Ep. 14 - Do Switching Costs Make Markets Less Competitive? With JP Dube, Gunter Hitsch, and Peter Rossi
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Hi, everyone. Happy holidays and welcome to How I Wrote This, where we go behind the scenes to demystify how great marketing papers came to be.

Before we get to that, I want to let you know that Karen and I have planned a little surprise for you in the new year. Two special mini episodes. Both conversations will be between Karen and me talking about what it's like to be a co-editor and how to be a good reviewer. We get lots of questions about these topics at seminars, at conferences, and so we thought it would be nice just to cover them and share this out with all of you. So be sure to look for them in January.

Okay, here's a not-so-random personal fact: my preferred deodorant brand is Old Spice. Now, by itself, that's not so interesting. But you might find it more interesting that I've used the same brand for over 30 years. Basically, since I started using deodorant. Of course, I know other brands exist, but I've never really given them much thought. I like the way Old Spice smells. Trying other brands feels kind of risky.

Sticking with Old Spice means one less shopping decision I need to make. To use more academic speak, you might say I have a high switching cost when it comes to my brand choice for deodorant. All of this was really just a roundabout way to introduce this episode's paper, which looks at switching costs and their implications for competitive pricing.

Switching costs are a form of state dependence, and they have an incredibly long history of study in marketing and economics dating back to at least work in the 1950s and 60s. After documenting their existence in data, a large theoretical literature emerged that examined the implications of switching costs on firms pricing strategies. One of the key questions was, did switching costs lead to higher or lower prices?

The main conclusion was: higher, because they helped to lock in consumers, insulating them from the potentially lower prices that competition might have offered them. At least in theory. Now, Einstein once said, "In theory, theory and practice are the same. In practice, they are not." And so we too might ask if, in practice, that is, empirically, is this actually true?

I'm Brett Gordon, professor of marketing at the Kellogg School of Management at Northwestern University and co-editor of the Journal of Marketing and Research. And today I'm speaking with J.P. Dubé and Gunter Hitsch, both at Chicago Booth and Peter Rossi at UCLA. Their 2009 JMR paper is titled, Do Switching Costs Make Markets Less Competitive? And their answer is no, at least not in the markets they study. First, they estimate a model of demand for consumer goods.

Next, they take the model as given, and then they conduct a series of simulations in a model of dynamic price competition. Their simulation results show that prices can actually be 18% lower in the presence of switching costs compared to no switching costs. That is the opposite of what most of the theory predicted. Let's join the conversation to learn more. Let me ask the three of you to introduce yourselves. Let's have Peter, then JP, then Gunther.

Okay. In order of senility, I guess. Well, yeah, I'm Peter Rossi. Happy to be here. I'm at UCLA in the Anderson School, where I've been here for about 15 years. And obviously, this paper was written when I was on the faculty at what's now called the Booth School of Business at University of Chicago, where JP and Gunther joined and were my colleagues for many years. And

Absolutely fabulous colleagues in general and more specifically in this paper, just absolutely wonderful people to work with and we'll talk more about that. Yeah, sure. Okay, so I'm JP Dubé. I'm at the University of Chicago in the Booth School of Business, as Peter pointed out. I've been there now for 24 years.

And I don't know if we're going to have a chance to get into it, but the process of how the questions in this paper shaped

is really a testament to the multidisciplinary and very collegial atmosphere that we have at Chicago because the original project we're working on is very different from the final paper and how the three of us ended up collaborating on this was also really interesting. So I don't know if that's as interesting as how did you get it published, but where did the idea come from? And it really did evolve and hopefully we'll get into some of that. I hope we do. And finally, Gunther, please.

Gunter Hitsch, I've been at Chicago Booth now for, gosh, it's 23 years.

Long time, yeah. And of course, you know, as both Peter and JP said, you know, we collaborated a lot. It's a great place to start collaborations, to exchange research ideas. The study of switching costs or state dependence more generally, of course, has a long history in marketing economics. So before we get into the actual paper, I wanted to set the stage a little bit. So if one of you could just describe what are switching costs in layman's terms?

