Journal of Business Venturing

Journal of Business Venturing 37 (2022) 106185

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Now that's interesting and important! Moving beyond averages to increase the inferential value of empirical findings in entrepreneurship research Scott L. Newbert a, *, Romi Kher a, Shu Yang b a Narendra Paul Loomba Department of Management, Zicklin School of Business, Baruch College, City University of New York, 55 Lexington Avenue, New York, NY 10010, United States of America b Department of Management and Entrepreneurship, Frank G. Zarb School of Business, Hofstra University, Hempstead, NY 11549-1000, United States of America

A R T I C L E I N F O

A B S T R A C T

Keywords: Analytical approaches Contextualizing research Empirical methods Quantitative research

Amid the debate over whether scholars should conduct interesting or important research, we contend that entrepreneurship scholars can achieve both ends by acknowledging the foundational role context plays in our discipline and designing our empirical research in ways that enable us to explore and exploit the heterogeneity of our samples. In turn, we provide a non-exhaustive list of analytical approaches and empirical methods that can enable scholars to look past sample-wide averages and, instead, explore the nuances that exist beneath the surface of those findings. By contextualizing empirical research in these ways, scholars can move beyond these averages in order to better understand not only whether a given result is “true,” but more importantly where, when, and for whom it is or is not true, thereby increasing the inferential value of our findings.

1. Introduction In his classic paper, entitled “That's interesting!…,” Murray Davis (1971) distinguishes between interesting and non-interesting research. As Davis (1971: 327) asserts, “an audience finds a proposition ‘interesting’ not because it tells them some truth they did not already know, but instead because it tells them some truth they thought they already knew was wrong.” In other words, according to Davis (1971), interesting research is counterintuitive. Far from taking a merely descriptive stance, Davis concludes with the normative argument that “what is needed is not more social theories, but more interesting social theories” (337, emphasis in original) and that, accordingly, “the social sciences as a whole could be much improved if all students of social life were taught to evaluate their own research according to this criterion consciously” (1971: 336, emphasis in original).

Davis' (1971) contention that scholars should focus only on what is interesting has since been criticized for its incompatibility with scientific progress. As his critics contend, if the only theories we develop are those that are counterintuitive, and if counterintuitive facts are required to support them, then no robust body of work can emerge by which those theories can actually be validated (Pillutla and Thau, 2013; Tihanyi, 2020). For these reasons, Tihanyi (2020) has recently argued that instead of focusing on research which is “interesting,” scholars should focus on that which is “important.” According to Tihanyi (2020: 330), important research “helps our societies in finding answers to a wide range of problems involving management and organizations.” As Pillutla and Thau (2013: 192)

* Corresponding author.

E-mail addresses: scott.newbert@baruch.cuny.edu (S.L. Newbert), romi.kher@baruch.cuny.edu (R. Kher), shu.yang@hofstra.edu (S. Yang). https://doi.org/10.1016/j.jbusvent.2021.106185 Received 30 June 2021; Received in revised form 15 October 2021; Accepted 24 November 2021 Available online 7 December 2021 0883-9026/© 2021 The Author(s).

Published by Elsevier Inc. This is an open access article under the CC BY-NC-ND license (http://creativecommons.org/licenses/by-nc-nd/4.0/).

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add, “the theory itself may be dull or old, but as long as the problem is one that is unsolved and of interest, it is demanding theory that explains it.”

While we agree that the relevance of a problem to real-world challenges should be a main consideration of researchers, we caution Davis' (1971) critics to avoid throwing the baby out with the bathwater. After all, even research that meets Tihanyis' (2020) definition of importance still needs to be read in order to have the kind of practical impact for which he calls. And, to the extent that Davis (1971) and Tihanyi (2020) are right in surmising that both scholars and the media are more likely to read and promote research that challenges their assumptions as opposed to that which appears trivial, the interestingness of our research still matters. So, rather than frame what is interesting and what is important as an either-or choice, we maintain that research can, and should, be both interesting and important.

In mounting our argument, we begin by noting that the focus of the debate over interesting vs. important research has been largely confined to the “what” – what types of theories should be proposed (Davis, 1971) or what types of phenomena should be studied (Pillutla and Thau, 2013; Tihanyi, 2020) – and have, in the process, ignored the “how” – how scholars can actually test theories or examine phenomena in ways that generate interesting, important findings. This lack of attention to empirical issues is noteworthy given that the genesis of the debate over interesting vs. important research is an explicit focus on “those theories which Kant has called ‘synthetic a posteriori propositions’” (Davis, 1971: 310), or theories that require empirical observation to confirm. Davis (1971: 310) rationalizes his decision not to address how empirical concerns inform the interestingness of our research by claiming that “space forbids consideration here of the various types of non-propositions that are also capable of evoking interest” such as “findings which confirm or disconfirm hypotheses.” Moreover, neither Pillutla and Thau, who acknowledge that “the validity of any law depends on the strength of the empirical evidence” (2013: 190, emphasis added), nor Tihanyi, who notes that “our theories and findings, via the pages of textbooks, teaching, and through the media, can shape the minds of future managers” (2020: 330, emphasis added), address how the empirical content of our research can contribute to its importance.

We see an opportunity to complement this acute focus on what scholars should study in order to generate research that is either interesting or important, by focusing on how scholars should study it in order to generate entrepreneurship research that is both interesting and important. We believe that by being thoughtful about the strategies by which scholars approach their empirical work as well as the tactics by which they implement those strategies, they can produce interesting, important findings no matter the problem they study or theory they employ to study it. To be clear, our position is not that extant empirical research in entrepreneurship is uninteresting and/or unimportant. On the contrary, the entrepreneurship field has progressed from a fringe area of scholarship to a mainstream discipline on the very basis of increasingly rigorous empirical (and theoretical) work. Thus, our thesis is simply that we can do better; that there exists an opportunity to conduct empirical research that is more interesting and more important than has been the custom to date and, in so doing, increase the inferential value of our findings. Note, in fleshing our thesis out, we focus solely on quantitative analysis. While qualitative research can likely also be enhanced to increase the interestingness and importance of the insights it provides, we leave consideration of that issue to future scholars.

2. The role of context We propose that a main reason that we, as entrepreneurship scholars, have not fully-exploited the interestingness and importance of our quantitative research is that we have tended to employ theories meant to predict context-free phenomena to propose and/or test conceptual models that are not context-free. According to Whetten (1989: 492), context refers to the “when,” the “where,” and the “who” of a given phenomenon. As he maintains, “these temporal and contextual factors set the boundaries of generalizability, and as such constitute the range of the theory” (Whetten, 1989: 492). In support of this conceptualization, Welter (2011: 167) argues that “by introducing the who, where, and when dimensions of context, Whetten (1989) draws attention to the diversity and manifold facets of context.” While most scholars advocating the incorporation of context into our research have focused primarily on the “where” (i.e., the locations in which entrepreneurship happens; Welter, 2011; Welter and Baker, 2021) or the “when” (i.e., the temporal and historical influences on entrepreneurship; Ancona et al., 2001; McMullen and Dimov, 2013; Mitchell and James, 2001; Mosakowski and Early, 2000), Johns (2006: 391) reminds us of the importance the role the “who” (i.e., the individuals who enter entrepreneurship) plays in assessing the limits of a given theory. He writes, At first glance, it might seem strange to consider who is being studied as a contextual variable. However, use of the who heuristic alerts us to the occupational and demographic context in which all organizational members find themselves embedded. Thus, the who variable concerns both direct research participants and those who surround them. Gender provides a good example.

The distribution of the sexes in the workplace can be a potent if subtle contextual variable. Furthermore, men and women often face very different work and nonwork contexts such that separate models may be required to adequately describe their attendance patterns and their career advancement.

