The Relevance of Inequality Research in Sociology for Inequality Reduction

Frame Shifting versus Rational Reconstruction

In the American intellectual community, perspectives on reducing inequality are deeply split. Those with left-leaning political perspectives see inequality as economically inefficient because of large amounts of rent capture by high-earning individuals. These scholars think inequality reduction is just, because people in a rich society have a right to a minimum standard of living and because low-earning individuals were generally deprived of opportunity to increase their skills and incomes. They also see inequality reduction as efficient, because an increase in opportunity for the less well off would have important economic as well as social benefits for the country as a whole. Those with right-leaning political perspectives see inequality as largely efficient, because inequality motivates the most talented to work hard, and fair, because hard-working, talented people deserve their “just deserts” (Mankiw 2013). According to this conservative perspective, inequality reduction is both morally wrong and, beyond limited transfers for poor relief, inefficient.

There are important empirical questions that underly these opposing positions. To what extent are opportunities to obtain valuable skills unequal? To what extent does inequality motivate efficient human and physical capital investment? To what extent are inequalities in human capital investment a consequence of individual differences in motivation, choice, and effort as opposed to structural constraints? To what extent are high incomes a result of productivity and effort compared with inefficient rent seeking? Big questions such as these are relatively easy to state but not as easy to answer.

Answering questions such as these is one of the fundamental goals of sociological research, as it is for large parts of the other social sciences. To develop an understanding of whether and how inequality might be reduced, it is of course necessary to accurately describe inequality and, crucially, to understand its causes. We would argue that most research on inequality takes these objectives as the primary goals. As we discuss later, understanding the causes of inequality does not automatically imply the most effective and achievable paths forward to reduce inequality. At the same time, some of the theories noted above imply to some the infeasibility (e.g., because people have unequal talents and motivations) or undesirability (inefficient and unjust) of efforts to reduce inequality in a serious way. Descriptive and analytical research probes the empirical bases for these theories. When research directly debates and—when the evidence supports—rebuts these frames, and when scholars propose alternative frames for making sense of the body of empirical research, we call this analytical research “frame shifting.”

Frame-shifting research points to the possibility and desirability of inequality reduction, but it does this largely through the quality of its investigation into description and causes and its debate with others who propose different descriptions and different causes. It is a necessary step on the path toward inequality reduction, in part through its efforts to reorient the political debate away from the position that inequality is the fault of individuals or the logical consequence of individual differences. However, we are surprised that social science research does not pay greater attention to how inequality in its multiple dimensions might be reduced, aside from strategies implementable via the tax system or as separate cash transfers connected with existing social welfare programs. Indeed, we would argue that frame-shifting research does not by itself typically provide sufficient research-based guidance as to the shape of these policies even were a decisive political realignment to be achieved. It often, at least implicitly, treats such questions as premature. In its focus on the possibility of change, frame-shifting research too often neglects to examine and therefore address potentially feasible pathways of change.

One does not have to agree in its details with the research program outlined in James S. Coleman’s 1992 presidential address to the American Sociological Association (ASA) (Coleman 1993) to see the contrast it offers to an orientation based mainly on description, explanation, and frame shifting. Coleman’s address focused on what he called the “rational reconstruction of society.” Coleman argued that the societies of highly industrialized nations had been fundamentally transformed by political, social, economic, and technological forces and that these forces had weakened “primordial” social organization based on kinship. Sociology, he argued, needed to recognize that societies of the future will be “constructed,” that the dominant actors of constructed societies (“corporate actors”) are themselves constructed, and that “constructed” social organization is based on “rules, laws, supervision, formal incentives, and sanctions” instead of on the “social norms, status, reputation, and moral force” that controlled primordial social organization (p. 9). The change in the institutional foundations of society dictated that sociology (and by extension, other social sciences) recognize that its task “is not merely to describe and analyze the functioning of society” (p. 10) but also to engage in “the design of organizations, institutions, and social environments . . . intended to optimize relevant outcomes” (p. 14).

Coleman’s presidential address occurred more than 25 years ago. If “optimizing relevant outcomes” in the context of inequality meant “reducing inequality” by one method or another, it begs three important questions. The first question is the extent to which 25 years of additional research on inequality—a core topic of sociological research if ever there was one—has further advanced the field beyond describing and analyzing to fully engage in the task of researching effective ways of reducing inequality that might actually be implemented in real societies. If the answer to the first question is “not as much as might be expected,” then the second question is why has sociological research not moved in the direction called for more than a quarter century ago by Coleman, specifically whether lack of movement stems simply from the enormity of the problem and the strength of opposing political forces. The third question is whether the textbook distinction between “basic” and “applied” research has much to do with the extent of progress toward designing “organizations, institutions, and social environments” (Coleman, 1993, p. 14) in a direction that would read to an achievable reduction in inequality in American society.

Concerning the second question, an obvious response is that the political environment of the United States has not been conducive to inequality reduction, and this response is largely correct as far as it goes. But we suspect that it does not go far enough. One might imagine the thought experiment of an election that realigns the country in a progressive direction. One might imagine that the new president assembles a council of policy advisers. She then asks them how best to accelerate the task of inequality reduction in a way that improves the country as a whole and that maintains political support for the policies that accomplish this goal. Imagine further that the new president stressed the importance of doing things right rather than just doing them quickly, and she cautioned about the dangers—socially, economically, and politically—of doing things wrong. We suspect that her scientific advisers would tell her that they can identify some policies with confidence that would help and that should be implemented quickly and that there are other potential policies that would benefit from further research—both at the level of evaluation research and at the level of what we have termed “feasibility research”—to establish how to (using Coleman’s words) “optimize relevant outcomes.” Over the past 25 years, we have made some progress toward these goals. Where progress has been slow, the lack of sufficient resources for research may play a role. With or without expansive resources, however, we suspect that research goals would be achieved more rapidly when scholars focused attention on what we do not know and would benefit from knowing before more specific policy research is brought to bear to sharpen the optimization.

