Abstract
In Sandra Waddock’s article “Taking Stock of SIM” in this journal, she identifies key issues in the work of the Social Issues in Management (SIM) Division of the Academy of Management. This article challenges her analysis of SIM scholarship and her arguments of what is necessary for the division to progress. Scholarship in SIM should emphasize two key streams: First, scholars in SIM should seek to develop a science of social forensics, design, and social repair—in essence, develop a method of problem diagnosis, an approach to practical solution design, and a systematic understanding of the selection and implementation of social repair—in other words, seek to understand how to systematically troubleshoot and engineer solutions to fundamental issues in the business and society interface. The second stream, which informs the first, involves the development of original, core, transferable systematics that can “travel”—be the source of understanding-generating analysis—in other disciplines, including the topical regions of the Academy of Management. The article argues that laying claim to and developing true normative theory applicable across disciplines should be a distinctive identifier of work in SIM. The article concludes with an illustration of how systematics can be applied to address the literature’s failure to even seek to understand the logic underlying the standard ethical theories. These theories are properly seen as complements rather than substitutes. We need to ask and answer the “fundamental question of business ethics”: What should I do? .We suggest an approach labeled “integrative ethics,” employing ethical frames/injunctive formats, framed contexts for action, and the distribution of desires.
Keywords
In a strong challenge to the current role of the Social Issues in Management (SIM) Division within the Academy of Management, Waddock (2016) sees the Division as losing its place as the primary home to research in the traditional topics of SIM. These central core areas of research have been spreading throughout the Academy, potentially posing a threat to the need for a separate division.
To address this threat, she argues that SIM must return to its “normative roots,” by which she means a return to the SIM represented by the Division’s vision statement. Approved at a contentious business meeting in August 2000, the statement envisioned “a community of enthusiastic, committed scholars and practitioners consciously questioning the social, political, ecological, global, and ethical issues raised by business activities in relationship to multiple stakeholders.” Waddock (2016) recalls “a division historically oriented to asking big questions about the system, critical questions, and generally questions without neat answers or well-constructed theory, or, for that matter, large datasets of quantitative information, behind them.” She argues that “SIM scholars have fallen prey to the same narrowing of research scope and attempts to improve ‘rigor’ . . . that beset the rest of the Academy . . . with implications for breadth of focus and questioning attitude.” “Edginess” has been replaced with “normal science,” which also tends to limit publication of questioning pieces that do not meet methodological hurdles.
I submit that this prescription would be a return to a world that never existed, at least for the Division as a whole, and that, as characterized here, is not a world that SIM should seek to create for itself now in lieu of other kinds of research. The Division’s research was never dominated by scholars asking big and edgy questions, though we have benefited from some who have. Frederick’s decades-long path through a series of corporate social responsibilities (CSRs) might qualify—but Frederick is still here, asking questions, as well as suggesting paths to solutions (Mitnick, 1995). 1 I strongly agree that work of this kind has had extraordinary value to our area and should be encouraged. But at some point, we have to answer questions as well as ask them (and Frederick works on answering them as well). The issue is how our field as a whole develops the means to generate answers, not just edgy questions—that is, to build systematic understandings about business and society. Big questions are asked because the answers are important.
Big Questions and SIM as an Academic Field
Consider the sample list of Big Questions that Waddock supplies in her Table 3. Most of these questions relate to how we can achieve more desirable social and environmental conditions; they are not in general questions that can proceed without acknowledgment of their broad normative content. They presume particular normative stances. For example, she asks, “How can or should the power of corporations, particularly multinationals, be harnessed for the benefit of humanity and the planet?” Although we may be unclear on exactly what she means by “harness,” would specify as “power,” and include under “benefit,” her question strikes a particular normative stance where others would be possible. The alternative stances possible can vary depending on her implied meanings. For example, there are academics who could also ask, “How can we unharness the power of corporations . . . for the benefit of humanity . . . ?” What is it that makes Waddock’s version superior to its opposite? Don’t we also need understanding of how the system works and how we construct normative preferences for one system over another?
Big Questions
So, can we sort the Big Questions and learn something about the structure of what we do not know? Can we sort the possibilities for normative guidance built into such questions to learn something of the possibilities for action that could provide, or fail to provide, real social repair? Can we be systematic with both the questions and the possible answers?
We are dealing with at least, and almost certainly more than, the following list of kinds of Big Questions. Where available, I have sorted some of the questions that Waddock asks in her Table 3 into these Big Question categories:
Existential questions: Does the social world really have a certain character? Is it possible to create certain systems of action in the world? Waddock asks, for example, “What economic systems will work in a resource- and climate-constrained global village?”
Constitutive questions: How can we identify the active components of key social systems, and what exchanges occur within and among them? Waddock asks, for example, “What global governance (government?) frameworks and approaches are needed to manage the global commons? . . . How are the sharing economy, rapid technological substitution of work, and artificial intelligence affecting businesses and societies?”
Integrative questions: How do the perceived key components of the social world work with one another, be reconciled with, or be adapted to other components to satisfy our purposes of inquiry—which may be to understand how they could work together, or simply to develop integrated theories of behavior in such complex systems? Waddock asks, for example, “How do and should wisdom and ethical systems in different cultures and traditions relate to one another? . . . What is the role of cross-sector engagement in business strategies, in corporate social responsibility (CSR)/sustainability programs, and in the purposes of companies?”
Evolutionary questions: What paths can social systems follow to achieve potentially differing future states? How can various interventions promote evolution over more desirable paths? Waddock asks, for example, “How do/can large systems change towards sustainability and greater equity be brought into being? . . . What are companies doing to bring about sustainable enterprise? . . . How can or should businesses relate to growing inequality in different societies or the world?”
Functional questions: How do normative elements function within, and influence, components of social systems? How are desirable/undesirable processes and outcomes obtained? Waddock asks, for example, “What political and regulatory systems work effectively in the global commons? . . . How do we incorporate sustainability responsibility (ethics) into the system, not as an add-on? How can the world, individual societies, and businesses attain social justice along with sustainability? . . . How can or should the power of corporations, particularly multinationals, be harnessed for the benefit of humanity and the planet?”
Methodological questions: What kinds of abstractions, and what methods of inquiry employing those abstractions, can provide us with the level of understanding of normative phenomena that we require? Waddock asks, “How can and do big data affect society and what are the ethics of gathering and using such data?”