In light of this shared understanding of context, we contend that only by considering whether and how our theories hold up across distinct locations, at various times, and for different types of entrepreneurs can we truly generate findings that are both interesting and important. Of course, incorporating context into academic research is arguably important in all fields, but we believe it to be particularly so in entrepreneurship given that, as Baumol's historical analysis reveals, “how the entrepreneur [who] acts at a given time [when] and place [where] depends heavily on the rules of the game” (Baumol, 1990: 894). Given his acknowledgement that the rules of entrepreneurship “change dramatically from one time and place to another” (1990: 898), it would seem logical to contextualize our research in ways that reflect its dynamism.

Unfortunately, despite the fact that calls for incorporating context directly into our research are not new, scholars have by-and2

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large tended not to do so (Welter, 2011). Indeed, as Whetten (1989: 492) lamented more than three decades ago, “few theorists explicitly focus on the contextual limits of their propositions. In their efforts to understand a social phenomenon they tend to consider it only in familiar surroundings and at one point in time.” To be fair, there are whole theories that are often applied to entrepreneurship research that, by definition, allow for contextualized research. For example, Yang et al. (2020) analyze how gender affects the degree to which men and women benefit from prior investment when seeking entry into startup accelerators by applying gender role congruity theory (a “who” theory), Boudreaux et al. (2019) explore how country-level institutional context moderates the relationship between cognition and opportunity entrepreneurship by applying institutional theory (a “where” theory), and Boone et al. (2020) examine how effective team entrepreneurial passion is at reducing conflict and improving performance at different stages of venture development by applying organizational life cycle theory (a “when” theory). And although these and related studies have revealed some extremely interesting, important empirical findings with regard to context, we as entrepreneurship scholars have rarely stepped beyond the well-defined boundaries of contextualized theories to explore how the phenomena we study might be influenced by other “who,” “where,” and “when” factors. We maintain that this circumscribed attention to context has limited the inferential value of our findings by failing to reveal the limitations of the many other theories we apply to our research and the boundary conditions of our subsequent findings. Accordingly, we propose that there are at least two paths forward in order to increase the interestingness and importance of our research: [1] contextualize our theorizing and/or [2] contextualize our empirical analysis. Given the abundance of recent studies that have provided thoroughgoing discussions of how scholars might address the first option (e.g., Bruton et al., 2021; Filatotchev et al., 2021; Szkudlarek et al., 2021; Wadhwani et al., 2020; Welter and Baker, 2021), we focus herein on the second.

2.1. Moving beyond averages To begin, we maintain that the main consequence of the largely context-free approach to empirical work in our field is that we more often than not employ analyses that yield insights about the sample as a whole. In other words, most findings in the field are useful in understanding the “average” entrepreneur or the “average” venture. But, as we know, there is no “average” entrepreneur or “average” venture (Davidsson, 2003). Indeed, novelty, idiosyncrasy, and distinctiveness constitute the very essence of entrepreneurship. Thus, studies that fail to dig beneath the surface of the samples they analyze will invariably generate results that are not reflective of the individuals (or groups of individuals) that comprise it, thereby limiting their inferential value.

As Fig. 1 illustrates, when our level of analysis is the sample as a whole (Panel A), we inherently assume that the estimate of the X-Y relationship that emerges from our empirical analysis tells us something about all members of that sample. However, it is generally the case that this relationship unfolds quite differently for each of the distinct subgroups that make up that sample (Panel B). While it is possible that the sample-wide estimate will hold for some subgroups (e.g., subgroup I), it is equally likely to be weaker (e.g., subgroup II), stronger (e.g., subgroup III), and/or reversed (e.g., subgroup IV) for other subgroups. It is only when we contextualize our empirical approach that we are able to identify whether and how the nature of a given relationship differs across the sample. It is precisely by demonstrating that sample-level effects do not hold for all cases, but rather vary based on any number of “who,” “where,” and “when” factors, that we can increase the value that can be inferred from our empirical analyses.

If different types of entrepreneurs are indeed behaving in unique ways, we are underserving our readers by explaining that behavior on the basis of omnibus correlations. On the one hand, we risk overgeneralizing a behavior to all types of entrepreneurs simply because a correlation is significant at the level of the sample. On the other hand, we risk missing out on what might be significant beneath the surface because a correlation is not significant. As Davidsson (2003: 354) explains, due to the heterogeneity of most samples of entrepreneurs, “the research may end up with a sample that is too diverse for any strong relationships to emerge.” If, instead, we could

IV

III Panel A Notation:

I

II Panel B

Case – Correlation -- Subgroup boundary Fig. 1. Sample vs. subgroup correlations.

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conduct empirical studies that provided greater insight into what different types of entrepreneurs, operating in different environments, at different points in time do, then we can avoid these risks and the interestingness and importance of our research would increase dramatically. Specifically, such an approach would demonstrate where, when, and for whom the sample-wide averages that we currently assume to represent the “truth” about a given X-Y relationship are both true and untrue. By revealing new insights into a given theory's boundary conditions, such an approach would, by definition, engender unexpected, counterintuitive, interesting (Davis, 1971) results. Such an approach would also provide entrepreneurs who may be struggling to implement strategies for the “average” entrepreneur with a more effective set of strategies tailored to the specific contexts in which they operate. By identifying the nuances that underly the generic tools that we have heretofore provided to entrepreneurs, such an approach would provide more accurate answers to the relevant, real-world, important (Tihanyi, 2020) problems entrepreneurs face.

3. Limitations of common approaches Our call to entrepreneurship scholars to engage in more interesting, important empirical research begs the question, “how is this to be done?” As alluded to above, the overarching solution that we propose is to avoid the tendency to analyze the average entrepreneur given that the very essence of entrepreneurship suggests that averages are unlikely to apply broadly. In order to arrive at interesting, important findings that reflect the dynamism of the phenomena we study, we must, therefore, take the time to explore and exploit the heterogeneity in our samples. Before highlighting some empirical approaches that scholars can employ in order to answer the above question, we first discuss how two techniques commonly employed to account for context – control variables and moderator variables – often fall short of this goal.

3.1. Control variables Control variables are a critical component of research and their inclusion allows researchers to account for possible confounding factors in a given X-Y relationship. When used correctly, these variables help researchers derive more precise estimates of Y as they account for the effects of extraneous variables. On the other hand, when a relevant control variable is missing from the estimation model, researchers may encounter the issue of omitted variable bias, a situation in which the estimate of Y is biased due to a key variable (X) missing from the equation. Yet, even if we assume that all of the “right” control variables are included in a given analysis, their ability to explain context is limited. Because a regression analysis predicts an outcome (Y) conditional on all inputs (all Xs), the estimated coefficient for each control variable is “conditional on” or “adjusted for” all of the other Xs in the equation. Thus, a control variable coefficient cannot be interpreted as the independent effect of that variable on the outcome, but rather the partial effect of that variable on the outcome given all of the other variables in the equation. This is not to say that control variables are not useful to understanding the relationship between an independent and dependent variable, but rather that their coefficients cannot tell researchers much about the contextual issues they are included to account for.

To illustrate this point, assume that we want to investigate the impact of the number of years of entrepreneurship education (X1) on an individual's proclivity to pursue entrepreneurship (Y) and decide to control for the individual's age (X2) and gender (X3). Let us further assume that once we run our regression, the coefficients for X1, X2, and X3 are positive and significant. This is where we often misguidedly try to interpret these coefficients independently, even though each coefficient is actually conditional on the other. In other words, all we can truly deduce from our regression output is that more entrepreneurship education (X1) has a positive impact on the proclivity to pursue entrepreneurship (Y) conditional on the individual's age (X2) and gender (X3). While the inclusion of these control variables enables us to partial out the effects of age and gender in order to provide a more precise estimate of the relationship between education and entrepreneurship, they do not enable us to deduce any differences in an individual's proclivity to pursue entrepreneurship due to age or gender. Thus, if we are interested in for whom education matters when trying to identify future entrepreneurs, simply adding control variables for age and gender does not provide us any real insight into these potentially interesting and important contextual factors.