The argument of this article applies to sociological research on inequality across multiple areas of the discipline. The breadth of inequality research in sociology—even American-focused research—is too great to be covered in a single article. Therefore, we focus on an important segment of inequality research, namely, the segment that focuses on the impact of parents, schools, and neighborhoods on the opportunity for mobility. There are other important topics in inequality research that could be the focus of scrutiny, for example, labor markets, or health or criminal justice, or immigration. However, we also have to set realistic scope conditions for this article. Our purpose is not to do a literature review but instead to analyze what we see as general tendencies in sociological research. We discern the tendencies we discuss below in these other areas of inequality research as well, but we leave the testing of this conjecture to others. Also, although our focus is primarily on sociology, it is important to contextualize sociological research within broader patterns of social science research that addresses these same issues, because these broader patterns provide important information for getting answers to the three questions we pose above.

Social and Natural Science versus Political Consensus

One might begin to answer the questions posed by Coleman’s address in terms of the societal influence, or lack thereof, of social science in general and of sociology in particular. Scholars have studied the questions of whether and how much the formation of social policy is influenced by social science research, and the extent to which the influence of social science varies by national context (Campbell 2002; Campbell and Pedersen 2014; Prewitt, Schwandt, and Straf 2012; Weiss and Bucuvalas 1980). ² To be very clear, these questions are not the topic for our article. Our interest is not in the consequences of social science research, including the reasons why it does not have more influence on the formation of social policy than some might expect. Our concern is with the type of sociological research that is conducted and ultimately published. ³ We focus on inequality research within sociology because of its importance as a social, intellectual, and moral issue, as well as the centrality of this question to the sociological discipline. We are interested in the type of inequality research that gets done, the conclusions it reaches, the implications authors draw from these conclusions, and the frame that they bring to this research concerning the nature of inequality, its causes, and possible solutions.It is of course important to understand the extent to which ideas, including scientific ideas, affect public policy and evidence-influenced politics (Prewitt et al. 2012). Campbell (2002) argued that social policy is formulated as a function of particular paradigms for how the world works and for what the policies are intended to accomplish. Policy also reflects the self-interests of powerful actors engaged in policy formulation, legislative approval, and policy implementation. The frames supporting these policies may be relatively impermeable to even important facts that are discovered through social science research. ⁴ Frames may be controlled more substantially by normative beliefs than by scholarly consensus about facts and causal processes. Perceptions about the extent to which social science influences policy formulation are, as we will argue, a primary force that shapes the type of research that gets done. It is simplistic, however, to argue that a lack of policy influence discourages sociology from conducting policy-relevant research. Instead, we argue that paradigms and frames play a central role in the structure of research, and a primary purpose of this article is to make this connection explicit as a way of making the field more self-aware of the forces that shape its research output on inequality. Although far from a perfect analogy, the example of climate research is instructive about the influence of political controversy on the structure of research. Climate change is in some respects an easier problem to address than social inequality, because an understanding of the main causes of global warming (a principal one being the release of carbon dioxide into the atmosphere from fossil fuel burning) provides a powerful strategy for a slowing of the trend (reduce the burning of fossil fuels). There is also a—perhaps naive—belief that strong scientific evidence about the causal effect of fossil fuel burning on global warming, sea level rise, extreme weather, and so forth, will either now or eventually strengthen the political will to confront the challenge of slowing and/or adapting to the warming trend.

One might see a further analogy between the global warming controversy and the controversy over the hypothesis that cigarette smoking increases the risk for lung cancer. This hypothesis similarly generated huge controversy in large part because both smokers and the tobacco industry had reasons to contest the claim. The resistance of the tobacco industry was greatly weakened by the mounting and ultimately irrefutable scientific evidence that smoking indeed causes lung cancer. It did not then take a complete understanding of the causal mechanisms linking smoking and cancer to generate cancer reducing policies and behavior. The lung cancer example is similar to climate change in that an identification of the major cause implied an obvious preventive strategy: modulate the cause to modulate the effect.

Inequality reduction is arguably a much harder problem. It is less obvious that understanding the causes of inequality in educational or occupational attainment, earnings, or risk for unemployment or poverty produces a straightforward strategy for modulating the consequence of these causes even as this understanding is a necessary condition for identifying strategies that would be effective (Brady 2019). Scholarly research on inequality could have an inequality-reducing effect through the discovery of social facts that point to feasible strategies implementable by individual, collective, corporate, or governmental actors (in the latter case, a social policy implementation) along the lines suggested by Coleman. However, the global warming and smoking analogies point to another strategy by which inequality research might produce inequality reduction, namely, by creating a sufficiently strong consensus around the ideas that inequality (or too much inequality) is bad in itself and produces undesirable social consequences. In other words, research that shifts the framing of the “inequality problem” to a scientific and popular consensus that current levels of inequality are “very bad for society” might have a bigger impact on inequality reduction than would research that probes more deeply into the mechanisms that produce inequality in order to identify new or better strategies to reduce inequality.