Well, I guess, I mean, a canonical example would be, you know, you decide to work on Windows and at some point you get interested in macOS. And, you know, there's, of course, a large cost of

moving your data, learning a new workflow. There's products with explicit switching costs where you sign a contract with your mobile phone provider, right? And if you want to get out before the expiration of the contract, you pay a dollar switching cost. There is something that, and I'm going to use the terminology about Paul Klemperer, who is the most eminent economic theorist who has worked on switching costs. He calls this psychological switching costs. And in marketing, we

give it a much more intuitive word, which is brand loyalty. So you try a product and that creates some kind of habitual buying behavior. Now, the idea is, and that's the premise of the paper, that if consumers have such behavior, that leads to very interesting dynamic strategic pricing incentives by firms.

There's one incentive is to kind of acquire consumers and that's called the investment motive. And then, you know, once consumers are locked in, maybe you want to

other term is harvest to consumers because now they experience a psychological switching cost if they actually substitute it to a different brand. Can I just follow up on the first question you asked about what's the switching cost? I just wanted to add some stuff like Gunter pointed out that the term psychological switching cost is a term that's used in the survey articles by Paul Klemperer on switching costs. But I also want to point out that

Actually, the term came from marketing, and it's actually a form of switching costs that was discussed in marketing, I think, long before the switching costs literature and economics had materialized. The term came from a paper by Agle et al. in 1968, and they referred to the term psychological commitments as opposed to psychological switching costs.

This was in reference to their theory of repeat purchases, habitual brand loyalty using cognitive dissonance theory. And it was an appeal back to psychology from the 50s by Festinger and Brehm. But the term psychological switching cost or psychological commitments was actually coined by marketers in 1968 and then used by Klemperer et al. to try and show that this was an early form of a broader literature.

Thanks for adding that additional context because one thing that struck me immediately when I first was looking at the paper was you really pivot from this theory of literature in economics, Klemper and related authors, and you start the paper by saying the theory of literature concludes that switching costs are going to raise prices anti-competitive and we're going to show that that's not the case necessarily for empirically relevant

switching costs. So it's a very clear positioning, really from the first couple sentences of the paper, which I think is is really helpful and really nice. So how did this project come together? It sounds like it evolved over time. So do you remember? Do you guys remember the genesis of it?

Yeah, I actually do very well. It started as a lunch conversation between Gunther and myself where I was complaining about a referee report. I had two papers in a row with choice models that were on a completely different topic where I was told in no ambiguous terms that the paper would be unpublishable unless you included a lag choice variables. It was well known that lag choice variables are very important things.

for understanding demand and there was no real explanation for why they're important or why this would change the result I was working on. And it was Gunther who said, well, what makes us so sure that the literature is right? Like, why are these these lagged choice variables so important? And the project kind of started out with us trying to debunk this, what we thought at the time might be a myth that this was a critical part of demand.

and trying to think about how to estimate a richer model of demand with better controls for heterogeneity, see if we could knock this thing out of the model entirely. And as Gunter and I explored more and more ways to include heterogeneity, we started chatting with Peter, and Peter said, "Well, the way you're doing this," I won't get into the details, but we were using frequentist approaches, so this is like totally archaic, it's inefficient, "You should take my new PhD class on Bayes

and use a Bayesian approach. And so Gunter and I both signed up for Peter's PhD class as we were working on this, as we started talking about this with Peter, the three of us ended up in a three-way collaboration on this project.

To make a long story short, and I'll let someone else take over from here, after using what I guess I would call at the time state-of-the-art controls for persistent heterogeneity, which was stuff Peter was simultaneously working on with others, using a mixture of normals approach, we actually weren't able to nominate.

this out of the model, which sort of changed our direction a lot. It's like, nope, it looks like even with state of the art, it's still there, which then led, I still remember Gunther asking, well, if this is really a robust part of demand, why has nobody ever actually talked about the marketing implication? And that's where we start to get into the dynamics.

But you can see it started off with referee reports and then ended up with like a result that we couldn't actually get. We couldn't knock out. We thought this would be like it. Go ahead, Peter. Go ahead. You actually got something out of those referee reports. So that's pretty unusual. Yeah.