To reiterate, control variables are important as they both help researchers account for possible confounding factors in our estimation of Y and address omitted variable bias. Yet, even when used correctly, the meaning we can extract from the coefficients of control variables, with respect to contextual differences, is limited at best because estimates of these variables are conditional outcomes that cannot be interpreted on their own. For this reason, Johns (2006: 391) argues that “the frequent practice of controlling for the who variable in much organizational behavior research simply washes out salient contextual influence.” Thus, rather than trying to control context away, we contend that reseachers would be better served by digging into context by incorporating it as part of the research design in the ways in which we will outline in Section 4.

3.2. Moderator variables Moderators are a natural next step toward explaining context beyond the limited inference provided by control variables. A moderator variable is often included in empirical analyses in order to help researchers determine whether and how an X-Y relationship varies based on a third “where,” “when,” or “who” variable. In order to test for such effects, researchers generally include an interaction term between the moderator and independent variables in their regression analyses and rely on their sign and significance levels to accept or reject the associated hypotheses. Unfortunately, this is an incomplete approach for at least two reasons. First, because the interaction term coefficient is actually a composite estimate, it needs to be untangled into its individual parts to fully understand the context in which the moderation effect occurs, if at all. Second, as Hoetker (2007) points out, the sign and significance of the 4

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interaction term, especially in non-linear models, may not necessarily reflect the actual direction or significance of the interaction.

To illustrate the complexity of the interaction coefficient with an example, assume that we are interested in assessing how the impact of an entrepreneurial training program (independent variable, coded one for those who received training and zero otherwise) on venture performance (dependent variable) differs according to the gender of the entrepreneur (a “who” moderator variable, coded one for women and zero for men). Further assume that when we run our moderated regression analysis, we find that the coefficient of the interaction term (training * gender) is not significant. As researchers, we might stop at this step and conclude that no gender differences exist. However, because both the independent (presence or absence of a training program) and moderator (female or male) variables are dichotomous, there are actually four distinct outcomes that make up this one interaction coefficient – women who underwent training, men who underwent training, women who did not undergo training, and men who did not undergo training.

Because interaction effects reflect the multiplicative combination of the independent and moderator variables on the dependent variable, the coefficient for the interaction term in the regression output only reflects the outcome of one such category – women (coded one) who underwent training (coded one) – and not the other three possibilities. As such, this coefficient does not tell the whole story. Were we to dig more deeply into this meta-estimate by examining how the impact of the training program varies both betweenand within-gender, it is possible that we would uncover evidence that the moderation is statistically significant for one of the other (training * gender) categories, even though the overall composite coefficient is not.1 While plotting the interaction effect can better enable researchers to assess whether contextual differences exist in the data (Aiken and West, 1991), the value of any inferences that can be made is dependent upon what is actually plotted. In entrepreneurship, researchers tend to plot interactions by [1] computing discrete values for the interacted variables based on the coefficients from the regression output in order to simulate values of Y and then [2] connecting those points in order to intuit the slope of the effect, the result of which is often an X-shaped plot. While this approach pervades management research (Busenbark et al., 2021), it is plagued by at least three limitations which hinders its ability to communicate the size and significance of any potential between- and withinvariable differences and, in turn, any meaningful contextual nuances that might exist in the data. First, because these plots include only a finite set of X-Y values, their inferential value about the moderation effect is incomplete (Brambor et al., 2006). Second, because the plotted points are usually connected with straight lines, these plots assume, oftentimes erroneously, that the interaction effect is linear (Hainmueller et al., 2019). Third, as alluded to above, because the regression coefficient used to generate the plotted points is derived from only one of the four possible contextual categories (e.g., women who underwent training), these points do not capture any contextual nuances of the other categories (Hoetker, 2007).

Given these concerns, scholars have encouraged researchers to compute and plot marginal effects, or the predicted values of Y conditional on each possible interaction outcome, instead of plots generated from regression coefficients (Brambor et al., 2006; Hainmueller et al., 2019; Hoetker, 2007). By plotting the estimated marginal effects of the independent and moderator variables over the full range of outcome values, researchers can more accurately infer how the moderator variable amplifies and/or attenuates the effect of the independent variable on the dependent variable. Thus, while moderator variables can be extremely useful in understanding contextual nuances in our data, their value is often limited due to the fact researchers generally fail to analyze them in ways that can maximize their inferential value. To this end, we elaborate on marginal effects analysis in Section 4.1.4.2.

4. Accounting for context in empirical studies The above discussion is not meant to imply that control and moderator variables do not have value in our research. They do. Our prior discussion of their use, therefore, is intended merely to help researchers appreciate the limits to which they can provide insight with respect to contextual issues, so that those who are interested in studying context can complement these approaches with additional techniques that can provide a more informed understanding of where, when, and for whom their results do and do not matter.

Below, we provide a non-exhaustive list of analytical approaches and empirical methods that scholars can employ in order to increase the importance and interestingness of their research toward this end. For each technique, we provide a brief explanation of how it can be effectively used to explore context, followed by a brief overview of an empirical study that has used it. As this is not a “how-to” methods article, we encourage interested authors to consult these exemplar studies for additional detail regarding application.

4.1. Analytical approaches The analytical approaches below are strategies researchers can employ in order to test whether contextual nuances exist in their data. These approaches can motivate the study (e.g., replication), test and validate context-based hypotheses (e.g., subgroup analysis, robustness checks), or further probe where, when or for whom an effect might differ (e.g., post-hoc analysis). In all cases, however, the approach should only be used if it aligns with the underlying research question and design of the study.

4.1.1. Replication As argued above, just because a relationship is found to be significant for one sample of individuals or organizations, in one place, at one point in time, that does not mean that it holds for other individuals or organizations, in other places, at other points in time. Thus, 1 Of course, researchers can also explore the moderation effect by including three of the four categories as dummy variables, with the fourth as a reference group. However, the inferences that can be drawn from the dummy variable coefficients is limited given that they enable direct comparisons only with reference group and not with the other categories, thereby hindering the ability to make between-group comparisons.

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conducting the same analysis on different whos, wheres and whens should help us sharpen our understanding of a given phenomenon.

As Popper (1959: 45) argues, We do not take even our own observations quite seriously, or accept them as scientific observations, until we have repeated and tested them. Only by such repetitions can we convince ourselves that we are not dealing with a mere isolated ‘coincidence,’ but with events which, on account of their regularity and reproducibility, are in principle intersubjectively testable (p. 45).

Tsang and Kwan (1999) call on scholars to operationalize this guidance by engaging in replication. In so doing, they develop a typology of replications based on the nature of the data and the methods employed to analyze it. Among these replication options, at least four – empirical generalization, exact replication, conceptual extension, and generalization and extension – would help scholars identify variation in X-Y relationships based on nuances in context.

In an empirical generalization and an exact replication, scholars apply the same statistical procedures as the original study in order to test the focal relationship on new data (Tsang and Kwan, 1999). More specifically, in an empirical generalization, scholars draw their sample from a new population. By analyzing the same relationship in an entirely different context, they can assess whether and to what degree the findings from the original study hold in that new context. In an exact replication, however, scholars draw their sample from the same population. While this approach might seem, at first blush, to be less able to discern boundary conditions in the focal relationship, it is important to note that because we often do not know (or do not test for) the extent to which the various heterogeneous groups in a population are over- or under-represented in our samples, we cannot assume that the estimates generated by any given analysis approximate those for the population as a whole. And, even if we do test for representativeness, the average result we obtain is, as argued above, unlikely to hold for each subgroup within that population. Thus, to the extent that different samples from the same population reflect different subgroups, or different proportions of subgroups, each successive sample can provide new insights unavailable to the original researchers.