There are reasons to be cautious or even skeptical about the potential efficacy of the frame shifting strategy as a sufficient strategy for change. First, the case of global warming shows that an enormous body of scientific evidence all pointing in the same direction might fail to be persuasive. This is especially the case when politically powerful actors perceive a threat to their interests (tobacco companies in the lung cancer debate, the oil and gas industry in the case of global warming, the rich in the case of the debate about inequality).

Inequality is a harder problem than smoking or global warming because much of the political controversy about inequality shades into the question of whether poverty is caused by personal failings as opposed to structural conditions. Inequality is also a harder problem because the evidence for its negative effects on society is not as comprehensive and definitive as is the case for global warming or smoking. There is an at least ideologically powerful argument that inequality does not harm the material circumstances of the nonrich because of an hypothesized connection between inequality and economic growth. As with the controversy about global warming, many working- and middle-class people in the United States see their interests at risk from efforts at inequality reduction via tax policy in an effort (that many of them would see as futile) to benefit low-income Americans. ⁵ These controversies fuel a widely held opinion that social scientists are partisans who underemphasize the role of personal responsibility, morality, and innate individual difference in their criticism of rising inequality. Skepticism about the possibility that social policies can reduce inequality is further fueled by the somewhat distorted collective memory of Lyndon Johnson’s “War on Poverty” in the 1960s as a failure (Bailey and Danziger 2013). Taken together, these considerations call into question the potential of frame-shifting research by itself to affect the political discourse about inequality in comparison—to take a notable example to the extent that Harrington’s The Other America shifted the American conversation about poverty in the 1960s in a productive as well as progressive direction (Isserman 2001). To put it another way, frame-shifting research may (like an understanding of the causes of inequality) be another necessary condition for inequality reduction, but its potential for inequality reduction may itself depend on the existence of sufficient feasibility research to show that acceptable effective strategies for reducing inequality can be found and implemented. Feasibility research is the next logical step beyond research which describes inequality, that provides accurate and comprehensive explanations for its causes, or that critically rebuts narrative frames that would logically discourage efforts at inequality reduction rooted in misunderstandings or misinformation about inequality’s causes.

Feasibility research in our sense of the term identifies and illuminates social realities that either imply strategies for reducing inequality or that provide insight into behavioral or institutional reactions that might impede inequality reduction. Although contemporary policy research focuses on evaluating the causal effects and the costs of implementing specific “treatments,” feasibility research points the way toward designing treatments and other strategies that are likely to be effective. These treatments and strategies are then ripe for pilot implementation and rigorous evaluation as a prelude to implementation via government policy or adaptation by communities and other nongovernmental social groups. The successful design of treatments and strategies requires attention to causal mechanisms, because an understanding of feasible ways of reducing inequality requires an understanding of mechanisms that link existing social realities to inequality or that link possible interventions to a reduction in inequality. However, the focus is less on rigorous estimation of the causal effects of specific treatments than on the design of treatments and strategies that show promise and on the assessment of social, institutional, and financial challenges to the implementation of these treatments and strategies.

One might see an analogy between feasibility research and policy research on the one hand and the design and testing of new drugs on the other. Feasibility research focuses more on addressing questions whose answers would identify or further substantiate the identification of promising interventions and strategies that can later be more rigorously evaluated with follow-up policy research. Feasibility research is analogous to the design of potentially valuable drugs that show enough promise to be taken into phase 1, phase 2, and phase 3 trials. Policy research that uses experiments or high-quality natural experiments to assess the causal effects of a given treatment is analogous to the drug trials that assess the causal effects of a candidate drug. Taken together, these two steps build on high-quality research about particular forms of inequality and their causes to identify promising strategies that may take the form of government policies or of strategies implemented by community and other organizations to reduce inequality in society in its multiple forms.

The distinctions we make between descriptive, explanatory, frame-shifting, feasibility, and policy research do not constitute a system of classification for research studies on inequality. We do not argue that every study belongs in one and only one of these conceptual bins. Rather, we see these concepts as a set of attributes that apply to a greater or lesser extent to the articles and books that report the outcomes of research or that explain to relevant publics what these outcomes mean. Individual studies can and often do have more than one of these attributes. Our argument is that the goal of reducing inequality would be advanced if research projects devote greater attention to bridging the gap between descriptive, explanatory, or frame-shifting research on one hand and policy research on the other. Feasibility research bridges knowledge gaps to facilitate the design of more effective interventions. These designs can then be subject to further research to evaluate their efficacy and cost.

Sociological Dissensus on How to Solve Social Problems

Sociology has had a complex relationship with the question of how social science research can and should be used to address social problems. This complexity arises in part from the history of ambivalence by many sociologists toward state-based solutions to social problems. The conflict over policy research was arguably more intense in the 1960s and 1970s, but it still influences the discipline and the stance toward the idea of “reducing inequality,” even though (it is fair to say) the overwhelming majority of sociologists favor inequality reduction.