I don't recall the exact origin, and I think there's various origins. I remember, you know, I took a market, I have an economics PhD, but I took a marketing PhD class when I was a PhD student at Yale University. And I do remember there was one week where we covered, you know, work,

that goes into persistence and persistence in part based on brand choice processes, not just persistence based on, for example, advertising. And, you know, in conversations with this, you know, JP points out with JP and Peter, I think we got into this

So we have now tools to kind of say something about what is actually a causal, potential causal impact of a brand choice today and brand choice tomorrow. And we realized that if you take this seriously and you want to know then how should you price the product, now you've got to solve a dynamic pricing problem. And I'm pretty sure about this. What we did not immediately realize is that now once we think about competition, this goes into this whole switch in cost literature. That is something that we eventually figured out.

So you weren't thinking, you didn't have the tie into the theory literature immediately? Like that wasn't the jumping off point, it sounds like? Not the theory literature that goes into competition, right? Because things are much more clear cut if you have a single firm pricing, essentially under quasi monopoly or oligopolistic pricing conditions. Interesting. And so because you were talking to Peter

Initially about the problem you were working on, he said, take his class. And then I imagine that the three of you just kind of kept on talking organically over lunch and whatnot, kind of thereafter. It's all related, right? So without Peter's work and, you know, there's no way to have a credible empirical foundation for what we did.

So how did you then make progress kind of moving forward? Because one of the things I'm always interested in is, you know, people have ideas, they talk about things, they maybe have some initial rough analysis, some output in. I'm not sure what you, what were you guys coding this? I guess this still would have been R probably. You should distinguish between sort of fitting the demand models and

and then the computations of the dynamic equilibria, which in some cases were driven by the estimates from those models, not all cases. But yes, so there's sort of a separation in there. And obviously, Gunter deserves the great lion's share of the credit for doing these calculations and doing them well.

Sometimes as a co-author, I'm somewhat frustrated by the apparent lack of progress from Gunther, but it's just because he's trying to do it right. And I didn't really appreciate at the time how difficult that computation was, you know, that you don't have all these contraction mappings and all these things that happen in single agent or competitive type models or the social planner type models, which I'd actually computed myself and published in the JP on dynamic taxation, you

you know, years before this project, I didn't realize how much more difficult it was to compute. Even if you put in all these refinements like Markov, perfect equilibrium and so on. And Kunta really deserves credit for that. So how did, how did you actually work together? Like what was the process of managing, how did, how did it move from kind of just rough output, especially in C++ into tables and a paper and a draft?

Well, I would come in the morning and JP is already there and already coded up a whole bunch of stuff and done all kinds of things with incredible infectious energy. So, you know, I kind of had a partitioned area of the of the project in some sense, although really one of the most interesting parts of the paper, I thought, which is this issue about how do you differentiate between switching costs and other possible explanations for this kind of behavior like learning?

And that really actually extends back to when Gunter joined the faculty at his job market paper on new products. And I had many conversations with Gunter about the Bayesian learning model. And of course, I'd studied that by reading DeGroote and so on. And those conversations came back. And then JP was very, very much part of those conversations.

I think also the paper does a remarkably good, interesting discussion of competing explanations and why we think that this explanation sort of survives those comparisons. There isn't really explicit, you know,

testing of alternative explanations in the sense of calibrating those models. But there is a discussion about what would be consistent with this data. What would they show? How could I tell the difference between an environment with state dependence and an environment with learning, for example?

Yeah, no. So I wanted to bring this up because I think it's hard to talk about the JMR paper without talking about the RAND paper. You know, one part of that paper is to delve into the search versus learning versus switching cost kind of possible stories. And what I what I imagined is, is that you started the project in 2005. You said, you know, looking at this broad topic.

