ACR Presidential Address 2011

What’s New?  Novelty in Consumer Research

Sharon Shavitt

Walter H. Stellner Professor of Marketing, University of Illinois

This is a slightly expanded version of the address given in St. Louis, October 14, 2011

I want to talk about your next paper. The next piece of work you will submit for review.  In this talk, I will address one of the most important criteria that will determine whether it is accepted or rejected. Surprisingly, it’s the least understood criterion. Everyone will judge your work on it, but no one quantifies or defines it.

I’m going to talk about novelty in research. How we assess it. Why we seek it. And what are the consequences.

The topic for this talk was inspired by a review of one of my old manuscripts. Perhaps you have a review just like it – the kind that haunts you long after the paper is published. Years ago, my student and I submitted such a paper to one of our top journals. It addressed how attitudes can shift when people anticipate a group discussion. We got good feedback, but one reviewer complained that the paper lacked novelty:  “The additional contribution seems marginal. We already know that reference groups influence judgments.”

That review changed my view of our field. It was accurate – we do know that reference groups influence judgments. But does that mean we’re finished with this entire domain? When is a topic spent? How do we decide if something has already been done, or if it’s novel? I couldn’t stop asking myself these questions.

The view of novelty in that review reminds me of the New Yorker cartoon where one caveman says to the other, “Og discovered fire, and Thorak invented the wheel. There’s nothing left for us.”

It’s easy to get the feeling that it’s all been done. We could have stopped with Og and Thorak. Yet, people have found ways to keep innovating.  We have novelty, but we don’t always recognize it.

In this address, I will describe the subjective ways we assess novelty. I will discuss our deeper motivations for seeking it. And I will propose that if we worried less about pursuing what’s new, we could enhance innovation in our field.

Who Cares About Novelty?

We all do. We are all judged on it. We all try to claim it for our research. Making a convincing claim is getting harder as the field rapidly grows. But it’s urgent for junior scholars. They need to carve out their niche while the tenure clock is ticking. There is a lot on the line.

For us older scholars, novelty is also important. It’s a way of ensuring we have made a mark. Our life’s work has mattered because we did something new.

Why is novelty so important to these goals?  Because, in the academic world, novelty is status. It’s the Gucci, Vuitton, and Lamborghini of research -- all rolled into one. Novelty compensates for other flaws (Rozin, 2009), like Botox, smoothing out the wrinkles in our studies. Novelty assures our findings will get attention and admiring glances. If we’re lucky, maybe publication in JSSR -- the Journal of Short Sexy Results. Who wouldn’t want that?

Journals want novelty, too. Want it and demand it. Each editorial we read tells us to send in only our most novel work.  One marketing journal’s website insists that,

"All submissions must be interesting,..."  "...The editors...especially encourage research that is novel, visionary or pathbreaking." 

Clearly, the bar is high for judging the novelty of your next paper.

What’s New?  Defining Novelty 

Novelty can come in various forms. So, when you ask people, “what is novelty in research?” they will say: It is a new area, a new idea, a new finding or method. That is fine, but it still leaves the question – what’s “new?”

The subject of novelty has been addressed in the sociology of science. Robert Merton (1973 [1942]) and others described how scientists get credit for original discoveries, and the rewards that follow from that (see Guetkow, Lamont, & Mallard, 2004, for a review). This classic work dealt with a number of issues, except what novelty actually is. What is the threshold for calling something “novel?”

There really is no authoritative work on that. The word “novel” is used – a lot— but always as if the concept is self-evident. As if everyone who looked at a piece of research would judge its novelty the same way.

The difficulty in defining novelty is immediately apparent to those who try. C.W. Park (2011), editor of the Journal of Consumer Psychology, offered helpful guidelines on submitting novel work to JCP. He acknowledged that judging novelty,

“involves a high degree of subjectivity… The bottom line is that [novel papers] …cause readers to slap their forehead, exclaiming ‘Silly me, …why didn’t I observe this?’ ”  

I think this statement may be as good as it gets in defining novelty. It recognizes that novelty in research confers status and elicits envy.