SIM as a Fledgling Academic Field
Thus, I argue that Waddock’s unhappiness with SIM’s lack of attention to what she calls the “big questions” about the functioning of business systems in society is very much on target, but incomplete. I would widen the target of such questions to include what the field accepts today as adequate intellectual frameworks to guide our work and, ultimately, generate our understandings of the social world. We should be questioning not only the world as we perceive it but the quality of understanding that we derive from our observations of it. And I would revise her call for a return to “critical” approaches anchored in dismay at the social performance of our business institutions. As scholars, we can and should do far more than be “critical”; we are not fundamentally critics of institutional behaviors and social systems, but, rather, we are creators of the understandings of what generates those behaviors and of the means to repair them. The trick is to effectively join these capabilities.
Thus, in response to Waddock’s challenge, I suggest that SIM, as a fledgling academic field, not an adjunct of the critical studies academy, should emphasize two key streams:
Scholarship in SIM should seek to develop a science of social forensics, design, and social repair—in essence, develop a method of problem diagnosis, an approach to practical solution design, and a systematic understanding of the selection and implementation of social repair—in other words, seek to understand how to systematically troubleshoot and engineer solutions. The term “social engineering” has acquired a negative connotation in its association with top-down, paternalistic, and simplistic solutions to social problems. But, strip the connotation, and the claim that the activities in our field should be both systematic and normatively or solution-driven is as valid as it is in the applied sciences (cf. Mitnick, 1998). That the social world is complex and reluctant to yield to our understanding is hardly remarkable in human inquiry; the capability of humans to solve incredibly complex engineering problems has certainly been validated in recent decades.
The second stream, which informs the first, involves the development of original, core, transferable systematics that can “travel”—be the source of understanding-generating analysis—in other disciplines, including the topical regions of the Academy of Management. Waddock sees the SIM problem in part as other disciplines essentially poaching the study of “our” characteristic research problems while we fail to ask the tough questions. I argue that such a perspective sells the intellectual underpinnings of SIM short. It accepts what our name used to literally mean—an area that addresses SIM, but has few if any independent, developed-here logics or modes of inquiry. It is the same sort of intellectual surrender that has led some scholars to develop an entire stream of work on CSR using logics from economics when it is possible that newly built logics based in, say, responsibility systems, among other conceivable approaches, can perhaps provide a richer analysis. We need to give other disciplines the tools to use, rather that importing whatever the social science disciplines, and other areas of management research, have on the shelf. In essence, we need to invent the powerful systematics that we may apply both to traditional topics and, via the questions Waddock asks us to pose, to the new areas that our tough questioning about society and business lead us. The social and organizational world transcends each of the topical areas of management research. So let us make our own border-crossing theory logics, so that they emerge as tools with power.
SIM, Social Forensics, Design, and Social Repair
What I offer as an alternative to Waddock’s goal is to ally the identification of tough questions about the functioning of society with the creation of the understandings of how social problems are produced and can best be ameliorated. Such an approach forms, in essence, a science of social forensics, design, and repair. That science should be our true forte. The same scholar who can pick apart conceptual fine points and integrate complex literatures as well as assemble the deep descriptive knowledge of applied social settings represented by well-done cases should also be able to do what Lasswell (1970) called policy science. 2
Policy science is concerned with understanding the direct and comparative effects of alternative public policies, and of designing effective implementation and remediation tools using systematic theory and evidence-based analysis. As in the natural sciences, policy science aims for predictive success based on descriptive generalizations supported by attempts at empirical confirmation/disconfirmation. Not only would policies be shown ex post to work or not to work, but, if we know the science well enough, we can design policies that do work. Journals such as Policy Sciences and the Journal of Policy Analysis and Management, which often feature articles that rely primarily on economic analysis, represent the current scholarly realization of Lasswell’s vision, even as that vision has narrowed to use the tools of applied economics.
Indeed, Lasswell’s approach to policy science was criticized at the time and has been criticized since for being top down, simplistic about complex institutions, ignoring issues of politics and of practical implementation, tied to analytic tools rooted in economics and simple policy analysis, insensitive to human cognition/biases and the dynamics of social construction, and so on. Later, after the political science discipline had largely dismissed and forgotten Lasswell’s ambitious approach, a new generation of scholars offered a logically similar, if now far more grounded and contextual approach. The so-called “tools” approach (see also “policy instruments”; on policy tools, see Dubnick, 1979; Hood, 1983; Howlett, 1991; Kneese & Schultze, 1975; Linder & Peters, 1989; Mitnick, 1980; Salamon, 1989; Weimer & Vining, 2005) to policy design sought to compare and contingently assess design alternatives for public policies, with regulation an early focus. For example, incentive means of regulation, such as effluent charges and subsidies, were assessed and compared with directive means, such as standards.
As the literature has evolved, it has become less focused on a fixed set of tools and more on how workable, adaptive, and contextually contingent systems can be made to work effectively, that is, taking better account of the regulation’s embedded context and of the practical ways in which nominally standard tools operate and are adapted in situ, as well as how systems of policy participation function to adapt to and shape policy outcomes (on this approach in regulation, see Ayres & Braithwaite, 1992; an example of joint production is the now expansive literature on coproduction, originally, Whitaker, 1980; on adaptive coalitions in policy systems, see Sabatier’s work, such as Sabatier, 1988). In particular, it became sensitive to how people and organizations actually make decisions (see Sunstein, 2013, on “nudges” and regulatory design, applying the work of Kahneman, 2011, on System 1 and System 2).
Although what we may call the science of social repair is logically parallel to policy science (at least, with respect to modern policy analysis), it should not be limited in the kinds of social science approaches typically used as tools in policy analysis; it should not be seen as a subdiscipline of applied economics. Look at the compelling complaints leveled at institutional and systemic functioning by scholars such as Waddock. Now search in SIM for scholarly efforts to assess and design social institutions that would address those complaints. The literature at large is full of reform complaints and proposals—but too little of it is based on solid scholarship that can advance confident means of repair.
We have been trained as social scientists to seek to develop and find evidence for descriptive theory—in essence, to develop abstracted statements about observed behaviors. We have been warned about doing normative analysis—prescribing the world we think should be. Some of us experience an almost guttural reaction against injecting normative concerns in our research. But we have made a basic error in recognizing such a divide.
As Waddock argues, we should ask tough, edgy questions about the social order; we should work to identify more desirable social conditions. And then we need to do the very practical work of showing how to get there—developing understanding of the conditions that produced the problems, the mechanisms of transitions to better states, and the design and characters of new institutions that would function with more consistency to the ends we seek. Getting there—figuring out social repair—requires hard, systematic, theoretical, and empirical work. Doing SIM means sometimes doing what I have termed prescriptive explanation: “the study and evaluation of the principles of societal operation that produce differently valued future states” (Mitnick, 1973b, p. 1074).