And then out of that emerged eventually these two different papers. So actually one question I did have was, I think this is something that a lot of people face, especially when they, when they are getting into a project that turns out to be, you know, meaty is how do you decide what goes where, when should you slice the bologna, how to slice the bologna, because you, you know, you're balancing impact on the one hand, but also something that I've grown to appreciate, which is readability. Like if you have a paper that has, you know,

too many slices of bologna in it, people don't notice at all. - Well, I think that, I think it's the separate, a bigger problem was we had, we found ourselves flapping in the wind. We had our original version of the paper did have everything in one draft,

And you would have one set of people would say the theory was super interesting, but they had a whole bunch of questions about the empirics. In other words, the empirics are interesting, but it wasn't really enough to call it theory. And so we're kind of getting attacked on all ends. And really, the solution was to split it apart, I think grudgingly, because I think we all felt originally that the

single comprehensive paper was just made for a more powerful piece. But as I said, I think it was a lot easier to split it apart. I think the key in the empirical paper was not just testing between those mechanisms, but really reaching a conclusive evidence

that what we were finding was structural state dependence, whatever the mechanism may be, and not just some kind of spuriously correlated omitted variable or omitted source of choice driver. And I think that was a really important part of that, that what became the RAND paper. And then the second paper was, okay, well, if this is really some kind of structural state dependence, and if we really strongly feel it's

this kind of loyalty that looks like a switching cost, what are the marketing implications? And in particular, what are they in an oligopolistic market structure? So I think related to this, there's maybe a somewhat bigger point. That is something that's very much on top of my mind as I'm much, much older and

an editor. And I think at least part of this maybe, you know, is the reason for how we started on, you know, essentially, as JP said, have everything in one paper.

But given the long history in marketing that's trying to, you know, where research is trying to distinguish between structural state dependence, essentially the causal effect of purchase on purchase in future, versus pure state dependence, which is just simply serially correlated unobservable, confounding unobservable. Given that, you know, the existence of the problem was recognized, we thought, well, you know, this is maybe not such a big question. We maybe can't really make so much progress.

But as a matter of fact, the Rand paper is extraordinarily widely cited is because it does a very, very good job. Okay, maybe I shouldn't compliment. I'll credit my offers on a good job. So I don't want to compliment myself, but I think at least it's a very lucid exposition and it tries to look at this problem from every single angle to kind of provide robust evidence. Well,

No, I agree wholeheartedly with Gunther on this. But again, I even see rookies coming and give job talks, and this has been true for many, many years, maybe a little less today, but that people sort of want to say, what's your research agenda? And then they'll put down a matrix and they'll say like, well, we want to fill in missing elements of the matrix or something like that.

and i i think there's way too much strategic behavior on the part of junior faculty and it's sort of saying well how should we divide this up and can i get two publications out of this rather than one or you know can i target different audiences and so on i i think

The better way to look at this is this is what research is supposed to be. You solve the problems you need to solve and then solving those problems, for example, like distinguishing between heterogeneity and state dependence and estimate and using the features of marketing data to credibly estimate the state dependence that that facilitates another research.

avenue, namely, okay, now, as Gunther said, what happens when you have firms with market power competing, and there is this aspect of preferences. So I think people are vastly overinvested in these sort of micro strategies of how they are going to publish their research.

So then I think one of you mentioned that the paper, the project, the paper changed a lot over time. I mean, I guess one way it changed, of course, is it went from kind of one big paper to slightly shorter papers. Was there content that got removed for whatever reason because of the process? No. No.

No. And the reason the paper grew was because our research hypothesis was growing organically. Just to put this in the right context, everybody was, well, reviewers, editors were saying you got to stick in a lag choice variable because it's well known this is important. But if you go back and read the literature Peter referred to earlier, this literature that started in the early 1960s, just testing the order of the choice process,

Most of that literature was totally inconclusive. What we knew in the data from the 1950s onwards, once we started getting panel data from newspapers, was that people had long spells where they repeat purchased the same brand and it was tempting to call that loyalty. But actual attempts to test

loyalty in the sense of some kind of higher order process was completely inconclusive. And then magically in the 80s, in a parametric choice model, if you plugged in a lag choice variable, suddenly it came out really significant. It wasn't really clear why. And I think that's why Gunther and I had this view. If we control properly for heterogeneity, we were skeptical that there really be any residual evidence

for this kind of state dependence, for this kind of carryover and from the choice. And so when we weren't able to knock it out, even with Peter's state-of-the-art semi-parametric approach with mixtures of normals, then the paper pivoted to, well, now what are the implications? And you can see how the paper, the manuscript itself started to grow