For example, in a recent empirical generalization, Arend et al. (2016) replicate Busenitz and Barney's (1997) study of entrepreneurial decision-making, but collect their data from a new population of entrepreneurs. By confirming Busenitz and Barney's (1997) earlier finding that entrepreneurs think differently than managers due to overconfidence bias and the representativeness heuristic, Arend et al.'s (2016) study is both interesting and important. It is interesting because it adds credibility to the earlier results by demonstrating that they hold in a different context. It is important because it reinforces what we think (based on one population) we know about how entrepreneurs make decisions.

Unlike the above two replication approaches, a conceptual extension and generalization and extension enable researchers to apply different measures and/or analyses to those used in the original study (Tsang and Kwan, 1999). The value of such approaches is that researchers can glean whether a relationship holds not only for different samples from the same population, such as in a conceptual extension, or different populations altogether, such as in a generalization and extension, but also for different empirical specifications.

More specifically, these designs allow researchers the ability to explore how the original study's findings hold up in a new context while, at the same time, providing them the latitude to utilize alternative measures and analytical approaches, both of which may be necessitated by the type of data that is available in the new population, which is of particular concern in the case of secondary data.

As one example, Park et al. (2016) conduct a generalization and extension of three different studies (Certo et al., 2001; Filatotchev and Bishop, 2002; Cohen and Dean, 2005), all of which explore the effect of top management and board-level characteristics on IPO underpricing. The authors of this replication proceed to test each of the hypotheses put forth in the original studies with entirely new data (US-based IPOs between 2010 and 2013) and find that virtually none of the original results hold. While there are many possible explanations for the difference in findings, Park et al. (2016) surmise that they might be explained by differences in temporal and geographic contexts. Specifically, given that each of the original studies analyzed data from the 1990s, which was prior to both the widespread use of the Internet (and social media in particular) and a relevant 2005 SEC regulation pertaining to the quiet period leading up to an IPO, they speculate that “perhaps access to rich fine-grained information and the sources of such information along with the regulatory changes may have potentially diminished the significant signaling value observed in past studies” (2016: 2376).

Park et al. (2016: 2374) also suspect that their results may have differed from those found by Filatotchev and Bishop (2002), who analyzed a sample of IPOs listed on the London Stock Exchange, given “differences between U.K. and U.S. markets in terms of the mechanisms guiding IPO pricing and control.” By suggesting that “where” and “when” IPOs are undertaken matters, the inferences that can be drawn from this study are clearly both interesting, by revealing reveling the temporal and geographic boundary conditions of prior findings, and important, by identifying a more appropriate roadmap for ventures seeking to offer IPOs. 4.1.2. Subgroup analysis As argued above and illustrated in Fig. 1, a given relationship is unlikely to manifest the same way for all entrepreneurs, in all locations, at all points in time. Thus, subgroup analysis can enable scholars to dig more deeply into their data by uncovering whether and to what degree the correlations they find for the sample as a whole hold for different “whos,” “wheres,” and “whens.” Scholars can exploit their data by examining subgroup effects in at least one of two ways. For starters, they can develop formal hypotheses that predict how various “who,” “where,” and “when” factors ought to contextualize the focal relationship as outlined by Welter (2011).

The benefit of this approach is that scholars can not only provide evidence of the nuanced ways in which a relationship unfolds for each subgroup, but also explain why those differences exist. However, when contextualizing hypotheses proves too daunting (i.e., due theoretical challenges, space limitations, etc.), scholars can analyze different subgroups in a set of exploratory analyses. While such an approach may only enable scholars to speculate as to why any nuances in the correlations exist, the fact that they do (or do not) is a valuable first step in establishing the boundary conditions of the underlying theory. This latter approach is particularly useful when it is not clear which subsamples would result in the most homogenous subgroups a priori (Davidsson, 2003). It is important to note that 6

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these two options are not mutually exclusive. In fact, studies that test contextualized hypotheses and then also explore additional subgroup effects are likely to provide the most comprehensive set of insights about the focal relationship, thereby maximizing the inferential value the empirical analysis provides to readers.

For example, in response to the Chinese government's promotion of entrepreneurship as part of its national urbanization strategy, Liu et al. (2019) explore the effect of human capital, social capital, and community trust on the decision of migrants to pursue entrepreneurship. In so doing, they also seek to determine what differences, if any, exist between migrants residing in rural vs. urban areas given the Chinese government's emphasis on rural migrants in order to close the wealth gap between urban and rural residents.

Their results for the full sample suggest that men, older individuals, and individuals without a college degree are more likely to pursue entrepreneurship and, more importantly, that human capital, social capital, and community trust do not impact this decision. However, by analyzing these relationships for each of three subgroups – rural residents, urban residents, and rural migrants – the authors find that who the entrepreneur is, matters. Specifically, Liu et al. (2019) find that the negative effect of age holds only for rural residents (but not urban residents or rural migrants) and that community trust, which is not significant in the full sample, is a significant factor in the decision to pursue entrepreneurship for rural migrants (but not rural residents or urban residents). The finding that community trust significantly impacts rural migrants' decision-making is interesting given that it stands in contrast to the decisionmaking processes of other potential entrepreneurs. Moreover, because rural migrants are the individuals the Chinese government is most trying to serve, this finding clearly has important implications for policy-making decisions.

4.1.3. Robustness checks Before drawing any conclusive inferences from our results, it is useful to first confirm whether those results are robust enough to hold under different conditions and how the results might change when the assumptions underlying the data are tightened, relaxed, or otherwise altered. Which specific robustness checks to employ depend entirely on the individual research question, but researchers would be well-served by exploring alternative measures for the key independent variables, using different reference groups, and imposing varying restrictions on the dataset. By conducting such tests, researchers can determine whether they have indeed identified a “true” relationship between X and Y. This attempt to validate findings by triangulating results from multiple similar tests can help researchers either establish boundary conditions for the focal relationship or alert them to the possibility that the correlation between X and Y is simply spurious. In either case, such results can demonstrate how contextual factors influence what we know about the relationship, thereby providing more interesting and important findings than a mere sample-wide regression estimate.

As one example, Brachert et al. (2019) conduct several different robustness checks (e.g., rerunning their analyses with varying time periods and employing alternative indicators for their independent and dependent variables) to validate their finding of a significant relationship between self-employment and individual risk preferences. Because their robustness checks generate results that align with their initial findings, Brachert et al. (2019) are able to conclude with more confidence that the relationship they have discovered is “true” regardless of "when," which is arguably an important outcome. Of course, had any of these robustness checks diverged from those initial results, the relationship would not be deemed “false,” but rather merely subject to certain temporal contextual (i.e., interesting) nuances.

4.1.4. Post-hoc analysis Once researchers have confirmed that their results are robust, they can then explore intricacies via additional post-hoc analysis.

