In with the old,out with the new! The more we keep pushing for theoretical novelty,the less informative entrepreneurship theory will become

Which entrepreneurship scholar garners most respect? The scholar who tests theories most likely to be true, or the scholar who tests theories deemed most interesting? I started my research career under the admittedly naïve assumption of entering a profession in which the former applies, or at least a healthy balance would be present. A decade later however, it seems to me that, also in entrepreneurship, “[t]hose who carefully and exhaustively verify trivial theories are soon forgotten; whereas those who cursorily and expediently verify interesting theories are long remembered.” (Davis, 1971, p. 309). Indeed, a recent editorial in the flagship journal of my own sub-field explicitly instructs authors to “improve our understanding of theory as a tool (e.g. ‘Hey, this is a new insight or explanation’) and not simply reaffirm an existing theory's utility (e.g. ‘Hey, it works here too’)” (Neubaum and Micelotta, 2021, p. 243). Hence, new thoughts are everything, while addressing the robustness of existing thoughts will not get you published, and therefore essentially is a waste of time.

Sure, a field that does not move forward loses its legitimacy, which makes theoretical advancement over time necessary for all of us to justifiably keep studying entrepreneurship phenomena (Wiklund, Wright and Zahra, 2019). Additionally, like other business and management fields, entrepreneurship covers phenomena across levels of analysis, and thereby carries an inherent need for theoretical plurality and sophistication (cf. Aguinis and Gabriel, 2021). Should theoretical advancement however really be achieved in every project, or rather be the outcome of a collective effort of rigorously scrutinizing existing theory before adding additional complexity? The expectation for each study to offer new insights or explanations strongly implies the former. Specifically, it builds on the assumption that there is a seemingly infinite amount of ways in which the social world is much more (predictably!) complex than we currently believe. While I would gladly challenge this assertion on a philosophical level, ¹ it might be more useful to address its (quite predicable) long-term practical consequences, as the constant push towards the new and away from the old distracts us from doing research that may actually lead to a more reliable and ultimately useful knowledge base. I will therefore make a case for a paradoxical prophecy: The more we keep pushing for theoretical novelty, the less informative entrepreneurship theory will become.

The figure above visualizes my concern in reference to the “standing on the shoulders of giants” metaphor often used to highlight the cumulative nature of scientific progress. The left human pyramid symbolizes a healthy process of knowledge accumulation and theory advancement, where further theoretical extensions are added once sufficient confidence has been established in the robustness of the prior research findings built upon. Such confidence is created through replications of potentially theory-shifting findings in different contexts, by using complementary forms of evidence (cf. Munafò and Smith, 2018), or by verifying the causal structure of often merely correlational initial findings using (quasi/natural-) experimental study designs. A research field developing like this is resistant to false positives, as these are likely to be ‘self-corrected’ over time (Ioannidis, 2012), and even to occasional retractions, as each layer of theoretical advancement builds upon multiple pillars of evidence. As an apparent downside, theory advancement is relatively slow because many efforts will go into re-testing ‘already supported theories’ and can – assuming a fixed collective research capacity – therefore not be allocated to developing and empirically testing new theoretical propositions. Additionally, many such ‘already supported theories’ will not be supported across replications, and may therefore not be constituted on robust enough evidence to build more advanced theoretical extensions upon.

The right pyramid is closer to my ‘lived experience’ as an early-career academic. Expectations for theoretical novelty seem to drive researchers towards erecting new layers of theoretical complexity before the cement of the prior work departed from has even had time to dry. As the apparent upside, theory advancement is fast, as we are quick to address new predictions, and therefore can regularly share exciting findings with each other, and with non-academic stakeholders. However, what superficially appears to be a knowledge pyramid rapidly and regularly reaching new heights, in reality will, if we are not careful, evolve with near certainty into a house of cards of increasingly large proportions. ² What may keep this house upright for the time being primarily seems to be the lack of incentives for and willingness towards ³ figuring out what happens when the strength of its foundations is put to real empirical scrutiny (cf. Ioannidis, 2012; Ryan and Tipu, 2022).

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Figure 1.

Whose shoulders would you rather stand on?

I often wonder what would happen if we were to commission independent research teams to try and replicate the 50 or 100 most cited empirical studies in entrepreneurship, or, perhaps even more insightful, multiple independent replications of the 10 or 20 most cited studies in entrepreneurship. Utopian? Not really: such large-scale initiatives have delivered sobering insights into the true reliability of individual research findings in disciplines like psychology, where independent scholars failed to replicate significant findings in more than half of 100 studies in three leading psychology journals (Open Science Collaboration, 2015), and the broader social sciences, where at least a third of 21 highly-influential social science experiments published in Nature and Science failed to replicate and were found to likely contain inflated effect sizes (Camerer, Dreber, Holzmeister et al., 2018).