Because we had all this material on, can we knock this out? No. Then they're sort of like, well, if we can't knock it out, what is it? And that's like, what's the mechanism? And then now that we have a sense of what we think the mechanism is, what are the marketing implications? And it was only in retrospect, I think, that you could look back and say,

Well, we probably should have left the what are the marketing implications for a separate follow-up paper and really fleshed out the idea that this is structural state dependence first. But, you know, that is what it is. It grew organically, and that's what made the project so much fun. Well, I want to switch to the review process. Where did you send it first?

I guess Econometrica. This is the full paper before it was split. Ah, so you did send the full paper somewhere else first. And I guess the feedback from that led you to split the paper?

In fact, I may be mistaken on this. Peter and Gunther, you can remind me if I'm mistaken. But it might have been at one of those general interest journals in economics that even the editor said you might consider splitting the papers, which led to that long, complicated discussion we had about whether we should. I don't recall when we made that decision to split it. But it sounds like maybe one of the main...

outcomes from that process simply was that you did end up splitting the paper yeah but i think the main pushback wasn't actually hey you know like it's not quite clear what the source of switching cost is it was a different point and the point was that the result that you have is already known in the literature oh so that's a much more subtle kind of that was at marketing science

Sorry? I was at Marketing Science. I don't recall, but I mean, you may be, maybe I'm misremembering. I don't recall the economics journals saying that this was a well-known result. I think what they didn't like was the empirical example said this isn't a switching cost. We got a little bit of echo from the NBER that if we had, I remember the econometrica, the editor saying it's too bad we don't have it.

on operating systems. I think if we'd done an empirical case study, was Windows... Yeah, of course. But if we did, I think if we could magically have those data, I think we would have had a success. No, but the data doesn't exist because they vary. Of course. To identify the model doesn't exist. Sure.

Sure, sure. But I'm just saying, I think it was marketing journals where they said this result is well known. And sorry, I interrupted you. I'll let you continue because the context in which it was well known was somewhat silly. Yeah, so I confess, I mean, I don't remember in detail the exact feedback. I do know that this was a completely separate criticism, right? By people who said, yeah, sure, there's a switching cost. However, your result that you say, you know, is...

It's kind of adds to the literature started by, or at least the literature is just one of the main contributors to the literature where we said, this is something that adds to this literature, right? And there's a

Some people said, well, we already know all of that, right? There's nothing new. I think there was another thing that's involved here, and I've gotten more of this in my career, is at that time, there was a fairly large fraction of the economics community. And you have to remember that the I.O. at that time was not considered particularly distinguished economics studies.

discipline. In fact, my friends who had the Nobel Prizes in macro and other things would say, well, Iowa's kind of a silly field. It's kind of like development economics was for lightweights. Of course, that's changed. But so there was a lot of hostility to computational economics, where that is to say, using a computer instead of a pencil to solve problems

And that's exactly what we did, and primarily Gunther did this, right, was to calculate these. You couldn't possibly even imagine calculating, being able to derive any sort of pure theoretical results with these kinds of specifications, which allows you, and there was a lot of hostility to that.

at that time. I think that's gone away to a very large degree now that people recognize that for any serious model, computational economics is really important and is the only way to really make progress in some of these situations. So there was also that in the background. I don't know how much of it leaked over to this particular problem that we experienced

But it was a somewhat discouraging process, right? Because we really had something to say to this broader economics community.

And really more about what happens when firms compete, right? When there exists non-trivial switching costs, right? And that should have been printed in top economics journal. There's no question about it. Now, in the end, maybe it didn't matter because it does get cited a lot. But frankly, publishing something that

that you want to speak to the economic community in jmr is like you know wrapping it in a blanket putting it in a safe and dumping it in the ocean because no one in economics reads jmr now we might be the only article in jmr that people right you know and it's true also to some extent of marketing science right it's not so much true of cumi but so in some ways the outcome was

In terms of placement, it's sort of the opposite, right? In some sense, in the end, it's sort of, you know, that's not the game that we're in. The game that we're in is impact.