Post-hoc analyses are powerful because they allow researchers to explore nuances in their data after hypotheses have been developed (perhaps even in a contextualized way) and tested. Because post-hoc analyses are not driven by theory, they often reflect an “honest” approach to research (Kerr, 1998). Whereas hypothesis testing research is often criticized due to suspicion of p-hacking/cherry-picking (conducting multiple analyses with alternative measures to find the results that best support a hypothesis) and/or HARKing (hypothesizing after results are known) (Murphy and Auginis, 2019), post-hoc analysis frees scholars from such criticism by affording them the space to explore patterns in the data that they may not know exist or that they may not have considered to have existed at the hypothesis stage. This way, scholars can explore relationships that appear interesting and/or important based on the initial findings, analyze them, and then infer boundary conditions that establish where a given result does and does not hold. In this way, post-hocs are guided by intellectual curiosity toward unveiling new knowledge that lies outside what we are able to theorize, and in so doing, arrive at potentially interesting and important conclusions that would not be gleaned from our formal hypothesis tests. Among a variety of post-hoc analyses that might be useful in increasing the inferential value of our empirical findings, the following may be especially useful for our purposes.

4.1.4.1. Sensitivity analysis. Sensitivity analysis allows researchers to discover how much variation in the value of the X impacts the Y (Rosenbaum and Rubin, 1983). Such analysis allows researchers to approach what-if questions with more certainty and, in so doing, dig more deeply into their findings. From an econometrics standpoint, sensitivity analysis is different from a robustness check because here, researchers are not seeking to prove or disprove whether the relationship exists, they are simply seeking to explore what would happen if one input were to change. While common in finance research, entrepreneurship scholars can similarly benefit from exploring the boundary conditions of their results in this way.

For example, research has established that women founders are at a disadvantage when seeking debt and equity financing (Marlow and Patton, 2005). This is an important finding as it highlights a fundamental inequity in the entrepreneurial ecosystem. But suppose we wish to determine if this gender-financing relationship also holds in the burgeoning context of Initial Coin Offerings (ICOs). We might begin by running a regression to determine if female founders raise less financing than male founders via an ICO. If the effect is 7

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significant, this finding would also be important, but given the precedent for this type of gender bias in the extant entrepreneurial financing literature, it would not be particularly interesting. However, a sensitivity analysis could show us what would happen to financing outcomes if we were to add a male co-founder to every female founded venture. By changing this one input, we could better understand the nature of the funding bias and glean more insight into this process. It is possible that in the ICO context, funding biases evolve differently than in debt and/or equity contexts, but these cannot be revealed by a simple regression analysis. Thus, this additional step could make the research outcome from such a study not only more important, but more interesting as well.

In a recent article, Ferede (2021) uses sensitivity analysis to provide more insight into his primary finding that Canadian provinces that raise their provincial top personal tax rate by 1% will experience a loss of 405 new businesses. For one sensitivity test, he de­ termines self-employment outcomes by including the federal tax rate and compares that outcome to the original estimation where only the provincial tax rate is used. This additional analysis demonstrates how his results change when other factors are included in combination with, and instead of, the original estimation variables. By supporting his original results regarding the role tax rates play in promoting local small business, Ferede's (2021) sensitivity analysis has important implications for those charged with setting tax policy. Yet, because these additional tests also tease out how the business population is influenced by different types of taxes, his results also establish interesting boundary conditions for the focal relationship.

4.1.4.2. Marginal effects and contrast analyses. A marginal effect represents a change in Y as a function of a change in X, holding all other variables constant (Greene, 1997). In linear regression analysis, for example, a marginal effect can help quantify the impact of a given variable versus its average effect. As such, marginal effects are important as they can help researchers look beyond the samplewide average estimates from regression analyses in order to understand what the model actually says about specific groups or in­ dividuals in the sample. Moreover, marginal effects analysis is often combined with contrast analysis in order to test whether the differences between groups is statistically significant. In this way, marginal effects analysis can help researchers move beyond sta­ tistically significant averages toward a deeper understanding of the substantive significance of their results.

As argued in Section 3.2, marginal effects analysis is critical when interpreting moderation variables. To illustrate how, let us return to our previous example in which we were interested in assessing how the impact of an entrepreneurial training program on venture performance differs by gender. Let us assume this time, however, that the interaction term (training * gender) is significant. In that case, all that the coefficient for this term tells us is that venture performance is conditional on gender and training. This may or may not be important, but because of the ambiguity in what we actually know on the basis of this result (as discussed in Section 3), it definitely is not interesting. A marginal effects analysis, however, can break this interaction down into its constituent parts by calculating predicted outcomes for each of the four distinct gender-training conditions. By then conducting a contrast analysis of different conditions, we can both determine whether any differences between men and women are statistically significant and compute robust effect sizes for each group. If the differences in probability outcomes for men and women are sizable, we may, in turn, be inclined to conduct additional post-hoc subgroup analysis to identify where or for whom our sample-wide significance does not hold, even though overall, we have a gender effect. As evident, these simple post-estimation commands can provide us with nuanced results that truly help us understand our research question. The fine-grained conclusions these analyses enable provide far more important and interesting insights to our readers than regression coefficients alone.

To highlight one example of this approach, Yang et al. (2020) investigate the acceptance decisions of social impact accelerators (SIAs) and find that they are impacted by the level of congruity between the signals a startup sends and the gender of its lead founder.

Their mixed-effect Probit regression results suggest that, on average, male-led startups are preferred by SIAs, regardless of the signal a startup sends. However, these authors then conduct marginal effects analysis to calculate the predicted probabilities of acceptance for each of four gender-signal scenarios – male-led startups sending economic signals, female-led startups sending economic signals, maleled startups sending social signals, and female-led startups sending social signals – and then contrast these probabilities to find the precise size and significance of the differences in SIA acceptance rates for male- and female-led startups based on the signals they send.

These subsequent analyses highlight the fact that, among all startups sending social signals, those led by women have higher acceptance rates than men. Yang et al.'s. (2020) ability to identify a scenario in which women outperform men is both interesting, given that it runs counter to evidence that accelerators overwhelmingly prefer male entrepreneurs (which is corroborated by the overall average effect they find), and important, given the implications this finding has for entrepreneurs seeking entrance into accelerator programs.

4.2. Empirical methods In addition to the above analytical approaches, researchers can also employ various empirical methods to tease out contextual nuances in their data. We highlight three such techniques below that can be used to analyze issues related to “when” (e.g., regression discontinuity), “where” (e.g., difference in differences), or “who” (e.g., Monte Carlo simulation). To be clear, not only are these methods not limited to answering the specific context-based question we highlight here, but there are also many other methods that can be used to answer these questions. Thus, our objective is to merely showcase how certain methods can be effectively used to this end. Of course, as with all methods, each of the tools below can only succeed at isolating context-based differences if the data are appropriate for the technique.

4.2.1. Regression discontinuity Although in observational studies, researchers cannot randomly assign treatment to specific groups, they may nevertheless still be 8

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interested in studying the impact of a treatment on a specific group. In such instances, researchers can establish a threshold level to divide their samples into two groups representing those that received an intervention and those that did not. They can then use regression discontinuity (RD) design to compare the outcomes experienced by cases just above and just below this threshold. In most uses of RD, thresholds are defined by specific events, such as the receipt of angel funding (Kerr et al., 2014). Given that such events are generally experienced by cases in the sample at different points in time (i.e., not all new ventures receive angel funding on the same day), no inferences with regard to time can be drawn. However, when temporal issues of are of interest, researchers can employ a variant of RD, known as regression discontinuity in time (RDiT). This technique “has adapted the RD framework to applications where time is the running variable and treatment begins at a particular threshold in time” (Hausman and Rapson, 2018: 533). In other words, RDiT is a special case of RD that can explore contextual issues related to time by operationalizing RD's thresholds as specific points in time, such as dates corresponding to economic disruptions or regulatory changes. Given that all cases in a sample are exposed to the same temporal threshold, researchers are able to use RDiT to compare discontinuity in the outcome variable before and after the threshold date. As such, inferences can be drawn about whether what occurred before a specific point in time is significantly different than what happened afterward, thereby enabling researchers to establish whether and to what extent the “when” matters.