Sociology’s ambivalence toward social policy has been one of the major forces that has produced a distinct institutional evolution for sociology compared with economics, which, like sociology, pays a great deal of attention to the issue of inequality (see House 2019 for a recent discussion of this point). Aside from intellectual differences, the organizational structure of the two disciplines is at present very different. Sociology as a discipline is predominantly located in the setting of the university. Within the university, sociology is largely carried out within arts and sciences (A&S) departments of sociology. The most prestigious location for scholarship in economics is also in the university and arguably within A&S departments of economics. But a great deal of economics research also takes place within business schools, public policy schools, and other schools and departments. Indeed, in the typical research university, the number of economists outside the A&S economics department (in schools of business, law, public policy, and elsewhere) probably exceeds the number of economists with A&S appointments. Additionally, economists greatly outnumber sociologists in private policy organizations such as the Brookings Institution, the American Enterprise Institute for Public Policy Research, and the Urban Institute. This much greater anchoring of economics research within academic settings that focus on policy by itself gives a different orientation to the research of the two disciplines.

Even academic economics research gets criticized by researchers in policy institutes as being too out of touch to be useful (Campbell and Pedersen 2014). Nonetheless, we think it obvious that the institutional setting within which research is conducted has an impact on the type of research that gets done. In the case of these two disciplines, one could cogently argue that the differences in their institutional arrangement is a consequence as well as a cause of different orientations toward the relationship between social science and social policy and the relationship between social policy and social change.

This difference is readily illuminated via the illustration of opposing sociological perspectives from the 1970s and 1980s. During the 1980s, Bernard Barber (1988) edited a volume for the Russell Sage Foundation that provided a series of case studies on “effective social science.” In Barber’s view, the tension between social science and effective social science was expressible in the frame that we have already criticized as simplistic, namely, the distinction between “science as pure versus science as useful.” According to this argument, the ultimate justification for science and the highest prestige was reserved for the production of scientific knowledge that led to greater understanding. “Applied” social science was seen by Barber as less prestigious, though he noted that Merton had recommended that sociologists should take applied social science seriously and study the ways it can be used effectively. ⁶ Barber saw the roadblock to be located more in the implementation process, in the priorities of decision makers in terms of their orientations toward policy goals, and the relevance of scientific knowledge in implementing these goals. Nonetheless, Barber’s perspective in 1988 was that social science indeed does affect policy. Other social scientists have noted the source of tension that arises from the question as to whether the state’s interests are aligned with those of social scientists. Weiss and Bucuvalas (1980) wrote in 1980 that

many social scientists consciously reject the role of “technician for the state” and choose to be social critics. . . . They do not look upon government as their natural audience but choose to stand outside and raise fundamental questions about the assumptions and operations of the current order. (p. 2)

A more critical perspective on social policy is illustrated in the writings of Robert Bellah (1982). In a 1982 essay, Bellah commented on the 1979–1980 annual report of the Social Science Research Council (SSRC) by Kenneth Prewitt, the former director of the National Opinion Research Center at the University of Chicago and future director of the U.S. Census Bureau, who was then in his first year as SSRC director. Bellah began his essay by quoting from Prewitt’s opening of his SSRC annual report: “As the social sciences enter the 1980s, they move from a decade in which purpose or relevance became the dominant metaphor into a new decade characterized by the themes of performance, productivity, and usefulness.” Bellah characterized these words “as expressive of the views of the majority of social scientists.”

Bellah (1982) criticized this “majority” emphasis on “usefulness” for what he considered to be its implicit acceptance of the possibility of being manipulated by “the hands of those with political and economic power” (p. 32). He called instead for social science to be guided by what he called “practical reason” rather than “technological reason.” In his view, the most powerful product of sociology is not the production of social technology but rather its ability “to discover through mutual discussion and reflection between free citizens the most appropriate ways, under present conditions, of living the ethically good life” (p. 36) with an emphasis on human interaction structured by norms and a shared conception of what a good society looks like. He contrasted this with what he called the “strategic” paradigm that explains human action “primarily in terms of the behavior of individual persons motivated by needs and drives, chief of which are self-interest and will to power” (p. 37) and that sees this paradigm as an essential element in the development of “technological” social science. In Bellah’s view, many sociologists have been optimistic that “technological social science” could be implemented “on the basis of the normative paradigm,” but he concluded that all efforts to do so have ended in “self-contradiction” (p. 37).

Bellah (1982) argued that the distinction between “practical” and “technological” social science does not correspond to a methodological division between qualitative and quantitative social science but rather to a tension over who the audience is for the products of social science. In his mind, technological social science provides “useful applications” for government and management, whereas practical social science has the public as its chief audience because its goal is to “influence the climate of opinion” (p. 38). ⁷ Bellah concluded that “practical social scientists” “do not claim the degree of scientific precision to which technological social science aspires, partly because they do not think it is possible in the study of human affairs” (p. 39). They do not make claims of expertise but instead see themselves as the carriers of “prudence and judgment” even as they do not see themselves as “strikingly different from or superior to those they address, whether ordinary citizens or decision makers” (p. 39). In many ways, Bellah’s essay anticipates the attention to “public sociology” epitomized by Michael Burawoy’s 2004 ASA presidential address. Burawoy’s (2005) address develops some of the same themes that were expressed in Bellah’s essay, though Burawoy saw what he called “professional sociology” (which overlaps with technological social science in Bellah’s formulation) as an integral part of the discipline that should live in “respect and synergy” with public sociology. ⁸ Two more recent and somewhat parallel perspectives on the relationship between sociological research and the solving of social problems come from William J. Wilson and Herbert Gans. Their perspectives, although different from that of Bellah or Shils, also differ from that of Coleman in their emphasis on frame shifting as opposed to concrete guidance for social policy that flows directly from research findings. Gans (1997), in an essay on sociological “best sellers,” argued that sociology’s support from the public arises from “how informative that public finds sociology, and what uses it can make of the discipline’s work.” He operationalized his measure of support as book sales, even as he noted that many of these sales were to undergraduates for books required in their courses. Gans further argued that “books that try to understand and explain American society as a whole are also among the leaders” and that