When you submit your next paper, you may be told that it does not seem new, or that enough has been done on your topic. That kind of feedback can feel quite discouraging, especially if you are a young scholar eager to establish yourself. Fear not. You are in good company:

“For my annual review in 1974, the department head suggested that I move away from pricing research as I had done about all that could be done in this area.”

This is Kent Monroe (2008, p. 16) speaking when he was named ACR Fellow for decades of pioneering work on pricing. I mention this quote for two reasons. One is to reassure you that the best have faced this criticism. Another is to support the plausibility of three points I want to make about novelty.  

(1) Novelty is not an intrinsic attribute (of a theory, a finding, or anything else).  

-An assessment of novelty is a mental construction.

-It draws from feelings and subjective experiences.

-And it is sensitive to context. How we judge it depends on where we’re standing.

We don’t have to look far to see what kinds of factors can impact judgments of novelty. We can just look at the research we conduct or cite: Research on fluency and metacognition, on thinking styles, and values. In fact,

(2) The way we seek novelty in research is tied to our core values.

Because values are not universal, neither is the way we understand novelty, as we’ll see. And my final point:

(3) Pursuing novelty in research has unintended consequences.

Of course, we need novelty if we hope to push the boundaries of knowledge. At the same time, any criterion applied reflexively is bound to cause trouble. I will offer some reasons to loosen up when it comes to judging the novelty of each other’s work.

How Do We Assess Novelty?

Let’s consider my first point: Novelty is a mental construction. I think that something is perceived to be novel when it,

- feels unfamiliar and surprising and

- does not appear subsumed by existing categories.

Seen-Before Judgments

For research to seem novel, it has to be experienced as unfamiliar – as something we haven’t seen or learned before.   

As John Lynch (1998) noted in an earlier presidential address, reviewers will often assert that a finding is already well known without providing references to back it up. In principle, if you already know something you should be able to say where you saw it. In practice, it’s not so easy.

In fact, entire paradigms in psychology have been based on the fact that people are not good at judging whether they have seen or experienced something before.  Consider mere exposure effects (e.g., Zajonc, 1968; Bornstein, 1989), false-fame effects (e.g., Jacoby, Kelley, Brown, and Jasechko, 1989; Jacoby, Woloshyn, & Kelley 1989), and various false memory paradigms (e.g., Koriat, Goldsmith, & Pensky, 2000; Lakshmanan & Krishnan, 2009; Rajagopal & Montgomery, 2011). Conscious recollection of past exposures is not at all accurate. This is why people can confuse fluency from an irrelevant source with familiarity. 

In consumer research, as well, studies show that when something feels easy to process or when an experience evokes imagery, it creates a false sense of familiarity. People think they’ve already been there, done that – when they haven’t, and didn’t (see Rajagopal & Montgomery, 2011; also Lakshmanan & Krishnan, 2009; Mehta, Hoegg, and Chakravarti, 2011; Schlosser, 2006).  

It’s hard for people to remember every piece of research they’ve ever seen. This is especially so with increasing online exposure to science blogs, TED talks, journal feeds, etc. (see Lutz, 2011). Many assessments of novelty are probably not based on exact recall of past work. They reflect a vague sense of whether a topic feels saturated. So, if something about your next paper feels too fluent, instead of taxing their memory, people may assume it’s all been done.  

Feelings of Surprise

For research findings to be experienced as novel, they also need to feel somewhat surprising.  But here too, as some have observed, our feelings can be misleading (Lynch, 1998; Lilienfeld, 2011).   

One can fall prey to the hindsight bias – the feeling that one "knew it all along” (Fischhoff, 1975; Wood, 1978).  People who know an outcome tend to overestimate its likelihood. This is one reason that surveys show the general public tends to dismiss behavioral research (Lilienfeld, 2011). It feels like common sense.

The hindsight bias has been demonstrated many times, in many populations (Bernstein et al., 2011; Pohl, Bender, & Lachmann, 2002) and domains (see Bernstein et al., 2011, for a review). Could it also affect an expert’s view of whether a research finding is surprising?