As one example, Baruffaldi and Simeth (2020) leverage RDiT to study how the change in the American Inventors Protection Act, which reduced the disclosure times for patents filed at the United States Patent and Trademark Office, impacted the knowledge diffusion of patents filed after this date (treatment group) compared to those filed prior to this date (control group). The authors find that a one-year reduction in disclosure times led to a 12% increase in patent citations and that citations by patent attorney services firms grew twice as much due to this policy change. Because traditional regression techniques do not account for the temporal order of the events when determining averages, RDiT is able to provide a nuanced understanding of the impact this policy had on patent filers based on when they filed. Such a finding is both interesting, as it reveals important differences in patent citation rates based on the introduction of this Act, and important, as it highlights the impact policy-makers can have on knowledge diffusion when establishing patent regulations.

4.2.2. Difference-in-differences Difference-in-differences (DiD or Diff-in-Diff) seeks to explore differences between a treatment group and a control group by comparing the average differences between the these groups before and after an event of interest. In implementing DiD, researchers first divide their samples into two groups: the treated group, which experienced an intervention, and the control group, which experienced no such intervention. They then measure outcome levels for each group prior to and after the intervention. Finally, the difference of the differences in outcomes between the two groups (pre- and post- treatment) is calculated to determine the effect (if any) of the intervention on the treated group. Because there are several common characteristics between the two groups, a key assumption behind this method is that while the unobservables may differ between the two groups, their effect does not change much over time and, thus, any differences between the two groups can be attributed directly to the intervention.

Assenova (2020) uses this method to investigate the effect of institutional norms on the selection probability of a sample of startups that applied to a global network of accelerators. To do so, she divides her sample into two groups – the treated group, comprised of startups formed in countries that experienced institutional changes, and the control group, comprised of startups based in countries that had no such changes – and analyzes them using DiD. Her findings reveal that institutional reforms helped startups survive and grow when compared to their counterparts in countries that had no such reforms. By uncovering evidence that where a startup is located plays an important role in its growth and survival, Assenova's (2020) findings are both interesting, given that they highlight the previously unknown role that national-level institutions play in strengthening the accelerator-performance relationship, and impor­ tant, given the message they send to governments of countries with weak institutions interested in supporting entrepreneurship.

4.2.3. Monte Carlo simulation A key underlying principle of empirical research is that a random sample from a given population will have the same underlying properties as the population as a whole. However, in many empirical studies, samples are not randomly drawn from their populations, resulting in biased samples. This bias is reflected in Fig. 1 above, whereby each nonrandom sample is likely to have a unique X-Y relationship that does not approximate the X-Y relationship for the population as a whole. One way to account for this variance is to conduct a Monte Carlo simulation. A Monte Carlo simulation is a mathematical technique that repeatedly samples the data under multiple scenarios to determine different probability outcomes of an uncertain event (Y). In so doing, it allows for many random samplings of the data, effectively simulating multiple datasets, thereby giving researchers a probability distribution for all possible outcomes, including the average of all the simulations, which is assumed to approximate the population. These multiple samplings give researchers more precise estimates since they mimic random samples drawn from a population. Researchers often take the results they get from a regression as a “truth” that is generalizable to all members of the sample (and population). However, by determining probability distributions for all possible regression outcomes, Monte Carlo simulations acknowledge and account for the fact that the sample-wide average for a given X-Y relationship is not evidence of a single “truth” about that sample, but rather that the nature of that relationship is quite likely to vary based on any number of contextual factors within a sample. As such, Monte Carlo simulations allow researchers to place less emphasis on the single point estimates and associated confidence intervals that regressions provide, and more emphasis on assessing how likely such outcomes are for a population. These probability distributions can, in turn, provide guidance to researchers as to whether sample-wide estimates are reasonably accurate or whether additional analysis of subgroups is warranted.

For example, Konon and Kritikos (2019) note that while personality profile testing has been used in various fields to give career advice to individuals, the efficacy of such testing is usually based on group averages. In their research, Konon and Kritikos (2019) observe that several personality traits have been linked to successful entrepreneurship and that most research trying to predict this 9

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outcome do so by comparing the average personality trait scores of successful entrepreneurs to the average scores of a counterfactual group (e.g., non-entrepreneurs or failed entrepreneurs). To test the value of this “average-score method” under different assumptions, the authors employ Monte Carlo simulations to draw multiple random samples from the German Socio-Economic Panel. Their simulation results show that the average-score method of personality profiling lacks precision when seeking to predict entrepreneurial success. Such average-based techniques fall short because the average personality profile cannot capture the breadth of personality types of individuals drawn to entrepreneurship. To further explore their primary finding, the authors use various subgroups (e.g., varying the percentages of entrepreneurs in the population, exploring different correlation levels between traits and abilities) also drawn from Monte Carlo simulations, to establish upper and lower boundary conditions for their findings and conclude that, under certain conditions, advice based on average scores is actually worse than a coin toss. The key insight that derives from Konon and Kritikos' (2019) Monte Carlo simulations is that entrepreneurship cannot be accurately predicted by average personality test scores due to the heterogeneity characterizing entrepreneurs. Given that Konon and Kritikos' (2019) results stand in opposition to decades of research in psychology supporting the average-score method, especially by banks and investors which have historically used per­ sonality tests as a tool to mitigate risks, they have clearly identified an interesting finding with regard to “who” does (and should) benefit from entrepreneurial financing decisions that has important practical implications for lenders.

4.3. Summary While the above list of strategies and tactics that scholars can employ in order to tease out contextual nuances in their data is by no means exhaustive, it is intended to provide some actionable guidance for scholars seeking to increase the interestingness and importance of their empirical findings. Since we as entrepreneurship scholars are seeking to understand populations that are, by their very essence, heterogeneous, we need to eschew the overwhelming tendency to provide readers with sample-wide averages in favor of the nuances that exist beneath the surface of those samples. By engaging in the approaches outlined above, we believe entrepre­ neurship scholars can progress from a general understanding of what is happening in our data to a more informed understanding of where, when, and/or for whom it is happening. By increasing the inferential value of our empirical research in these ways, the con­ clusions we draw from it can reveal interesting insights that can better prepare individual entrepreneurs (rather than the “average” entrepreneur) to more effectively address the important problems they face.

5. Illustrative example In order to provide a more in-depth illustration of the problem we identify herein as well as evidence of the effectiveness of some of the techniques proposed above, we conduct a de novo empirical analysis of the relationship between accelerator participation and emergence. Our decision to analyze this relationship is due to the fact that the accelerator is increasingly considered to be an important component of the entrepreneurial ecosystem and emergence, or “the successful transformation of a nascent organization to an operational organization” (Tornikoski and Newbert, 2007: 312), is a main objective of startups and accelerators alike (Cohen and Hochberg, 2014). From a practical perspective, in 2020, 2971 accelerators across the globe helped early-stage startups raise more than $2.7B in financing (Crunchbase, 2020). Moreover, startups are widely agreed to contribute heavily to economic growth and devel­ opment and wealth redistribution (Kirchhoff, 1994). From an academic perspective, of the more than 100 articles published on ac­ celerators since 2004, almost half were published in the last three years (Crișan et al., 2019; Yang et al., 2020), and virtually all find positive relationships between acceleration and various outcomes of interest to entrepreneurs (e.g., financing, employment, survival, etc.), most of which are fundamental to emergence.