Now, I am not arguing that we should all become policy scientists—far from it. In my view, our primary aim should remain the generation of understanding about the social world. That is scholarship’s fundamental task. But, as Waddock correctly argues, our field historically rose from the belief that by understanding the activities of business in society, with attention to issues of business responsibility, we can provide the intellectual tools to improve those activities. That was its normative origin, and in that Waddock is surely correct. The field grew out of CSR, with the unavoidable recognition that responsibility is a normative term, any way you look at it.
But although most everyone will agree that scholars would not want to seek, in Waddock’s words, “neat answers” to big normative questions, I fail to see why good theory and evidence-backed analysis—indeed, careful policy science—should not be done. It is as if there is a fear that systematic thinking will sabotage the result. We reason all the time from limited bodies of evidence. So if what Waddock means is that we should not be limited by our data in thinking about these basic issues, she is certainly correct. But that does not mean that we should disparage the goal of doing well-grounded analysis.
Consider, for example, the literature on corporate governance, which is full of complaints and proposed reforms (by corporate critics such as Nell Minow), as well as lots of solid scholarship about board behaviors. But can it tell us confidently how to design the peak level of corporate management to not only avoid the Enrons and JPMorgan Chases of the future but also to ensure that such firms perform well at the same time?
An enormous amount of research on boards of directors has accumulated (Dalton, Hitt, Certo, & Dalton, 2007; Johnson, Daily, & Ellstrand, 1996; Pugliese et al., 2009). We have an increasing understanding of things like the effects of different board compositions and of peak manager pay models on firm performance. But, apart from an energetic reform literature, have we really made the jump from science to design? Do we really know how to contingently design a board of directors, much less an entire business firm, that functions as we want it to function?
Moreover, from the perspective of SIM, to what extent do we understand the different ends that different board designs would seek to achieve, and on what grounds particular ends—and, thus, designs—would be chosen? If different ends are appropriate for different kinds of organizations, can we design boards that “fit”?
If boards and management fail to behave as we expect they should, do we have the knowledge to design fixes—can we do social repair? In the conclusion of an article, some of whose themes are not different from Waddock’s, Epstein (2000) noted the Judaic obligation of tikkun olam, to seek to repair or perfect the world, and associated it with what he believes should be a feature of SIM’s scholarly quest. For a SIM Professional Development Workshop (PDW) in 2008 in which leading scholars from diverse areas of SIM participated, I constructed the term social repair, based in the same tradition, to identify the particular application described here—the development of a normative literature comparing the mechanisms of social forensics, design, and social repair. I have seen the language of “repair” or similar phrases, as well as the use of terms like “mechanisms” or “tools” as in the policy design and implementation literature in political science cited above, suggested by others as well (see Margolis & Walsh, 2003; cf. Griffin & Prakash, 2014, on the systematic study of CSR “mechanisms”).
The phrase social repair is intrinsically normative; one cannot repair without a notion of what it means to be fixed. Thus, doing social repair must involve, explicitly or implicitly, attention to conditions of social desirability. We have to know the social status or end state that is judged normatively better than others. That state can, for example, be determined by a variety of social choice mechanisms. It can reflect widely held social norms or expectations of appropriate or legitimate behaviors; it can reflect legal standards or the accumulated decisions of common law. It can be the result of common or legislated law or regulated standards.
Consider the question of who the firm serves. The corporation is a constructed legal fiction. Scholars such as Stout (2012; cf. the “team production model,” Blair & Stout, 1999; Kaufman & Englander, 2005; Kaufman, Zacharias, & Karson, 1995; Lan & Heracleous, 2010; Mitnick, 2009; for a careful analysis of the arguments regarding shareholder wealth maximization, see Windsor, 2010; see also Epstein, 2000) have made a compelling case that the frequently repeated claim that the board has a fiduciary duty to the shareholders such that the shareholder interest has primacy over all others is merely a convenient myth; it has no legal status—it is descriptively false. This “agency” model of the firm, generated out of the work of Jensen and Meckling (1976), and confused with the more general institutional theory of agency that has no such problem (cf. Mitnick, 1973a, 2008; Shapiro, 2005), has acquired a normative status in practice that is completely unwarranted. More correctly, boards and peak managers must serve the firm, not the shareholders ahead of all others. As Stout emphasizes, the shareholders, moreover, are not the owners of the firm; they are owners of shares in the firm, a completely different context, that generates vastly different conclusions about the appropriate design and behaviors for governance.
Thus, the social construction of governing norms makes an enormous difference; it matters a great deal whether the obligation of managers goes to the board alone, to the shareholders’ interest alone, to various or all stakeholders, or to the firm as a whole. And one of the specialties of research in SIM should be the study of governing norms in social settings including the firm. It affects governance designs, regulatory/monitoring designs, and, ultimately, of course, our basic understandings of what a firm is and how it should and does function. So the normative is inextricably tied up with our science. Yet it is also not at all arbitrary and certainly identifiable and capable of systematic study. And, finally, how we decide to design and run one of our most fundamental societal institutions, the business firm, may be different as a result. This is not activism. It is most certainly a “big question.” Management is an applied science, and this is its normative application.
Therefore, in the context proposed here—social repair—SIM is unavoidably a normative science.
Studying SIM: Building Toward Systematics and Clear Theory Logics
To be coherent and acknowledged as a field, SIM scholars have to address important problems recognized within and recognizable as of the field. Consider four characters of the field: the content or topics of study; the influence that research within the field has outside the field; the legitimacy, respect, or acceptance that work in the field has among those with whom it interfaces; and the quality of science done in the field.
Content
Waddock (2016) argues that the field is not addressing important topics. She says it is not sufficiently “critical” in orientation, and it does not address the “big questions” about the design and performance of the business system itself and how to move that system to “a more sustainable and equitable world.” But she also argues that SIM has lost its “questioning edge,” a nice phrase. She clearly claims SIM has moved from what she identifies as its former questioning stance to one that cannot hope to get us to the world that she and, one supposes, most or all of her colleagues hope may someday come. Moreover, she sees the spread of attention to traditionally SIM topics throughout the Academy as a sign that SIM may no longer be a leader in the study of these areas.
Fields can differ in their topical coverage; their modes of or approaches to inquiry, including the theory logics that dominate the structure of explanations; their systematics, including the degree to which concepts/constructs are logically sorted and arguments systematic and even patterned in development; their normative content; and other aspects. Not all of these entities are intended for inclusion in a domain statement, nor would there be room for such a far-reaching analysis of the field. The SIM Division’s Academy of Management domain statement, which is very different from a mission or vision statement, is supposed to simply describe the research topics and approaches found in the Division’s work, as a guide to those who might participate in its activities. It is not a mission or vision statement, nor does it seek to identify what its members “should” be researching.