So you went to Marketing Science next with the paper. My understanding is that it got a reject and resubmit. And to say that you were a little disappointed in the reaction was maybe a little understatement. I'm wondering what you took from that reaction to the paper. And I'm sharing over chat something that Peter put in an email when we were chatting about the whole experience. So I thought that this was a really important point. Yeah, Marketing Science was the journal where they said,

the computational result you have, the one that says, contrary to a large extent literature on switching costs, that large switching costs don't necessarily soften price competition. We showed that prices can actually go down in the presence of a larger versus a smaller switching cost, all else equal. And marketing science, one of the AE said, this is obvious, it's well-known, which is odd because this is, again, it went in stark contrast with all of the published theory literature on the topic.

And the arguments that I think maybe this is the wrong venue to get into the weeds on why they thought it was obvious was silly. But, you know, as per Peter's email, our decision was, well, we're not going to wreck the paper or try and appease to somebody who's going to say something like that. And we just submitted it elsewhere. Yeah.

Yeah. So, I mean, so what I mean, just to follow up on JP, because I think he's absolutely right, which is so what would a lot of people do, particularly more junior people? They might say, OK, well,

I really need to get this published in marketing science. So what I'm going to do then is weaken the paper and sort of say, well, we're doing some refinements on a known result in a two period model or something like that. And that would really be doing damage to the to the long run.

Not just damage to your own. So there's a sense in which societal and private incentives are aligned here, right? It is not societally optimal for people to weaken their papers so you can't understand the contribution of the paper or to include a lot of irrelevant garbage to appease an associate editor. That's against the interest not only of the authors, but also of the profession.

Yeah, I'll just throw in on that, that I mean, I've had papers that were offered revisions, but the conditions for the revision seemed they were going to require me to do things I thought were wrong or completely off topic. And I've had more than one occasion where I've just withdrawn my paper and sent it elsewhere in spite of the review, the revision request. And I think that this is again, back to the audience of young authors who are trying to figure out how to handle the review process and

you can save yourself a lot of time as well by not trying to fight with a hostile team that doesn't understand or appreciate your work. And furthermore, this might be a better solution than trying to wreck your paper. I think fortunately, although good news for young scholars is that I think their review process has, I believe, improved. And I think these days editors, you know, and have more of the mindset. So back then the mindset was,

I, the editor, I'm always right. The reviewers are always right. And what do the authors know? And I think this has become better where editors know, well, you know, it's unclear. Reviewers make mistakes.

Of course, all the time, right? And you give the offers a chance to properly respond and get their side of this. And I think it just should be said that I think Peter deserves a lot of credit for this, the creation of QME, because it created competition by providing a very smooth review process. And I think it did. I obviously don't have any hard evidence for this, but my intuition and experience says that it made sense

other journals improve their review processes because they had, they did hear about how it was a better experience for the authors. And let me, let me wrap it up with this last question. Now that you're all 20 plus odd years, you know, in the field, if you could go back and give yourself kind of one piece of advice as a, maybe it's like a senior PhD student or as a junior faculty,

about the process of doing research? Of course, writing great papers is easy advice, but what would it be in terms of kind of how to do research? What advice would you give?

Well, I don't know if this is how to do research, but one thing that I would attribute to probably one of the hardest things I did when I was an assistant professor was actually going and talking to someone like Peter. When I joined the University of Chicago, I found Peter terrifying. Peter would sit in seminars and after a few minutes would understand presenters' papers much better than they did.

and then would point out to them what was wrong with their papers. And I just, I was terrified. I think one of the best things I ever did was to just deal with that, that intimidation and show Peter some of my work. And some of it, Peter gave, it was very complimentary. Other parts of my work, he was, would give some pretty severe criticism, but justifiable. And what I realized over time was that I learned more from Peter than I ever did from presenting a paper at any single seminar.