most of the books on the list are not empirical research reports, but of those that fall into this category, ethnographies outnumber depth-interview studies and surveys by a considerable margin. This is not surprising, since they are apt to be most readable, to emphasize narrative over abstractions, and to minimize quantitative analyses. Probably the book on the list with the most numbers is William J. Wilson’s Truly Disadvantaged, ⁹ but more completely quantitative studies have no chance in this competition; also, most are published as articles, not books.

Gans ended his essay with the contention that if sociology could produce “more relevant findings and influential ideas about society,” it might be able to attract more popular writers who could report sociology’s work to the general public even as he cautions that the “informational” role of sociology is increasingly “being taken over by talented journalists.”

Wilson’s (2011a) arguments in a recent essay align with those of Gans in many respects. Wilson argued that a scholar’s impact in the national public policy arena “depends on the attention his or her work receives outside of academia, especially in the media. And it goes without saying that a scholar’s insights have to be compelling enough to interest the media and policy makers.”

Drawing explicitly from Gans (1997), Wilson (2011a) went on to note the impact of other books in terms of sales numbers. He agreed with Gans that work that is “too technical and impenetrable to a lay audience, no matter how creative . . . is unlikely to be discussed in the media” and therefore, in his eyes, is unlikely to be influential.

The irony of both Wilson’s and Gans’s view about the need for sociology to become less technical in order to communicate with the general public is that it belies the arguably ever growing influence of economics in American social science despite its highly technical content. U.S. policy analysts and advisers themselves frequently have a technical background, most commonly in economics, and do not find the work of economists to be impenetrable. The communication of technical social science findings in the national media is arguably becoming increasingly common, as perhaps best illustrated by the New York Times venture The Upshot. The Upshot was launched on April 22, 2014, to replace the popular statistical analyses of Nate Silver (who wrote the column FiveThirtyEight and now manages the Web site of the same name) under the editorship of David Leonhardt, who has a BS in applied mathematics and became a specialist in economics reporting (in the column Economic Scene) for the Times in 2000. The Upshot is now edited by Amanda Cox, who has a BA in mathematics and economics and an MA in statistics. The Upshot is very data driven and gives considerable publicity to quantitatively driven research, albeit more detached from any single “public intellectual” author than is the case from the book-driven research of the authors on Gans’s list. The Upshot and similar venues, such as FiveThirtyEight, Freakonomics, National Public Radio’s series Hidden Brain and Planet Money, or Vox.com, offer extensive discussion of technical material in the media. One hears criticism from sociologists (e.g., in Author Meets Critics sessions at the ASA meetings) about sociology books as “inaccessible” because they contain technical material, even though their technical content is often much less than the technical material discussed in the New York Times, the business media, and the Web sites and podcasts mentioned earlier. The reason for this disconnect has to do with the way impact is being measured, whether in terms of book sales and readability by a nontechnical audience, as for Gans and Wilson, or in terms of the level of visibility from translators of technical material by Times reporters such as Leonhardt or Eduardo Porter or Gretchen Morgenson, or Planet Money reporters such as Adam Davidson or David Kestenbaum, or Radiolab reporters such as Robert Krulwich (now retired) and Jad Abumrad, or the policy analysts and publicists at the many American think tanks who have become so prominent in recent years.

We do not argue that Gans and Wilson are wrong to emphasize frame shifting. The question we raise concerns the extent to which “relevant findings” go beyond description, explanation and frame shifting to encompass what Weiss (1977) referred to as “enlightenment” research in a comparison she made between the “problem-solving or social-engineering model of research utilization” and the “enlightenment” model. In Weiss’s view, the “enlightenment model” “sees a role for research as social criticism,” “does not consider value consensus a prerequisite for useful research,” but rather “thinks big,” searches for new concepts and new generalizations, and thereby broadens the range of policy options. Both present-day frame-shifting research and the “enlightenment” research described by Weiss see social criticism as important. However, it is less clear to us how much effort is currently expended by frame-shifting research to develop a broader range of policy options that are tested by and emerge from the research itself. The emphasis is more on disrupting competing frames than on researching feasible solutions—in the sense of making the research on feasible solutions the central focus of the research—that could be implemented if the frame shifting succeeded in substantially shifting the direction of the public and political discourse.

A careful consideration of currently prominent proposals for reducing poverty and reducing inequality shows both that there are many good ideas under debate and that there is plenty of room for feasibility research on additional potentially effective strategies. The recent two-volume issue of RSF: The Russell Sage Foundation Journal of the Social Sciences edited by Berger, Cancian, and Magnuson (2018), “Anti-poverty Policy Initiatives for the United States,” contains many good ideas, but the emphasis is almost entirely on tax- and cash-based welfare policies, including a universal child allowance, a minimum Social Security benefit for older Americans, a public guarantee of a minimum level of child support for children in one-parent households, an increase in Supplemental Nutrition Assistance Program benefits, a renter’s tax credit, a savings component to the earned income tax credit, an increase in the minimum wage, a federal job guarantee via subsidized employment, and additional “race to the top” competitive grants for states to improve their community colleges via accountability based on the earnings of community college graduates. A related recent effort is a 2019 report by the National Academies of Sciences, Engineering, and Medicine, which proposed a roadmap for reducing child poverty (National Academies of Sciences, Engineering, and Medicine 2019). Eight of the 10 proposed policies involve cash transfers or vouchers. The 9th is a training and employment program. The 10th is the proposal that immigrants be given greater access to safety net programs. This emphasis on cash transfers is certainly not an implicit claim that social interventions will not work. Instead, it suggests a lack of clarity about what these social interventions might look like.