Waddock (2016) treats mission or values statements as coterminous with the domain statement that the Academy of Management requires divisions to post (see her discussion of the SIM mission statement, the Academy of Management mission/vision/value statement, and the SIM domain statements over time). These statements have differing functions. In early 2015, a years-long process resulted in the adoption of a new domain statement by the SIM Division, modernizing its research language and updating its content. As noted, the domain statement does not and is not supposed to lay out theory logics that predominate in the field, nor common systematics in use, nor offer an extended expression of vision or values for the field. The domain statement of an Academy of Management division is simply supposed to tell you what the division’s work/research covers. A mission/vision/value statement can complement a description of a domain of work, not substitute for it. Waddock has a valid concern in pointing out SIM’s mission statement has languished, and she would perhaps steer the division’s work in other directions (which might indeed lead to an altered domain description, if it actually occurred). But mission and domain statements are differently purposed documents.
The previous domain statement had been written in terms of various overlapping “environments,” a term that in practice means little other than group or context. But there has been a past substantial consensus that work in SIM covers such areas as ethics and corruption, CSR and related conceptualizations, corporate governance, stakeholder theory and management, regulation and political action, sustainability and its management, and so on. With some consensus on the descriptive topics of most existing work in the Division, the issues raised by Waddock concern the expansion or replacement of topical coverage in the Division’s work to address system change issues, the mode of inquiry taken to these topics, the role of the normative in each case, and whether SIM’s topical leadership is being ceded to others.
But what exactly is “system change,” given that it is held as desideratum? Waddock never tells us. I will assume a system change is a change in the basic informal or formal constitutive rules of a system of human or organizational interaction, the “rules of the game.” They operate as a constitution does to shape the competitive structure and dynamics of a democracy, and to shape the electoral system and system of governance permitted. If, as Waddock argues, system change is one of the topics that SIM should be covering, where is the guidance to choose what changes are important or consequential? Don’t we need to work out what we want from a system first before we can study how it can or cannot be changed? How do we know that one constitution is more desirable than another?
Presumably, we identify a system in use as not desirable on the basis of its outcomes. Were we all economists, presumably we would make the judgment of desirability based on observing people willingly choosing the system. We might also judge it on a quality of its process: for instance, that its rules are “fair.” Thus, if the system is fair, yet produces, say, rampant climate change and widespread income inequality, we may judge such outcomes as not necessarily the product of the functioning of the constitutive “system” but of something else. Or, of course, as is possibly the modal case, the performance of the system, in process and/or product (see Epstein, 1979, 2000, on this distinction regarding CSR), is complex. Fair systems can produce miserable outcomes, and unfair systems can have serendipitous positive outcomes.
I have argued (Mitnick, 1993) that “The test of a democracy is not if its rules seem fair, but that its system is contestable” (p. 21). Reasoning along these lines, if we cannot say a priori what is or is not desirable system change for business and society, nor even to be able to agree that its constitutive rules are fair, we may still be able to make judgments based on whether the system that produces such outcomes as inequality and climate change is contestable. And if we can determine that the rules are rigged to defeat challengers, then the system would stand as incontestable and, hence, undesirable.
Indeed, complaints that the system is “rigged” or “captured” or that there is a “thumb on the scale” that biases outcomes toward certain groups in society and away from others, such that some in society never participate in the making of policies that will affect them, is not a criticism foreign to decades of critical writing about the role of business in society. Such criticisms were a feature of the revisionist critique of the model labeled “pluralism” in political science (see Bachrach & Baratz, 1970, on “nondecision-making”; for summaries of the pluralist approach and critique, see Cobb & Elder, 1972; Mitnick, 1993). Waddock (2016) cites the business-centered ills of modern society as evidence that the system—“our businesses, societies, and ecology are in serious trouble, particularly with respect to their potential to continue to support human civilization in the manner to which all might like to become accustomed.” And such a dire and urgent status raises the importance of studying and doing system change. Hence, a reasonable aim for scholarship is to study the contestability of system change.
But system change has never been a large part of the actual research endeavor of the Division, neither in regard to the comparative study of different social systems or the means of organizing enterprise or society, nor in regard to the processes by which such change can be effectuated and implemented. Waddock is on solid ground in arguing that this is an important and relevant topic, but it would be a topic largely new to the Division, not a return to roots. System change is not a change in, for example, CSR practices—from, say, a stakeholder stance framed as engaging in CSR activities serving the community, to one that features sharing work in the community with other social actors, public and nonprofit, as part of a conception of corporate citizenship. The rules of the game are the same: These cases differ in the practices or mode by which the services are provided and in the forms of engagement with the community, not in the fundamental rules by which businesses in society operate.
System change, on the other hand, could involve, for example, changing the mode of corporate governance so that service to the firm, not to the shareholders alone, is institutionalized, rejecting the guidance of shareholder wealth maximization (Stout, 2012; Windsor, 2010). Or it might concern the changes in corporate practices, processes, and products (Epstein, 1979), as well as in society, that are needed to achieve credible and effective management for sustainability, to manage the threat of climate change. Note that these changes would require changes both in practice and in the normative ends held by social actors. Such changes are addressed to the basic rules of the game, rather than to incremental policy changes.
If a policy science approach were taken to such social repair, the analysis of alternative designs would be driven by assessment of effectiveness in achieving the normative ends sought. Design knowledge can advance by experimental additions or improvements or incremental adjustments in the direction of what an engineer would term “goodness.” But the goal of normatively guided system change more or less requires the capability to assess and compare the performance of systems as wholes. The ability to do such comprehensive analysis of complex systems of behavior is of course chimera, given typically limited knowledge and resources. But scholars have long ago moved past both critiques of impossibly global analysis and praise for the practicality of incrementalist approaches (Lindblom, 1959). A design perspective can take human and organizational cognitive biases and resource limitations as starting points for effective designs (see the analysis of nudges and default rules in regulation in Sunstein, 2013).
Influence
The fact that SIM’s topics seem everywhere in the Academy today, as Waddock’s exploration of Academy programs makes clear, should be seen not as a threat that sends the message that SIM itself is becoming irrelevant. Rather, it means SIM is even more central to the domain of the Academy at large. If SIM is only all about the subjects or topics we study, such as ethical leadership or corporate governance or corporate political activity, then we might as well fold ourselves into the other Divisions, following the paths of our topics.