And it came to the point where before I would take any project of mine on the road for presentations, I would always talk to Peter first. And no matter how harsh the feedback was, the papers got better. And that's how I ended up being really grateful to be able to work with Peter and write papers with him.

because I learned so much. And I think one of the challenges for a lot of junior authors is you'd prefer to work with people who don't intimidate you, but then the result is they don't really bring anything to the table for you either. I mean, it's nice to work with co-authors you're friendly with, but the most important thing professionally is that you learn something from them. And so get over your fear, take the risk, expose your work to people who know more than you do, and the result is your work will get better. Yeah, I second that advice.

I do remember my job talk, and it had nothing to do with the paper we're talking about today. And so there were certain things, important things in my paper that I didn't fully understand. I knew I didn't understand them. And there was one person on the job market who was...

sniffing that out and it was Professor Peter Rossi, you know, so having said that, yeah, maybe Peter was a little bit terrifying, but I realized being at the place where I can talk to somebody like this, this is, you know, I valued that.

Look, we took Peter's PhD class. I think that if any, I was, I was tenured already and we took this PhD class together. That should tell you something. I mean, I'm not sure how many junior faculty take the PhD class of their senior faculty. I'm sure it happens, but still, I think a testament to what we stood to gain. Well, thank you guys. But, but I would say on the answer to Brett's question, which is you got to have your confidence in yourself, right?

Right. You've got to do what you are excited about and you need to find a home for that, whether that mean literally in terms of the papers or literally in terms of yourself. Don't try. I don't know how much advice I received when I was a junior faculty. I received countless advice. Your work is too theoretical. Your work is too applied. You should do more theory. You know, I mean, I literally would get that in the same week.

from two different people, you know, or that paper, that, that paper is, is really, you know, that, that's not really interesting. The value of information, you know, like why would anyone be interested in that? Right. You know, that kind of stuff. And I got that from editors. I got that from, from senior people in the field, leading lights at the time, you know, all this Bayesian stuff, it's all nonsense. It's worthless. It doesn't work.

So you've got to stick to your guns. You've got to stick to what you like doing, right? Because ultimately, it's not about getting tender. That's not the goal. The goal is to have a productive, impactful career, right? And the only way to do that is to enjoy what you're doing. If you don't enjoy it,

then it's just going to be a job. It's going to be, you know, you might as well go work for, you know, for, for, uh, you know, Google or something like that. You know, I mean, you know, really, I mean, you know, even though there are good researchers at Google, I, you know what I meant, where you have a bunch of short run projects that have to be turned over and all that sort of stuff. And you can't really spend the time that you'd like. So, I mean, since we had this incredibly luxurious lifestyle and luxurious, uh,

opportunity to work on what we want, then you should really do it. And find a home, right? You'll find a home for this stuff. If you're enthusiastic about it and you've got good skills, you know, you're going to be a success. But don't try to sort of strategically say, oh, I got to work on this topic.

I got to work on, it was machine learning for a while. Now it's AI, right? Now AI will change the way firms interact. So I have no problem with people working on algorithmic pricing or something like that. I think that's really fascinating stuff. But if you're not interested in that and you're interested in something else of relevance to marketing, then pursue those. Don't try to reinvent yourself in that sense. Pursue your enthusiasms.

Well, on that note, thank you so much, Peter, Gunter and JP for joining me today on how I wrote this. Thank you, Brent, for having us. It's really good to hear the story here, of course. Thank you so much, guys. That was JP Dubé, Gunter Hitch and Peter Rossi talking about their paper, Do Switching Costs Make Markets Less Competitive? Published in JMR in 2009. Don't forget, follow us in your favorite podcast app to make sure you get the latest episodes delivered right to you.

This episode was produced by me, Brett Gordon. And if you like the way we sound and the music, you should thank our producer, Andrew Merriweather. If you have any ideas you want to share, please drop us a line. It's easy to find our emails online. And just to remind you again, in the near, we'll have two special mini episodes for you talking about what it's like to be a co-editor and on being a reviewer. We hope you'll tune in for those. Until then, thanks for listening.