When social interventions are proposed, they often lack precision. To take a prominent recent example, the American Enterprise Institute and the Brookings Institution’s Working Group on Poverty and Opportunity proposed a comprehensive strategy for reducing poverty in America (Aber et al., 2015). They proposed to strengthen families to better prepare children for success in school and at work via strategies such as promoting new cultural norms around marriage and parenthood and increasing investment in preschool and postsecondary education. Although these are important goals, they also raise questions that are potentially answerable with evidence-based research. How much is known about promoting and strengthening norms? Can we devise effective strategies for doing so? Are there practical ways of implementing these strategies? The Brookings working group does not answer these questions. These are important examples in which social policies would be more effective if the underlying social science foundation for the presuppositions and proposals were better understood. Much of this foundation would naturally come from feasibility research in sociology.

How Focused Is the Inequality of Life Chances Literature on Reducing Inequality?

As we noted above, inequality research in sociology covers a huge terrain. We focus here on the inequality of life chances, that is, the processes that cause children to have different likelihoods to achieve success as adults. Decades of research confirm five law-like generalizations. First, although family background does not wholly determine adult position, the correlation between position of parents and position of their adult children is considerable, especially near the bottom and near the top of the income distribution. Second, education is the most important determinant of adult status, earnings, or chances of avoiding poverty. Third, family background has a strong effect on educational attainment. Fourth, inequalities by race, ethnicity, and gender exist in educational attainment, occupational attainment, earnings, and wealth net of family background. Fifth, geography matters. A growing body of research indicates that local or regional context has a large effect on life chances.

These fundamental causes of inequality in life chances differ from the fundamental causes of lung cancer or climate change in that knowledge of the causes provides insufficient guidance about how to reduce inequality. Making progress on this goal requires an understanding of the various environmental factors that affect the development of inequality from childhood into adolescence and then adulthood. In the following, we discuss recent research literature on neighborhoods, families, and schools in order to identify the role “inequality reduction” plays in sociological research on inequality in these domains. At the same time, other themes, such as race and ethnicity, are treated in their aspects that overlap with these three themes. We then address the distinction between distributional and relational inequality, how each type contributes to the other, the extent to which research has identified feasible strategies to reduce relational inequality, and the extent to which the reduction of relational inequality is a mechanism for reducing distributional inequality. To state our conclusions at the outset, we find that description, explanation, and frame shifting dominate the research landscape. The counter-examples provide important models for an alternative emphasis, but research on feasible strategies for reducing inequality is underrepresented.

Plausibility, Feasibility, and Practicality

The question of how sociological research—and, more generally, how social science research—is relevant to the question of reducing inequality is a complicated one. This question obviously relates to the broader question about the extent of influence (or lack of influence) that social science research has on social policy and on society at large. Some of this influence (or its lack) is related to the tension between “basic” and “applied” social science. However, as we have argued above, this perspective can be misleading, particularly with regard to sociological research and maybe also for the other social science disciplines. Sociological research is not typically about disinterested knowledge acquisition to improve our “self-understanding of society” (Shils 1980). It is generally reform oriented. But in large part, sociology has not directed itself toward Coleman’s goal of rich research findings geared toward “optimizing relevant outcomes.” Instead, the emphasis on description and explanation, often from a critical perspective, remains the dominant focus, though the explanatory frames are generally not so well developed as to establish feasible strategies. In Michael Burawoy’s (2005) presidential address on the topic of public sociology, he argued that the general “pathology” of professional sociological research was its tendency to focus on the “seemingly irrelevant.” Our analysis of sociological research on inequality does not support this conclusion. Research on inequality focuses on highly relevant issues but is imbalanced toward description, explanation, and frame shifting at the expense of constructive findings that point toward viable strategies to reduce inequality.

The emphasis on frame shifting in the context of inequality research has the potential to undermine flawed, yet politically consequential arguments about the social arrangements that maintain inequality. In this sense, what we have called frame-shifting research is a necessary step toward developing social and political support for the idea that inequality reduction is feasible as well as desirable. But without feasibility research, frame shifting is not enough. Research showing that inner-city neighborhoods are poor because of a lack of opportunity in the local labor market is of scientific importance in countering the conservative argument that the poor are poor because of a self-produced deficient “culture” (as opposed to structural conditions). Research findings that neighborhood effects are large shift the frame away from individual explanations. Research showing that absolute mobility rates have fallen substantially in the United States contributes to the frame that opportunity could be greater. Research that residential segregation disadvantages minority families and is not a condition that they choose supports a frame that desegregation would enhance opportunity and reduce inequality. Sociogenomics research showing a relatively large shared environment effect on the educational attainment of twins (Branigan, McCallum, and Freese 2013; Conley and Fletcher 2017; Freese and Jao 2015) argues against conservative conjectures that, given genetic differences across people, American society may be already be close to providing equal opportunity (e.g., Mankiw 2013). Research on the structural sources of residential instability (Desmond 2016), the psychological consequences of poverty (Mullainathan and Shafir 2013), or the cognitive consequences of the environmental toxins, which are more common in low-income neighborhoods (Aizer et al. 2016), is all further evidence against the argument that the difficulties of the poor are attributed to personal characteristics that are (or should be) under their own control. But each such frame shift begs the question of whether these shifts imply feasible strategies for reducing inequality, what these feasible strategies might be, and what do we need to know that we do not yet know that would get us closer to implementation. The feasibility side of the research is underdeveloped compared with the descriptive, explanatory, and frame-shifting research effort that points the way toward a more just and equal society but does not yet provide sufficient guidance as to how to get there.