But consider what moves the other way in the Academy: Does the migration of institutional theory originating with organizational theorists whose major home is the Organization and Management Theory (OMT) Division across many divisions of the Academy mean that the OMT Division is irrelevant? Was the migration of stakeholder theory from its most influential statement in Strategic Management, a book by a SIM scholar, Ed Freeman, across the Academy, a lucky, never-to-be-duplicated happenstance? Indeed, I think the exact opposite is what we should work toward. It is not the topics that distinguish us, and that give distinction to a field, but the modes of thinking about the business and social world that are adopted from us and used by others. We influence via ideas that work as tools. If others are poaching our topics, we should worry less than if no one is poaching the ideas that we develop to impart understanding about the world (but cf. the issues associated with “theory borrowing,” Whetten, Felin, & King, 2009).
Thus, Waddock’s fear of irrelevance, once everyone is studying what we are studying, misses the real fear that we should have: Do our ideas have so little power that they can safely be ignored when others seek understanding of the same phenomena we explore? Are we developing powerful new tools that permit generalizable understandings across multiple contexts, or are we only borrowing from the toolboxes of our academic neighbors? The amazing success of economics in colonizing fields far beyond its nominal borders does not mean that resistance is futile, or, indeed, that powerful approaches that abstract the human and organizational experience in different ways cannot be equally as powerful. The most obvious challenge has come from work in social cognition, but SIM is home to normative approaches. There is no social setting free of normative concerns. Yet we have virtually no systematic tools of doing normative theory, a point I will return to below.
Legitimacy
We live increasingly in an academic world in which the value of knowledge is determined by where it is published rather than by the understanding it produces. Critics of the practice are not uncommon (Adler & Harzing, 2009), but reliance on publication in recognized so-called “A-journals” has become a core practice in the evaluation and promotion systems across the Academy. Exacerbating this practice is deference to invalid proxy measures and largely inexpert judges outside the academic system to determine the membership of those A-journal lists. Thus, A-journal list composition is hostage to judgments made by journalists at business publications that publish lists of such journals, and citation-counting organizations that use scale of citation as an (invalid) proxy for intellectual creativity and influence on both evolving knowledge and the field as a whole. Many schools either develop such lists in-house for their own evaluation purposes or use one of the commercial lists offered by publications such as the Financial Times.
Rigid reliance on journal lists seems driven more by school reputational concerns rather than by genuine belief in the lists’ validity. Business school rankings often employ proxies for quality that include publication by faculty in the lists. Thus, the academic enterprise is driven backward; instead of reputation following from recognition of genuine academic contributions, reputational status drives schools to pressure faculty to publish in the proxy journal lists. Hence, research content and quality is entirely irrelevant; all that is measured is whether an article gets in a journal on the list.
Yet valid measures are or can be available. The SIM Division’s Governance Committee formally adopted a white paper in 2012 that offered a scholarly opinion identifying the top journals in our field (hereafter referred to as White Paper, SIM Division, 2012). One would think that in a rational world in which judgments about academic value would be made by judges who are expert in the academic field, that such a White Paper would have immense importance in determining which journals in SIM are commonly considered the best and deserving of inclusion in such “A-journal” lists (suspending for now the more basic concern of whether such journal lists are truly valuable as proxies in evaluation). Moreover, the White Paper’s judgment of the top three journals, Business Ethics Quarterly (BEQ), Business & Society (BAS), and Journal of Business Ethics (JBE), is consistent with journal citation analysis and reputational studies of this area (see review in Beets, Lewis, & Brower, 2016).
Ranking data and judgments typically do change over time. But the principle that should guide any such assessments would not: Judgment of the quality of research in a field, and of the proxies used to evaluate the research, should be the province of the scholars in that field. The closer that ratings get to respecting what those scholars think, the more likely that the assessments would be valid.
Indeed, at this writing, only one of the journalistic A-journal rankings includes even one of the three journals identified by the field as of highest quality (JBE in the Financial Times list). A recent study (Beets et al., 2016) found that the most frequently listed of the three journals, the JBE, appeared on just under half of the business school journal lists in its sample. And that presence is likely strongly shaped by the Financial Times list, that is, by journalists not academics in the field.
To claim validity, business schools compare their lists to those of other business schools, as well as to the lists published by the Financial Times and other publications. But the process is circular—the lists at comparison schools are not independent academic evaluations; they are also influenced by the journalist lists. Because the lists are school-wide, faculty outside given academic areas have important influence on the process, lack the training to do independent assessment of journals outside their own fields, and so are constrained to rely on the external, and invalid, ranking lists. Less diverse, core business school fields with fewer members, such as finance and accounting, find it far easier to identify and gain support for a relatively small group of major journals than the more diverse and larger fields in management. Indeed, there are more total faculty in the management areas of business schools than in all the other business school fields combined (see statistics on division size and total members on the website of the Academy of Management). Yet for internal political reasons, journal list composition tends to be balanced by discipline rather than by rough proportional representation of number of faculty numbers. With the number of journals allowed on the A list per area thus kept limited, business and society journals are bumped by major journals in larger management fields that cannot be practically excluded. That process leads to underrepresentation or complete absence of business ethics/business and society journals—a process that has nothing to do with judgments of quality. 3
Given the critical importance that so many business schools place today on publication in the “list,” any discipline within a business school that is underrepresented in such lists poses difficult challenges for its practitioners. Rewards such as reduced teaching loads, summer support, and salary increases are often contingent on such publication. With greatly reduced opportunities to achieve these rewards, because they lack discipline-focused journals on the list—unlike their colleagues in other business school fields, such as finance, accounting, and marketing, and the management fields of strategy, entrepreneurship, human resources, and organizational behavior, scholars in business ethics/business and society are relegated to second-class status.
Faculty members in some business schools report anecdotally that this discrimination is reinforced by active biases. Colleagues view the area as “soft” and “arbitrary” in content, seeing their own area as a “hard science” using the systematic tools of economics. The not uncommon selection by administrators of individuals with formal training and certification in religion to teach business ethics represents gross misunderstanding of the nature of the field’s content and foments a dismissive view of its status as social science by colleagues in other disciplines. Ideological predilections—sometimes coming from both sides—confuse things further, as good science becomes confused with preferences either for market or for nonmarket solutions, often with absent or weak evidentiary bases. With what appears as great irony to scholars in SIM, faculty in disciplines such as finance and marketing teach their students, include as critical parts of their research, and speak about an alleged legal obligation of firm management to maximize returns to the shareholders, and to thus serve shareholders with primacy. But that is an obligation in U.S. law that does not exist (see Stout, 2012). How can one do science when challenged by fiction? No, not just abstraction—actual fiction. The false claim of legally mandated shareholder primacy appears shaped by ideology, not social science. Faculty identified with SIM are then seen (and sanctioned) as pursuing a marginalized scholarship at odds with the “real” world of business. Their journals are not to be taken seriously, and they are not to receive the same rewards as their colleagues for publishing in their own top journals.