While the abundance of research on accelerators justifies the topic's importance, it might also appear, at first blush, to undermine the interestingness of this example. Indeed, the sheer number of studies on accelerators and the consistency of the empirical findings they have generated suggests that any additional research on this topic would be redundant and, therefore, uninteresting. However, because the findings from these studies overwhelmingly derive from sample-wide averages, it remains unclear whether this positive acceleration effect actually holds for any particular type of startup. While there is no shortage of contextual factors by which we could look for nuances in this relationship, we explore a “who” factor herein. Specifically, given that our level of analysis is the startup, we examine to what extent the benefits of acceleration are a function of the startup's stage of development. In so doing, we employ a generalization and extension design by replicating prior studies that test for an acceleration effect using different measures, analyses, and populations.

5.1. Data To test for a relationship between acceleration and emergence, we use data from the Global Accelerator Learning Initiative (GALI), a collaborative data collection effort by the Aspen Network of Development Entrepreneurs and Emory University (GALI, 2021), which surveys startups at the time they apply to a global network of accelerators and one year later. From 2013 to 2017, GALI collected data on 13,495 startups that applied to 204 accelerators located in 41 countries across the globe. 4336 of these startups completed both surveys and after excluding 42 cases due to missing data, our final sample consists of 4294 (32% of the initial sample) startups that applied to 119 accelerators. This dataset has been effectively leveraged in several recent empirical studies on various acceleratorrelated outcomes (e.g., Assenova, 2020; Lall and Park, 2020; Lall et al., 2013; Uzuegbunam et al., 2021; Yang et al., 2020) and is particularly well-suited for our research purposes as it contains data on both accepted and rejected startups at the time of application and one year later, irrespective of whether they were accepted into an accelerator program or not.

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5.2. Measurement model Katz and Gartner (1988) argue that organizations emerge when they demonstrate intention, establish boundaries, acquire re­ sources, and engage in exchanges. Reynolds and Miller (1992) operationalize these dimensions as committing to the venture, receiving external financing, earning revenues, and hiring employees. Because startups applying to accelerators are, by definition, demon­ strating intention, we follow prior research and operationalize emergence along the remaining three dimensions: external financing, earning revenues, and hiring employees (Tornikoski and Newbert, 2007). Specifically, we measure this variable by coding cases as one if the startup experienced an increase in financing, revenues, and/or employment (Reynolds and Miller, 1992; Tornikoski and Newbert, 2007) from the year prior to applying to the accelerator to the year after applying to the accelerator and zero otherwise. By focusing on increases in each of these emergence dimensions, we are able to determine whether or not acceleration actually accelerates these outcomes.

Our independent variable is acceleration, which we operationalize by coding cases as one if the startup completed an accelerator program and zero otherwise. Our contextual variable is the startup's stage of development, which is intended to assess which startups (i.e., “who”) benefit (or not) from acceleration. We conceptualize this variable as the progress each startup had made toward each emergence dimension prior to applying to the accelerator and operationalize it by stratifying our data into four subgroups (idea-stage startups, nascent startups, emerging startups, and newly-emerged startups) that reflect how many (none, one, two, or three, respec­ tively) emergence dimensions each startup had attained at the time of its application to the accelerator. Table 1 provides an overview of these subgroups.

Because GALI contains data on accelerated and unaccelerated startups, we are able to compare virtually identical pairs of accel­ erated and unaccelerated startups using a vector of matching variables (Abadie and Imbens, 2011). Following recent empirical research on accelerators (Yang et al., 2020), we chose venture- and team-level variables on which to match accelerated and unac­ celerated startups that have been shown to influence both the likelihood of being accepted by accelerators and the emergence di­ mensions noted above. Venture-level variables include the year in which the startup applied to the accelerator (Hannan and Carroll, 1992), the sector in which the startup intends to operate (Wiklund and Shepherd, 2003), the startup's legal status (Hull and Lio, 2006; O'Connor and Raber, 2001), the startup's age, and the startup's intellectual capital (Baum et al., 2000; Nadeau, 2010). Team-level variables include its size (Eisenhardt and Schoonhoven, 1990), educational level (Van de Ven et al., 1984), gender diversity (Torni­ koski and Newbert, 2007), prior accelerator participation (Cohen et al., 2018), and prior management and entrepreneurial experience (Beckman et al., 2007). See Appendix 1 for a detailed summary of the measurement model.

5.3. Analysis and findings We test our hypotheses with propensity score matching (PSM). From among the various matching methods available, PSM, defined as “the probability of study participants receiving a treatment based on observed characteristics” (Li, 2013: 192), is highly efficient because it solves the dimensionality problem when multiple variables are used to match cases (Holmes, 2019). Specifically, it reduces the number of dimensions from the number of matching variables to that of a single score that reflects the probability of receiving the treatment (Rosenbaum and Rubin, 1983). To run our analyses, we use the teffects psmatch program in Stata 15, with the default nearest neighbor matching option, for each subsample, following Rosenbaum and Rubin's (1983) protocol: [1] we calculate the single pro­ pensity score for each observation in the treated group by using the vector of matching variables identified above, [2] we use the nearest neighbor algorithm to 1:1 match the treated and untreated cases based on the “closeness” of their propensity scores, and [3] we determine whether a treatment effects exists between the treatment and control groups.

To assess the similarity of the treatment and control samples, we plotted the probability density functions (PDFs) of both samples on each matching variable to visually inspect their overlaps before and after running the matching algorithm (Austin, 2011). Visual inspections of the PDFs for the full sample for each emergence dimension show that the post-estimated data overlaps extremely well to the raw data for each variable, suggesting that we have well-matched samples. This implies that any differences between the control and treated groups are due to the effect of the accelerator program. We subsequently apply this method to each of the subsamples and observe similar overlap among the matched covariates. Based on these results, we conclude that accelerated and unaccelerated groups are virtually identical prior to entering an accelerator program (Storey, 2000).

We report the results of our PSM analyses in Table 2. The results for the full sample suggest a significant acceleration effect across each of the three emergence dimensions. While consistent with what entrepreneurship scholars have found to date, these results only Table 1 Overview of sample by subgroup.

Full sample Subgroups Idea-stage startups Nascent startups Emerging startups Newly-emerged startups

Number of emergence dimensions achieved

N

Accelerated (treatment)

Unaccelerated (control)

Varied

4294

1071

3057

0 1 2 3

1215 1012 1190 877

278 209 320 264

841 773 843 600

Note: Minor discrepancies between the total number of observations and the number of accelerated and unaccelerated cases are due to missing data.

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tell us about the benefit experienced by the “average” startup. In so doing, they ignore how context shapes this relationship. When we design this heterogeneity into our analytical approach by employing subgroup analysis, we find that which startups (i.e., “who”) actually benefit from acceleration is actually highly dependent upon their stage of development. Specifically, among idea-stage startups, we find no differences between those that are accelerated and those that are not across any of the three emergence di­ mensions. For nascent startups, however, we find that accelerated startups are significantly more likely than unaccelerated startups to (if anything) increase the amount of external financing they raise. Where emerging startups are concerned, we find that those that are accelerated are significantly more likely than unaccelerated startups to increase their revenues or decrease their full-time employment.

Finally, we find that among newly-emerged startups, those that are accelerated are significantly more likely than unaccelerated startups to increase their full-time employment.

5.4. Implications The findings reported in Table 2 demonstrate how even just a few of the solutions proposed above can address the shortcomings of a context-free approach to our research in substantive ways. Specifically, by employing a generalization and extension design with subgroup analysis, we have shown that while prior studies are right to conclude that acceleration can benefit startups, they have yet to acknowledge how dependent this effect is upon context. Thus, despite the fact that academics and practitioners have come to nearly universally advocate the acceleration process, the evidence provided herein suggests that this support may not be true for all (or even many) startups. We believe such findings are both interesting and important. Because our findings stand in stark contrast to the prevailing assumption that all startups will benefit from acceleration, they suggest that the decision to participate in an accelerator should, in fact, be made in consideration of the startup's stage of development (a “who” contextual factor). By revealing this coun­ terintuitive boundary condition, the insights provided by our empirical analysis meet Davis' (1971) criteria for what makes research interesting. Moreover, given the critical role new venture creation plays in economic growth and development and wealth redistri­ bution, coupled with the high failure rates they face in the process (Kirchhoff, 1994), our ability to identify which startups in particular are most (and least) likely to actually benefit from acceleration provides relevant, actionable guidance for entrepreneurs seeking to solve real-world problems, thereby also meeting Tihanyi's (2020) criteria for what makes research important.