What does good feasibility research look like? Many of the studies discussed in this article already point to the feasibility of inequality reduction and thereby provide examples of a research focus on the practicality and durability of positive environmental interventions. One important strategy is the identification of specific causes of inequality that are subject to reversal via the identified causal mechanisms themselves. For example, Aizer et al.’s (2016) research about the toxicity of lead for cognitive development demonstrates the feasibility of closing at least part of the educational achievement gap by abating exposure to lead in the home and neighborhood. To take another example, the extent to which information deficits are a prime mechanism by which inequality in family resources creates inequality in educational attainment points to strategies to reduce the information deficit concerning both high school choice (Corcoran et al. 2018; Sattin-Bajaj et al. 2018) and application to college (Bettinger et al. 2012; Hoxby and Turner 2013; Oreopoulos and Dunn 2013) without taking on the gargantuan task of reducing the inequality in family resources. A third example might be the study of the factors that make for a good school teacher, to determine the feasible strategies for improving less than good teaching, or more generally, shifting the quality distribution of teaching and its correlation with the socioeconomic advantage of students (Kane et al. 2011, 2013).

Another strategy, which gets closer to the standard conception of policy research, concerns interventions that are intended to offset deficits stemming from disadvantage and thereby reduce inequality. This strategy requires sufficient understanding about the nature of disadvantage in order to reduce deficits without necessarily tackling underlying causes that are too politically difficult or expensive to change (e.g., socioeconomic inequality, or neighborhood inequality and racial segregation). The goal is partly to evaluate the effects of a treatment, but feasibility research needs to go further than that. Valuable interventions in the childhood life course must be durable as well as substantively important and practical in terms of cost. The Abecedarian program, for example, was notable for having durable effects on academic performance in contrast to the apparently short-term effects of Head Start and similar preschool programs (Bailey et al. 2017). Evidence about the size of teacher effects or “no-excuses” charter schools or classroom size or tutoring or vouchers for low-income families to move from disadvantaged to better neighborhoods needs to be coupled with evidence about the durability of these effects (e.g., Chetty et al. 2015), as well as the costs of interventions relative to the gains. Dynarski, Hyman, and Schanzenbach (2013), for example, compared experimental evidence on several educational interventions that appear to have positive effects and concluded that providing information about the Free Application for Federal Student Aid (FAFSA) (Bettinger et al. 2012) cost $1,100 per additional disadvantaged student going to college, compared with $133,000 for Head Start, $171,000 for class size reduction, and $400,000 for the Abecedarian program. Their calculations imply that an Abecedarian-type treatment for all low-income children is not a feasible strategy. In contrast, the provision of greater information about high school or college choice may well be feasible. Whether the cost structure of the Harlem Children’s Zone project is more feasible than that of an Abecedarian-type treatment depends on the size of its impact, which is still a matter of debate among academics (Dobbie and Fryer 2011, 2013; Whitehurst and Croft 2010).

Aside from effect size, durability, and cost, feasibility research must also pay attention to the mechanisms by which treatment effects work. Sociological research also emphasizes the relational character of inequality (Desmond and Western 2018; Schwalbe et al. 2000; Tilly 1998; Tomaskovic-Devey and Avent-Holt 2019). This work implies that feasible and effective strategies must also be relational. Consider, for example, the issue of improving the quality of schools. Socioeconomic composition of the student body is a prime determinant of school quality, but large-scale socioeconomic integration is infeasible. No Child Left Behind–type accountability systems had only small positive effects (Dee and Jacob 2011) and widespread undesirable consequences (Jennings and Sohn 2014). The possibility that high-intensity tutoring is behind the positive effects on achievement of no-excuses charter schools (Chabrier et al. 2016) is potentially of great value, but the feasibility of tutoring for inequality reduction depends on how much we know about tutoring and its effects, costs, and scalability. Is it feasible to improve the effectiveness of less than intensive tutoring, for example, through better tutor training, or through the combination of traditional in-person tutoring with online tutoring using (continually improving) educational software? Is one form of tutoring more scalable than another? Does scaling up mandatory intensive tutoring (as in the “no-excuses” charter schools) require the large-scale introduction of “no-excuses” charter schools in disadvantaged areas of the country? Could properly designed auxiliary tutoring services (e.g., including the use of volunteer or work-study college students combined with online tutoring) achieve similar results? Would the latter approach be more scalable? And finally, and assuming that tutoring is effective, why is it effective? The transmission of information is surely a major component but what about the relationship between the tutor and the student? Might these relationships build both interpersonal trust and generalized trust, and thereby help the student in other aspects of the schooling experience as well? More generally, are there feasible strategies of increasing trust between low-income and minority students and their regular school teachers that enhances educator effectiveness (Fox-Williams 2020)?