Sure. As just one example, Lily Wong (1995) in educational psychology showed people lists of findings about teaching that were either actual well-replicated findings, or their opposites. When asked to select which were the real findings about teaching, experienced teachers were no more accurate than novices – which is to say, not accurate at all. And both groups tended to rate their selected findings as obvious.

If reviewers dismiss the novelty of your next paper, saying, “it’s not surprising,” how much weight should we put on such feelings? Once people know your findings, they can feel obvious in an illusory way – even to experts (Wong, 1995; see also Arkes et al., 1981; Knoll, 2010).

Construal Level and Novelty Categorization   

To assess whether findings are novel, we also need to consider mental representations of “what everyone already knows” (Kaufer & Geisler, 1989), and decide whether the findings can be subsumed by those categories. Recent work by psychologist Jens Förster suggests that perceived novelty is a by-product of this sort of process (Förster, Liberman, & Shapira, 2009; Förster, Marguc, & Gillebaart, 2010). Events are experienced as novel when they don’t seem to fit existing categories.

But this, too, is a matter of perspective.

To understand the experience of novelty, Förster and his colleagues build on a theory that has inspired a great deal of consumer research, Construal Level Theory (e.g., Trope & Liberman, 2003). They emphasize that anything can be experienced as either novel or old:  Any new town we visit could be seen as “just another city;” any new person we meet could be “just another person” (Förster, et al., 2009, 2010).  

Whether we define something as “new” depends on how broad or abstract is the category we call “old.” And that has to do with our psychological distance from it.

Distance from something leads to the use of broader categories to represent it. This makes it easy to subsume new things, making them feel old and familiar. Innovation becomes harder to appreciate.

So it is in consumer research. If someone isn’t close to the subject, they tend to classify knowledge at an abstract level. They might say: We already know that consumers link possessions to the self. Or: We know that messages are more persuasive when they match one’s motives. These broad categories subsume a lot of the work in our field, and probably a lot of future work, too.  

As a result, if you want to increase the chance that your next paper will be seen as novel, some will tell you to go and explore a whole new area, apart from what others have done.¹  

Still, as we’ve seen, novelty is in the eye of the beholder. It’s a mental construction. And the size of the bins we use to classify existing knowledge is arbitrary. We don’t have to insist on novelty at the “never-been-done” level.

So, why do we?

Why Do We Seek Novelty?

To answer this question, let’s consider a finding in the sociology of science. A few years ago, Michele Lamont and a team of colleagues, supported by the National Science Foundation, set out to examine how scholars perceive originality (Guetzkow, Lamont, & Mallard, 2004). They were looking for variations between disciplines. So, they interviewed panelists for American fellowship competitions in social sciences and humanities. As it turns out, the most interesting thing they found isn’t what differed between disciplines, but what was the same. Across disciplines, from art history to sociology, reviewers saw the originality or novelty of a proposal as a sign of the applicant’s moral character.

People who submitted proposals seen as novel were described as courageous, independent, intellectually honest, and “thinking for themselves.” They were praised and respected as authentic scholars with high integrity.

To be independent and courageous demonstrates that one is pursuing one’s own authentic interests. Reviewers deeply valued these qualities and wanted to reward them (for similar perspectives, see King, 2010; Zaltman, LeMasters, & Heffring, 1985).

On the other hand, applicants whose work was seen as lacking in novelty were viewed as morally deficient. Reviewers scorned them as conformist, derivative, lazy, traditional, and “riding the bandwagon.” These were not scholars who had genuine intellectual passion. 

So, novelty judgments – subjective as they are – were more than an assessment of someone’s ideas. They were an assessment of the person, as well.

I was fascinated by this, and wondered, why the moral meaning of novelty? Then it hit me: There is a direct line between this novelty ideal and Western values. To be admired in Western individualist societies you have to be independent, authentic, honest, and nonconforming (e.g., Markus & Kitayama, 1991; Triandis, 1995). You’ve got to act on your passions and pursue your own unique interests. This is the perfect model of an authentic, independent, path-breaking scholar. In other words, this is where the values of our science map onto the values of our culture.