6. Conclusion We have argued herein that we as entrepreneurship scholars need not choose between doing research that is interesting and research that is important. On the contrary, we can achieve both ends by acknowledging the foundational role context plays in our discipline and designing our research such ways that enable us to dig beneath the surface of our samples and explore and exploit their heterogeneity. Given the attention that has heretofore been given to what types of theories and/or phenomena scholars should study Table 2 The effect of acceleration on startup emergence: propensity score matching results comparing accepted and rejected startups.

Emergence dimension Sample

N

Financing

Full sample

4294

Subsamples Idea-stage startups No prior financing, revenue, or employees

0.067 (0.022)

1215

Nascent startups Prior financing

0.038 (0.042)

258

Prior revenues

292

Prior employees

462

0.177 (0.082) − 0.006 (0.093) 0.083 (0.059)

Emerging startups Prior financing and revenues

222

Prior financing and employees

253

Prior revenues and employees

715

Newly-emerged startups Prior financing, revenue, and employees

877

Revenues **

0.040 (0.021)

Employment *

0.038 (0.018)

*

0.062 (0.038)

0.050 (0.037)

0.028 (0.075) 0.050 (0.068) 0.043 (0.066)

0.010 (0.093) 0.049 (0.068) − 0.048 (0.056)

− 0.143 (0.080) 0.112 (0.073) 0.045 (0.042)

− 0.083 (0.077) 0.180 (0.086) 0.104 (0.410)

¡0.166 (0.075) 0.036 (0.076) − 0.030 (0.044)

*

0.042 (0.037)

0.039 (0.037)

0.115 (0.037)

**

Standard errors in parentheses. * p < 0.05. ** p < 0.01.

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*

* *

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(Davis, 1971; Pillutla and Thau, 2013; Tihanyi, 2020), we focus our attention on how scholars can actually test them in order to generate more unexpected, counterintuitive, interesting (Davis, 1971) results that can provide more accurate answers to the relevant, real-world, important (Tihanyi, 2020) problems entrepreneurs face. To this end, we propose a (non-exhaustive) list of analytical ap­ proaches and empirical methods that can enable scholars to look past the initial sample-wide averages that most statistical analyses provide in order to explore the nuances that exist beneath the surface of those findings. By contextualizing our research in these ways, we can better understand not only whether a given result is “true,” but more importantly where, when, and for whom it is (or is not) true, thereby increasing the inferential value of our findings.

Of course, we acknowledge that undertaking this approach is perhaps easier said than done. Entrepreneurship research, like that in most other related disciplines, is guided by a somewhat formulaic protocol – [1] justify the research gap, [2] develop, test, and support theory-driven hypotheses, and [3] explain how those positive findings contribute to theory – each step of which faces a hurdle. For starters, conducting replication studies and/or testing contextual hypotheses in well-established areas is often viewed as failing to meet some arbitrarily-defined level of contribution given the assumption that once a relationship has been found to be significant in a leading journal, that is the end of the story. However, as argued above, that an effect holds in one location, at one point in time, and for one sample/population does not mean it holds for all. On the contrary, it may be that other “where,” “when,” and “who” factors shape the relationship in interesting and important ways. Thus, we encourage researchers to frame their research by crafting compelling introductions that justify the need to examine previously un(der)-explored contextual factors that they have good reason to believe ought to affect a relationship that has to date received support based on a limited number of sample-wide averages. This is arguably the most important task of the researcher as such a justification will provide them the latitude to engage in the types of empirical ap­ proaches discussed above without the pressure of having every coefficient in their results table come out significant. Indeed, the fact that journals tend to publish only (or mostly) significant results has long been lamented (Starbuck, 2016). But, the whole objective of context-based empirical research is to find out where, when, and for whom a relationship does and does not hold. Thus, non-findings are a strength, not a weakness, of empirical research as they can help to establish these boundary conditions, which in turn, provide fodder for the interstingness and importance of the study's implications. Scholars often struggle trying to demonstrate how their empirical findings inform theory (Geletkanycz and Tepper, 2012), but this is, perhaps in part, due to the fact that what we tend to study is so narrow and superficial that we rarely explore relationships that might seem unexpected given their misalignment with the theory undergirding our hypotheses. But, when we explore the limits of those theories, we can actually have something interesting and important to say about them.

Notwithstanding the promise of such an approach, enacting it requires a deviation from the conventional approach to science that “the system” has heretofore encouraged (Kerr, 1998: 209). To this end, we encourage reviewers and editors to view the type of research advocated herein with both an understanding of the extent to which extant research based on sample-wide averages may have resulted in a somewhat circumscribed view of a given phenomenon and an appreciation for how digging beneath the surface of those averages can provide more interesting, important insights going forward. Fortunately, there seems to be growing receptivity to the approach we outline. As evidence, recent editorials in the leading entrepreneurship journals (Anderson and Wennberg, 2020; Anderson et al., 2019; Levesque and Stephan, 2020; Maula and Stam, 2020; Parker, 2020), as well as those in management (Hideg et al., 2020), international business (Meyer et al., 2017), and strategy (Bettis et al., 2016), have advocated many of the techniques for which we call, albeit for different purposes, and have, in turn, called on reviewers and editors to be more receptive to them. We are encouraged by the groundswell of support these empirical techniques are receiving as they can invariably help us all do better at generating more interesting and more important empirical research than has been the custom to date and, in so doing, increase the inferential value of our findings.

CRediT authorship contribution statement Scott L. Newbert: Conceptualization, Writing – original draft, Writing – review & editing. Romi Kher: Conceptualization, Writing – original draft, Writing – review & editing. Shu Yang: Formal analysis, Data curation, Methodology, Writing – review & editing.

Acknowledgments The authors thank the Lawrence N. Field Center for Entrepreneurship at Baruch College, City University of New York, for its financial support of this research.

Appendix 1. Measurement model

Variable

Definition

Coding procedure

Emergence Accelerated

Change in external financing, revenues, and employment between the time of the application to the accelerator and one year later Whether or not the startup completed an accelerator program

Application year Sector

Year startup applied to accelerator Sector in which the startup intends to operate

0 = No or negative change 1 = Positive change 0 = No 1 = Yes 2013 to 2017 (continued on next page)

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(continued ) Variable

Definition

Coding procedure

Legal status

Legal structure of the startup

Venture age

Age of startup in years

Intellectual capital

Startup has patents, trademark, or copyrights

Team size Team education Team gender diversity

Number of primary founders Number of startup team members with more than a four-year college degree Startup teams with female cofounders

Team accelerator experience Team management experience Team entrepreneurship experience

Startup teams with cofounders who previously participated in other accelerators Startup teams with cofounders with prior managerial experience Startup teams with cofounders with prior entrepreneurial experience

0 = Others 1 = Agriculture 2 = Health 3 = Information and communication technology 0 = For-profit 1 = Non-profit 2 = Others 3 = Undecided Number of years since venture founding (squared term also included) 0 = No 1 = Yes 1, 2 or 3 (maximum) 0, 1, 2 or 3 (maximum) 0 = No 1 = Yes 0 = No 1 = Yes 0 = No 1 = Yes 0 = No 1 = Yes

Note: Data used to construct all control variables comes from the first survey.

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