever-increasing tendency toward micro-level, gap-spotting research and less tendency toward addressing bigger and more-meaningful, theoretical and practical questions. The former seldom leads to impact commensurate with the effort involved but, whereas the latter is sometimes more difficult to fully develop, the marginal effort required is usually much more rewarded, through the associated fun of exploration, sense of contribution, and impact. Early-stage researchers are often pointed away from big questions on the grounds that they are not yet in a position to tackle them. However, I would argue that relatively novice scholars are often more likely to have novel insights than seasoned scholars with an investment in particular models and paradigms.

Look beyond intra- and inter-disciplinary boundaries. 

The late Bob Lusch used to claim “you will never run into a great idea walking down the hall of your own department.” Clearly, he was (intentionally) overstating this claim, though not the general notion. Great insights come from seeing phenomena from different perspectives, but perspectives tend to become homogenized within organizational boundaries, both intra- and inter-disciplinarily ones. 

Of course, service marketing and service management are quite used to looking beyond disciplinary boundaries for theoretical inspiration. Arguably, however, they are less likely to look at the margins, or fringes, of their own disciplines, where new insights are often being developed. 

Ironically, seeing the benefits of this requires looking no further than the service disciplines, which were themselves considered to be marginal not long ago. Since then, at a minimum, they have exerted a significant influence on more mainstream marketing and management. Arguably, but even more significantly, as Bob Lusch and I (and others) have been arguing for the last 20 years, the service disciplines are also contributing to a more robust theoretical framework for understanding the purpose and process of economic activity in general—what we called service-dominant logic—compared to more traditional economic frameworks.

Reconcile perspectives, concepts, and models for parsimony.

Just importing theory from other (sub)disciplines and applying them is insufficient. I have occasionally argued that there are only about seven concepts necessary for understanding any phenomena of interest—e.g., service, marketing, or management (or probably all three). However, each (sub)discipline/research stream has its own perspective and lexicon for addressing them. The outcome is frequently “concept creep,” which often results in cumbersome, confusing, and uncompelling “Frankenstein models.” Perhaps ironically, big questions are best answered by simple, parsimonious solutions – think e=mc2. Reconciling similar concepts to eliminate redundancy will usually lead to more parsimonious models and thus more compelling and useful takeaways. 


Impactful research, almost by definition, often challenges existing models and paradigms. As might be expected, this will frequently be met with resistance. This situation points back to the need for important research questions, not only for theory and practice but also for the researcher. It motivates the perseverance often necessary to see a controversial manuscript through to publication. 

As I have discussed publicly on several occasions, Bob Lusch’s and my 2004 Journal of Marketing article, “Evolving to a new dominant logic of marketing,” which was the formal introduction of service-dominate logic, took five years from submission to publication. It also involved two editors, six reviewers, and four major risky revisions, in addition to a number of years of research and synthesis prior to submission. Consistent with the above, it was a transdisciplinary study that, aided by the review process, arguably provided a rather simple transdisciplinary answer to an important set of questions. It also was the beginning of the journey that has led to this much appreciated award, a journey, which I see as conformation that pursuing big questions, coupled with perseverance, pays off.

Stephen L. Vargo
Professor of Marketing
Shidler College of Business, University of Hawai’i