Thus, one of the tasks that scholars in SIM still face is to achieve full legitimacy with respect to other business school areas of study. As long as it is seen as an area determined by a group of particular topics to study, SIM will struggle in its effort to gain respect and peer-discipline acceptance. And if Waddock is correct that these topics are diffusing throughout the Academy, the likelihood of gaining recognition will fade even more. But, as argued above, SIM has failed to develop and export work that ought to be its forte: the systematic study of normative relationships and systems in society (cf. Donaldson & Preston, 1995; Epstein, 2000). We need to lay claim to the normative.
Quality of Science
The quality of science done in a particular field is often judged by its use of methods similar to those used in journals of recognized quality in the home field of the observer. That is, quality elsewhere is defined by what is considered quality close to home. Yes, in SIM, we do see some methods perhaps less used and in some cases even rare: for example, “big data” studies, formal mathematical models, use of some advanced statistical analytical techniques, and so on. On the contrary, some scholars in SIM may well feel like exclaiming, “If I hear another simple and often mediocre observational study rationalized as using ‘grounded theory’ one more time, I will absolutely [insert scatological referent here]!” And philosophy is still a science (a way of “knowing”) done to a significant extent with words. But the SIM methodological umbrella is broad and encompassing, and apart from the component anchored in philosophy, pretty much looks like the rest of management research, and research in social science generally. And it pretty much looks like work in most of the journals we see on A-journal lists. Except that SIM journals are much scarcer on such lists.
Unfortunately, the SIM journal most successful in breaching A-journal lists, the JBE, publishes an incredible 28 issues a year. As an amalgam of three merged journals, JBE hosts articles that range from traditional research studies of the type published in the other top journals in management, to articles on teaching, articles that have reflective or commentary content, and articles that are case or application oriented in key contexts. Pick and choose something that appeared in JBE, and you can find something that perhaps does not look at all like the kind of analytical or empirical research the strangers to our field expect to see in their own flagship journals. Moreover, we would not haul out such useful but not frontline research pieces and claim they contribute in the same ways as the actual front-edge research in our area (much of which is elsewhere in the same journal). And, sadly, to some in the business school disciplines, a view of articles composed of (severe blanching in observer noted) words in Business Ethics Quarterly, a journal that most certainly is not hostage to such a single mode of inquiry, looks to our colleagues as intrinsically not a modern research work.
At the same time, we look over to A-journal-list journals in areas of management that have articles featuring four or five authors that add a variable to a simple model, run a series of trials/variations, do an experimental study through a pool of subjects run out of a University resource center, and go on to the next incrementally different study. They then place the study in one of the A-journal-list journals and add it to their curriculum vitae. However useful in accreting understanding, such work fails to impress as necessarily superior to the quality work in SIM journals. Indeed, we are back again valuing research for where it is found rather than for the understandings it gives us. It is the work itself, not where it appears, or how many authors it has, or what method it uses, that should be determinant of value.
But this is a fight we cannot win—you cannot convince a colleague who judges the quality of his or her research world through the lens of his or her own preferred methods, and his or her treasured journals, that the methods of another field should be accorded equal status. So, what can you do?
Creating Scholarship That Travels
The rather simple answer is to offer ways of thinking about the social world that are so flat-out useful that they cannot be ignored. All research needs what some of us call the “front end.” That end is often devalued, but it is essential none-the-less. If we shape inquiry by shaping the framing and content of theory in the “front end,” our scholars’ work will be cited and respected whenever relevant applications appear in fields nominally outside SIM.
Consider, for example, the impact of Oliver Williamson’s work on transaction costs (Williamson, 1975). He introduced a compelling framework that has had enormous impact on the way institutional economists understand the functioning of exchange relationships within and between organizations. He literally changed the way people think about institutions. It is an abstraction, as is all social science, yet a powerful one, and we can judge its considerable utility by its widespread applicability and the quality of understanding it generates regarding such institutions, even including (if you are not a transaction costs fan) its obvious limitations.
The distinctive character of work in SIM, as well as its comparative advantage were we to offer a prognosis for the field, is its central focus on the normative. We may think of it as a focus on guidance and guidance systems. For example, we need to offer systematic, generalizable approaches to studying the normative content of social institutions, including the normative aspects of such features as exchange relationships, governance systems, and system and network structures—not only individual decision making.
Normative questions are constantly relevant to the governance of societal institutions, including the governance of exchange relationships. How can we understand the normative guides—the “overhead” influences—that impart critical value judgments and implicitly or explicitly direct and shape action? The approaches that provide essential insights into the normative features of society must become part of the research tool base of all disciplines that study such features. If, as we claim, you cannot understand how the thing works without resort to normative systematics, and those systematics are now to be developed in SIM, then SIM’s scholars, and SIM itself, get the “shout-out,” much less the respect, that its home-originated research deserves.
We have for decades worked under what I will call the fear of the normative. This is the descriptive social scientist’s burned-in dread of drifting away from his or her perceived primary task of developing understanding of social behavior via extracting useful abstractions of the complex social world and subjecting them to systematic empirical observation. For example, we study behavioral ethics but we typically take the ethics part as established and, essentially, fixed in place—or, at least, see it as resting in the exogenous realm of philosophers, not social scientists. Moreover, there has always been a divide in SIM between those who feel that social activism is part of their role as scholars and others who feel that social activism may be a consequence of what they learn as scholars, but is not in itself an appropriate part of scholarship. Social activism has been associated with application of normative judgments, so that attention to normative questions has been perceived as evidence of insertion of some inevitably personal and arbitrary social preferences. However one comes down in this debate, the fact is that colleagues sometimes confuse attention (or inattention) to normative issues as evidence of being on the other side of that scholarship divide. But the normative can be addressed as systematically as any other component of human decision making. Involvement in social activism is not the same thing as permitting normative theory and systematics to enter the analysis. Being normative is what humans do and is hence unavoidable as a focus of social science.