Extrapolating these replicability statistics to entrepreneurship research ⁴ demonstrates how accepting only a few initial findings as convincing enough cumulative evidence to ‘move a debate forward’ is a recipe for disaster. And its magnitude increases the longer we keep complicating our theories without really scrutinizing the robustness of the foundations we build them on. If we consider a theory development process consisting of a baseline theoretical argument tested once, and a string of sequential theoretical extensions each also building on a single preceding study with significant findings, at a replication rate of ∼50% (cf. the psychology initiative) already at the first extension of the baseline argument chances of none of the relied-upon studies constituting non-replicable evidence are only 25 percent, while after the fourth extension these chances are only 3 (!) percent. Although of course stylized, this simple thought exercise illustrates my point: the more we push (or are pushed) for theoretical novelty at the expense of scrutinizing the replicability and generalizability of existing findings, and thus the higher we build the research pyramid without first attending to the width of its foundations, the less informative (i.e. likely to be true) our new theories will become.

We may however also identify positive takeaways from these first replication initiatives: science works! Repeated testing of the same predictions gives increasingly accurate evidence about which initial potentially theory-shifting findings were ‘truly true’. Hence, the ‘recipe against disaster’ is – in theory – simple: collectively scrutinize influential findings in entrepreneurship for their replicability, causality, and generalizability, until chances of a prospective theoretical extension's core underlying assumptions relying on erroneous or purely idiosyncratic prior evidence are sufficiently reduced. Cynical readers may think: well, this may be perfectly reasonable, but at the end of the day I want to keep (or get) a nice job… and universities only allow us to keep (or get) nice jobs if we regularly publish in reputable journals… and those journals only let us publish interesting findings leading to new theoretical insights… so we really have no other choice than to keep doing new things, and cannot afford wasting time on addressing the old stuff… Fair enough, I would agree that the problem is largely systemic, but hiding behind that is too easy. We often forget that we – the researchers – are the ones serving as educators, PhD supervisors, and editors and reviewers.

Even if we aim for a still rather meagre one or two replications for every influential entrepreneurship study, we would create an infinitely more reliable knowledge base (cf. Coffman and Niederle, 2015). It is not that hard to envision some simple initiatives we could all contribute to. Are you a PhD supervisor? Why can your doctoral candidate's first project not be a replication of the most influential study the proposed doctoral thesis builds on? Does the prior study replicate? Great: publish it, even if in a less fancy journal, and rest assured that the candidate's next study can be a more meaningful extension with greater confidence in its baseline assumptions. It does not replicate? Also great: publish it anyway, be proud that your student has just performed an incredibly meaningful scientific act, and rest assured that the next study can still be built on more informative baseline evidence. Do you teach a methods course to graduate students or doctoral candidates? Why can their group project not be a replication study? It would be an excellent introduction for young researchers into the technical aspects of ‘doing’ research without the pressure of already having to craft a meaningful independent contribution to theory, and imprint them early on with a deep understanding of how science should function. Do you edit an entrepreneurship journal? Phenomenal, you can make a great difference. What if you set up a ‘tender’ for each of the three, five, or even ten most cited articles per volume two or three years post-publication, and crowdsource independent teams of researchers to submit detailed research proposals for a replication of one of those studies, based upon which – after peer review of course – you hand out conditional acceptances to the two best proposals per highly-cited article (e.g. Nosek and Lakens, 2014)? As long as final acceptance for such replications is not conditional on significance of results, but only on the authors executing their replication as promised, you would contribute to a reliable entrepreneurship literature. What are constraints here? Journal space? Publish them online only! Afraid of diluting your impact factor? What is more impactful than contributing to the truthfulness of (y)our journals’ own published research?

In closing: shall we continue adding layers of theoretical complexity until, at some unknown point in the future, our house of cards collapses? Or shall we create room – even if just a bit – for greater scrutiny of our field's core assumptions? In the end it is our collective choice as entrepreneurship research community. I for one would be much more comfortable using and teaching a smaller, simpler, and gradually developing set of thoroughly-tested theoretical ideas, than a diverse and colourful set of theories that in practice are only ever weakly – if at all – assessed for their truthfulness.