Defining novelty as “independent and different” is ingrained in our value system. We don’t question it. It’s assumed that you should blaze a separate intellectual trail. A trail that sets you apart.

For those of us who are Western individualists, this model of novelty is a perfect fit. We expect the same from ideas as we do from people: to be unique and independent. We are socialized to meet these expectations. As Ashok Lalwani and I have found in our research, individualists really do strive to present themselves in these terms (Lalwani, Shavitt, & Johnson, 2006; Lalwani & Shavitt, 2009).

What’s more, as Richard Nisbett and many others have shown, Westerners tend to think in ways that sharpen differences. They separate and distinguish things, disconnecting things from their context, choosing one side or the other (e.g., Nisbett, et al. 2001; Nisbett, 2003; Oyserman & Lee, 2008; see Koo & Shavitt, 2011, for a review). This analytic thinking style is perfectly suited to the task of differentiating oneself, and one’s ideas, from others (see MacInnis, 2011).

Consequences of Novelty Seeking

Looking at novelty through the lens of cultural values suggests some consequences, and in the last part of my talk I’d like to address them.

Novel = Different?

Our standard for novelty is about setting yourself apart. But reflecting on the values that drive our novelty standards helps us to evaluate those standards. If they reflect a cultural ideal, is it the only ideal we should pursue?

I don’t think so. Consumer research is globalizing fast. New scholars around the world are ready to contribute. Many are based in non-Western cultures that are collectivistic. In their day-to-day lives, being called “unique” and “independent” is not a compliment. Conformity and interdependence are more valued (Markus & Kitayama, 1991; Kim & Markus, 1999). Relationships are valued (Triandis, 1995).

In these societies, people are socialized to think in ways that connect and integrate, putting things together instead of pulling them apart, seeking resolution instead of choosing sides (Nisbett, et al., 2001; Nisbett, 2003; Oyserman & Lee, 2008). This holistic thinking style helps one to see relationships and to integrate things into a bigger picture. And this is not only a cultural pattern – individuals also differ in the values and thinking styles they tend to adopt (Choi, Koo, & Choi, 2007).

What does this mean for consumer research? There is no doubt that scholars around the world can meet the same standards for novelty. But imposing one standard at the expense of others is a mistake. We miss opportunities to leverage relational values and skills. Relational skills help us to represent connections between ideas.  

Indeed, as Debbie MacInnis (2011) points out in a recent essay, our thinking skills foster specific types of novel contributions. Analytic thinking skills foster typologies that highlight differences. It’s no surprise, then, that MacInnis’s analysis of our field’s conceptual papers over the last 25 years reveals a clear emphasis on differentiation. Integration papers are rare.

Yet, those are valuable innovations. McGill, Peracchio, and Luce (2011) point out in their editorial that, from a historical standpoint, the most important breakthroughs in science have been integrations. They innovate by unifying – highlighting parallels across areas, resolving contradictions, and enhancing understanding. Classic examples include Petty & Cacioppo’s (1986) Elaboration Likelihood Model, which unified distinct routes to persuasion under a common set of processing assumptions. In a current example, Press and Arnould (2011) show that identification with a firm happens in a parallel way for consumers as for employees. These are valuable innovations. We need more integration.

To get there, we need to broaden our view of novelty. We should encourage authors who have a relational view of the field, wherever they come from, to find novel connections, or to build new integrative frameworks (e.g., Deighton, et al., 2010).  If your next paper does these things, we should reward that.

Fragmentation

When we mainly reward the kind of novelty that sets us apart, we don’t foster integration. Instead, this fragments the field.

Consider our incentives. We reward novelty at the paper level. So, papers get published on the basis of their difference from other work, not their connection to it. Many have raised concerns about what this does to the literature (e.g., Guetzkow, et al., 2004; Hubbard & Lindsay, 2002; Wyer & Shavitt, 2005).