Desires and Injunctions
The side effects of the behavioral revolution in social science, which emphasized the study of observable behavioral patterns, classically illustrated by Skinnerian psychology, have lingered. In some literatures, behavioralism, despite its contributions, devalued the study of internal human motivators. As a result, we lack good empirically supported systematics to help us understand how human desires, including preferences for values and ethical positions, shape behaviors. The social science that has arguably had the largest influence on scholarship about management, economics, has had at its core for decades the assumption that we cannot know what humans value except by observing what they choose. Economic actors may maximize their “utility,” a mythical measure of desire. But we can never actually know what is going on inside—what people really, really want and value. Of course, we can posit goals and predict what people with such goals will do if they act with consistency with respect to those goals, that is, if they act rationally. And, of course, we can introduce the whole decision superstructure, including that more recently introduced from the social cognition literature involving such features as risk, discounting, cognitive biases that shape the patterns of choice away from rote consistency, and so on. But the black box itself—the systematics of human valuing—remained largely empty. Or it did, until relatively recently.
Of course, there is a long history of research on values, sometimes generating long and inconclusive lists of potentially overlapping values (cf. Rokeach, 1973). But, until recent work, we could not identify, with empirical support and systematics, the full set of human desires and the related full set of human values. To my knowledge, in current research, there are only two, partially competing, empirically supported value systems, the 16 basic desires of Reiss (2000, 2004; Reiss & Havercamp, 1998) and the 10 values of Schwartz (1994, 2012; Schwartz & Boehnke, 2004). Reiss and Havercamp (1998) observe, “If you want to predict what people will do, find out what they fundamentally desire and predict that they will try to get it” (p. 97).
Reiss’s empirical work on diverse populations of human respondents identified, empirically, what he argued was the full set of terminal or “intrinsic” human desires. Schwartz’s work on values does not necessarily assume they are ends. But, in either case, we no longer have to posit goals—We can actually measure them. As a result, the contingencies of assumption or of use of very limited or proxy measures drop out. We can actually measure which desires, among the full set of human desires, are relatively more important in driving given human actors. Reiss’s system has proven to be particularly powerful in a variety of applications; Reiss (2015) even applied the approach to explain the diverse ways in which people approach religion.
Consider, for example, the question of how to produce a high level of performance in a soccer team (Steven Reiss, personal communication, c. 2009). Some players intrinsically value exercise, which the sport provides; some value competition or winning; some value symbolic status rewards such as trophies; some value praise for good performance; and so on. Of course, some are driven by multiple desires. If we can measure the desires most important to each player, a coach can incentivize players by trying to satisfy what they are seeking to get out of the game. Note that making it possible for people to realize their desires is not cynical manipulation, especially when the joint outcome, winning, is a goal shared by all. The modern theories of desires, especially that of Reiss, allow such measurement.
If we aspire to study the normative systematically, it is necessary to discover what guides people—what they desire. If we cannot link desires to normative guides, we are prey to the charge that our claims that particular injunctive statements do or do not apply and/or are operative in given settings are arbitrary or ad hoc. We cannot explain why anyone’s behavior would follow from normative prescription. Indeed, general opposition to admitting the normative to social science analysis often rests on fears of such arbitrariness: People are just black boxes within which we cannot reach.
But now we can. What if we were able to relate the validated set of basic desires to the diverse ways in which people can approach ethical dilemmas? We would start, for example, by presuming that ethical choices are influenced by what people value—that, per Reiss and Havercamp (1998), people will elect the ethical guides that best serve what they value. Because research can now tell us what that set of desires/values is, it is reasonable to expect that a systematic and powerful theory of how motivation affects ethical choices is possible—It would be part of our general understanding of normative guidance. Such a theory would be capable of “travel,” with applications in many settings.
Going beyond the individual level, can we do more than simply identify individual drivers and actually create a systematic theory of normative governance? What are the contingencies and moderators of normative choice in institutional settings? How do we reference—identify—preferred normative positions in authoritative settings? Let us move away from our sometimes crippling emphasis on the normative as a feature of individual decision making—and construct it as an essential component of understanding the workings of human systems. If we were able to develop a systematic understanding of the normative and how it drives individual, organizational, and systemic behaviors—not just how, say, particular contingencies affect individual decision choices in ethical contexts—we would have a calculus that would travel—that could become an essential part of theory construction in all the divisions of the Academy.
But we also need intellectual work on the other side, the overhead side, of guidance—besides systematic knowledge of the distribution of intrinsic desires in the human actors, we need systematics that permit us to understand the injunctions of ethical systems—the instructions that tell us what we should do. One can argue that observed behavior can be understood as influenced by the distribution of desires, the contexts or contingencies for action, and the normative injunctions placed on situational action. We can now measure, with respect to the full set of such basic desires, what given people value or desire. We can observe context. But we still lack systematic understanding of how people assess what they should do. In other words, we need systematic understanding of the injunctive instructions that express preference for pursuing certain ethical positions—judgments of what is right and wrong, over others.
Identification of the systematics of injunction is what Waddock would call a “big question.” It is easy to complain about an absence of “big question” academic work. But maybe it is absent, at least in some areas, for good reasons—it may be technically difficult, practically infeasible, or require creativity that is so far lacking. The argument might go that we might as well grab the fruit we can reach and enjoy the intellectual nourishment it provides, than struggle for branches waving out of our reach. The orchard is bounded; stay on your property. If it were really possible to figure out how injunction works, why, it would have been done centuries, or, at least, decades ago. But at the risk of overextending a metaphor, I think we need to think about how seeds we plant can grow into orchards everywhere, not just at home.
The Fundamental Question of Business Ethics
To help make the case that systematic and perhaps travel-capable answers are within the reach of SIM scholars, I offer an illustration: I submit that scholars in SIM have done a poor job of addressing what I believe to be the fundamental question of business ethics:
What Should I Do?
What has become institutionalized in our field as supposed guides to answering this question—perhaps rigidified would be a better term—are four or five approaches, all dealing with aspects of moral guidance, that are referred to variously, and with implicit uncertainty about what they actually are, as ethical “theories,” or “perspectives,” or “frameworks,” and similar. They are all taken to be ways of framing the injunctions for attributively moral behavior—that is, they may be thought of as ethical frames or injunctive formats. Just look at our textbooks, which we would expect to abstract, introduce, and make understandable to practitioners that part of the research of our field that we think is useful in training managers. These approaches are generally treated as substitutes for one another. They are introduced as a common class and discussed sequentially. But they are NOT substitutes. Not at all. We are sleepwalking through the most consequential, the absolute core, part of our intellectual corpus.
The Normative System and Ethical Frames
As I have argued elsewhere (Mitnick, 2015), one way to approach this is to look for logical relationships among the ethical perspectives that we have heretofore treated as unique and self-contained. If they are not substitutes for one another, how may they be related? Why did scholarship settle on this set and not another? We suspect there surely must be some underlying logic such that these perspectives somehow span the behavioral space of normative agency—that is, the moral guidance mechanisms that instruct agent behaviors are not an arbitrary list.