Knowing that an intervention is financially feasible still leaves important research questions about its feasibility aside from cost. Is it feasible to deliver information about the FAFSA at scale to reduce the information deficit faced by less advantaged children? Are guidance counselors the best delivery vehicle? Should teachers also be engaged in the process of spreading such information? Some disadvantaged parents manage to gain this information through existing institutional sources or through their own social networks (Brown 2017). Do we know enough about social capital processes to enable parents to increase the efficiency through which this information spreads? Are there ways to set up positive feedback loops in communities that increase the density of this information? Might this be connected somehow to collective efficacy?

The situation with respect to the valuable positive identity projects described by DeLuca et al. (2016) is in some ways similar to that of information about colleges, though probably more challenging. Like Duckworth’s “grit,” positive identity projects would seem to have beneficial mobility enhancing effects and could therefore be a source of inequality reduction. Is it feasible to increase their frequency through achievable investments in neighborhoods? Could such investments be enhanced through peer-to-peer transmission or through mentoring to create positive feedback loops? Feasibility research searches for positive feedback loops—the essential mechanism of cumulative advantage processes (DiPrete and Eirich 2006)—that might enhance the agency of lower and middle-income people and communities to improve their situation and thereby reduce inequality.

Collective efficacy offers another possibility for a positive feedback loop. Assuming that collective efficacy really does improve neighborhoods (which perhaps remains an open question), is it possible to improve the collective efficacy of neighborhoods? Is it possible to develop programs to improve relations between the residents of poor communities and the police that patrol these communities? Could these programs raise trust and lower the detrimental impacts of policing on these communities, including offsetting the potentially negative consequences of strained interactions with police on young people’s educational attainment (Legewie and Fagan 2019)? More generally, can sociological research support the development of strategies to desegregate neighborhoods that are politically as well as economically feasible?

A similar issue comes up in the context of the coronavirus disease 2019 pandemic, which has already increased inequality in its differential economic and health impact on racial minority and working-class communities. To reduce the inequality-enhancing impact of the pandemic, the rate of infection and its consequences need to be mitigated. The intervention with the greatest potential is an effective vaccine. However, the impact of this vaccine will depend to a great extent on the proportion of the population who receive it, and current surveys suggest a substantial part of the population does not sufficiently trust the government and the medical establishment to seek vaccination (Gramlich and Funk 2020; O’Keefe 2020). Which social processes can reduce the impact of misinformation? Which social processes can enhance institutional trust especially in light of historical and contemporary racism in the medical establishment? Recent events have demonstrated that there is a great deal that we do not know about how misinformation spreads and the conditions that are sufficient or necessary for it to be corrected.

These types of questions are part of or closely related to policy research. But they are also close to what we typically think of as academic social science research. They focus on description, causal effects, and mechanisms, but in a way that links up social science with the feasibility of change whether through policy intervention or through actions by individuals, organizations, and communities acting individually and collectively. In addition to researching the causes of inequality and its consequences, these types of questions involve research on the causes of conditions and actions that might reduce inequality in order to establish the feasibility of alternative strategies. Feasibility research searches for conditions under which particular actions have positive and durable outcomes, and it seeks to understand how policies or people could produce or enhance these actions in order to harness their potential to reduce inequality.

Are there strategies that could be undertaken that would push sociology in particular but also other social sciences toward the search for feasible strategies to reduce inequality as well as the types of descriptive, explanatory, and frame-shifting research that the field is good at, along with the rigorous evaluation of policies that some sociologists do and that are more common in other social science fields? One change might be to shift the culture of the field in a more optimistic direction so that the “what do we need to know to be able to design more effective policies” becomes a natural question to ask at the end of any study that has enhanced our understanding of a cause of policy. Another strategy is for the field to be more explicit in its reward structure to honor research that brings descriptive or explanatory social science and policy research closer together. Papers in the Annual Review of Sociology that involve inequality should routinely see as their mission a description of recent work that bridges between descriptive and explanatory research on the one hand and policy research on the other. They should also highlight questions without current answers for which additional research could construct additional bridges. We have given several examples in this article. Maybe in the near future the number of possible examples will have multiplied. At the same time, frame-shifting research is critical for building a foundation in the political culture that supports effectively designed inequality-reducing policies. ²² Despite the centrality of frame-shifting research in sociology, there is not overwhelming evidence in recent decades that, by itself, it produces a large impact on society regardless of the political party that controls the presidency or Congress. Perhaps this is because of the increased polarization of our society and the increased disinclination of political leaders to engage in dialogue informed by social science findings. Given the current reality, it is possible that the goals of frame-shifting research would be enhanced if it were more frequently coupled with feasibility research to identify actions that are potentially effective at reducing inequality, even at a local level, enough to matter. If social science could enhance this potential, its research would be simultaneously frame shifting and problem solving, technological and practical, professional and public. This would strengthen social science claims to basic knowledge as well as to practical relevance. Such a state of affairs would not mirror the “optimizing relevant outcomes” mission that Coleman called on sociology to undertake, and it neither would nor should eliminate the healthy tension between problem solving and social criticism that must always remain a part of the social sciences. But it might bring the discipline to a more gratifying as well as socially beneficial place, and that would be a good thing.