These incentives for novelty affect what we study. Authors are encouraged to publish one paper on a topic and then go on to something different under the assumption that follow-ups will not be published. 

These incentives also impact how we write. To be seen as novel, we have to apply new labels. So, we try to “name it and claim it” or “RE-name it and claim it.” This doesn’t foster connection, either.

Incentives for novelty even encourage us to position our own articles as having little to do with one another, instead of building on each other. It becomes harder than it should be to grasp the big picture in the field because authors are reluctant to connect the dots.

Where’s the Theory?

Finally, our novelty incentives can get in the way of original theory building (Wyer & Shavitt, 2005). The shortage of original theories within our field has been widely recognized (see Frazier, 2011; MacInnis, 2004, 2011; Yadav, 2010). Yet, few theories that have a broad impact can be delivered in one paper. Building and testing a theory takes multiple papers reporting a program of research that shows generality, boundaries, and convergence around a core insight.

Authors who try may be told, “this is not novel because it is derivable from past work.” But testing an extension of a theory is, by definition, derivable from past work. 

What if we changed our incentives, and worried less about whether every paper is different? We would have the scope needed to build and test our own theories. And I think we would do it. In other words, we could greatly enhance originality at the macro level by relaxing the novelty constraint at the paper level.

Reviewers – all of us – play a key role in this. So do editors and other gatekeepers. Some have signaled openness to different types of novelty (e.g., Deighton, et al., 2010; Erdem, 2010), but it would help to be more explicit, to tell reviewers: Don’t just ask, is it new? Ask, what’s the connection? Encourage authors to link their findings to past work, don’t penalize them for it. Seek contributions that integrate and connect. Reward systematic extensions that establish new theories in our field. 

Conclusions

In summary, let us approach assessments of novelty with caution. They are mental constructions, influenced by the same factors we study: fluency, hindsight, level of construal. And the way we seek novelty reflects deeply held core values.

This means that we can acknowledge the value of novelty in research without imposing one criterion uniformly (Alba, 2012). We need more than one kind of novelty – things that differentiate and things that integrate. It would make our literature more coherent and enable originality in theory building.  

Our theme at ACR this year is “Building Connections.” In fact, this is a frequent theme for ACR conferences, along with bridges and confluence. We seem to yearn for a more integrated field. Let’s consider whether our expectations for novelty are getting in the way. We can build more connections when we’re less focused on setting ourselves apart.

Coda

In closing, I want to offer an invitation and some thanks. First, I invite you to a Roundtable Session right after this luncheon. In it, we discuss recommendations by an ACR Task force appointed this year to plan for the growth and globalization of our field. This task force, chaired by Joel Huber and Don Lehmann, made several recommendations to enhance the field as it expands, including suggestions for new and existing publication outlets and conference structures. The task force charge and report can be read, and your input provided, on the ACR website at www.acrwebsite.org/ .

Finally, I want to thank several people. First, I am grateful to the present and past officers and board members of ACR, for creating and nurturing such a stimulating association.

Next, thank you to my friends who gave me such generous and helpful input. And to my students who helped with details. I am so grateful.

Last but not least, thank you to my family for all of their patience and encouragement. My parents, for believing in me always.  My husband, Steve, who has been supportive and helpful beyond words. And my daughters, who found their own ways to cope with me being too busy: Arielle who worked alongside me on her homework so that we kept each other company, and Ellie who cheerfully repaid me by sneaking onto my computer to type nonsense words into this talk. I hope I found them all.

Thank you.

Endnotes 

¹This talk focused on novelty as defined in terms of unexplored topics or areas. Although I did not have time to address it, another important type of novelty is represented by findings that challenge existing beliefs in established areas. In some scientific disciplines, publication incentives reward this type of novelty, emphasizing results that question established ideas or reverse accepted findings. Jonah Lehrer (2010) analyzed the cumulative impact of these novelty-seeking publication incentives in several scientific fields. His review shows how these incentives give rise to oscillations in the accepted knowledge base. In short, pursuing this type of novelty can also produce unintended consequences that impact the reliability and credibility of scientific knowledge.

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