These perspectives each have vast literatures that developed over periods of time ranging from decades to centuries, without any real effort—at least, without any cumulating effort visible in modern social science—to see if some underlying logic related each to the other perspectives. To look for any such logic, we need to look to the essential characters of these approaches, which I call theory caricatures—we strip them down to what we claim are the most basic necessary elements, such that if we then remove any additional feature, the caricature arguably no longer has a resemblance to the approach in question. 4 When we do that, we see approaches that include the following simple mechanisms:
Attributed dominant virtues select behaviors or activities consistent with the basic characters of those guiding virtues (virtue ethics).
Moral principles instruct the qualities of outputs that should be produced (deontological ethics).
Net valuations of outcomes or impacts are constructed and inform choices of action (utilitarian ethics).
Absolute evaluations of instrumental or terminal outcomes or impacts are set and applied, and consequently require certain choices of action (rights). 5
Moral principles such as fairness are applied to particular distributions of outcomes or impacts to derive valuation and inform choices of action (justice).
But what is sketched here is implicitly a systems model—from activities/behaviors to performances (outputs) to outcomes. The ethics approaches are not substitutes; they are mostly complements. It depends on how you approach the system of action—which parts and how much of it is subject to ethical judgment in the case at hand, and how that system is perceived by the actor, that is, framed by the actor. By exposing the logical systems structure of the ethical theory caricatures, we make possible the development of an overarching ethical theory of action, what I will call integrative ethics (see Figure 1).
Integrative Ethics.
Thus, you really cannot ask a student (or a practicing manager facing an ethical dilemma)—an exercise common in the pedagogy in our classrooms—to take a given case and discuss the exact same features in the case in turn using each of the ethics perspectives, and assume that the student will be examining that case using five completely different yet somehow parallel flavors of analysis. Nope—it is more like picking up a pear, then an apple, then an orange, then a peach, and then an apple and orange together (justice) and claiming they are all the same because they are fruit. They are not the same. But we should promote understanding that they are all kinds of fruit that complement one another in a fruit salad. While that metaphor may be enough to drive our students bananas, it is not enough to answer the fundamental question, what should I do? Being able to classify does not instruct appropriate action.
Most social situations have aspects of some or all parts of the system process, so we perceive and/or use one or more of the approaches. But our selection of ethical perspective is importantly affected by the fact that we socially construct, or frame, both our ethical judgments and the contexts in which we hold they apply. That framing is affected in all the ways that are increasingly studied today in the literature on framing and social cognition (e.g., Chong & Druckman, 2007; Hallahan, 1999; Kahneman, 2011). Thus, it may appear that we are using the perspectives as substitutes, when we are actually applying contingencies in a variety of contexts, and making framed and attention-directed judgments to choose among complementary approaches. Obviously, our framing may be influenced importantly by what we desire—the particular distributions of values that we hold.
Hence, we need a good, systematic, contingency, and contextually anchored theory or theories that tell us several things: First, we need good descriptive theory of normatively driven behavior. For instance, under what conditions (perceived situations and operative desires), are particular moral drivers (ethical frames) chosen? For example, it can be argued that when known vulnerable populations are severely abused, and actors value social contact and/or family as per Reiss (2004) or are benevolent as per Schwartz (2012), social actors tend to default to deontological drivers, which are absolute, nonsubstitutable, and plenary. In other words, when we care about others, perceptions of their vulnerability drive us to apply (i.e., frame the moral solution as) moral principles to govern our actions (what we should do).
When material losses are observed, and where actors value “saving” (desire to collect, per Reiss, 2004, or other values for which material accretion is instrumental) or value “hedonism” (per Schwartz, 2012), actors tend to default to, that is, frame the appropriate moral solution, in terms of utilitarian referents. But if the losses involve both material effects and differential/distributional impacts on vulnerable populations (such as natural disasters), the default to what we should do is to actions informed by justice—a moral principle is assigned to the observed distribution of impacts from the disaster. In other words, when we perceive such a dire distribution of impacts, we perceive that we must steer aid to those who are severely impacted and unable to help themselves, that is, we see it as the just thing we should do.
In essence, we construct frames of the perceived situation and then choose the appropriate ethical frames of the normative drivers—what would have previously been considered independent ethical theories—that fit those descriptive frames as well as come closest to satisfying our basic desires.
Notice that this approach generates potentially testable propositions about how and which normative guides are used. Per Reiss and Schwartz, individuals are assumed to potentially differ in motivation, so that the assignment of ethical frames is contingent. But we can still generalize on the basis of common patterns of desires, framed contexts for action, and ethical frames/injunctive formats. Thus, our approach can develop actual normative social science theory. 6
The process of teasing out the normative guides that should govern behavior is termed normative referencing (Mitnick, 1995). Although the choice of normative guide is not necessarily hard-linked to action choices (a classic issue in the literature on public policy implementation; see, for example, Pressman & Wildavsky, 1973/1984), we would be coming a long way if we can understand how to construct the “should” in the fundamental question, “What should I do?”
Second, moving in the opposite direction, we need robust normative theory (as well as what could be called mediating or adaptive normative theory—theory that continually adjusts and/or corrects as the nature of the perceived world changes). Laying out desirable conditions in the perceived world, how can we get there? If we seek justice, or to reduce inequality, which actions in what contexts with what desires are most likely to get us to such outcomes? What do we have to learn about the way the social world functions to design a world that works as we want it to work? How do we shape the action and/or design alternatives to best fit the most prominent basic desires of the most relevant actors under particular perceived conditions or states? What Waddock calls for mostly falls in this area; it dominates the list of Big Question topics in her Table 3. But it is only a subset of the Big Questions we need to pursue.
And what would be most useful here, per Epstein’s (2000) injunction and as argued above, would be good theories of social repair. We need to not only ask Big Questions, of many kinds and levels, and as a result be able to provide fundamental understandings of how normative elements work in human systems, but also put on the hat of the engineer—if yet the moral one, unlike the famous manager’s hat that we heard about in the Challenger case covered in most of our classrooms. We should all be moral engineers busy developing the understandings needed to repair the world.
Footnotes
Author’s note
William C. Frederick, who is mentioned in this article and had a fundamental role in shaping research in SIM, passed away in March 2018, after this article was posted by Sage online in final form. He is deeply missed by all who knew him.
Declaration of Conflicting Interests
The author declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.
Funding
The author received no financial support for the research, authorship, and/or publication of this article.