Barry Ames, Miguel Carreras, and Cassilde Schwartz
From the perspective of one old guy and two young scholars, Latin American political science looks pretty good. Over the last thirty or so years, our understanding of the region’s political processes, both institutional and behavioral, has advanced rapidly. Political parties, legislatures, elections, civil society; these areas have all witnessed strong research efforts. Credit for much of this advance, of course, goes to Latin America’s latest wave of democratization: political scientists do better in open, competitive environments. But our progress is also due to the rising numbers of well-trained political scientists south of the Rio Grande and to the increasing methodological sophistication of Latin Americanists wherever they are rooted.
Suggestions for future research directions may thus seem both gratuitous and presumptuous. We are emboldened by the certainty that scholarship and fashion are not unrelated: our research choices are inevitably influenced by the reward structure of the discipline as a whole and by the methodological tastes of political science colleagues who are not Latin Americanists. So what follows are some easily ignored observations that could serve, we hope, as themes for debate.
Within the area of contemporary political institutions, we believe that increased research efforts should be devoted to two areas: bureaucracy and interest group lobbying. And although we know a lot about the everyday workings of other institutions, we know less about the formation and transformation of institutions. For such problems we advocate the use of “analytic narratives.”
That Latin Americanists have rarely analyzed lobbying and bureaucracy seems beyond dispute. Could neglect simply reflect unimportance? At least in the case of lobbying, a perception of business weakness may have contributed to the paucity of research, but a deeper and more insidious cause of the neglect of both lobbying and bureaucracy lies in the methodological evolution of the Latin American field. This evolution has an ahistorical, noncumulative quality: earlier methodological approaches—approaches intrinsic to the development of later methodologies—are forgotten when the most current research approaches are transferred to Latin America.
Consider the major institutions of modern government: legislative, judicial, and executive-bureaucratic. Twenty years ago, all three were research deserts in Latin America. The first to emerge was scholarship on legislatures. Early work built on the literature of the U.S. Congress, applying to Latin America such concepts as the primacy of reelection, credit claiming, and pork barrel. Latin Americanists gradually relaxed the assumptions of American scholars, modifying them to fit Latin American reality. In cases like Brazil, for example, the seeking of reelection is far from automatic, and the institutional perspectives that follow from careerism differ from those of U.S. congressmen. Reelection-seeking deputies in Brazil may actually prefer a stronger executive branch so as to facilitate the flow of pork-barrel benefits to their constituencies (Cunow et al., 2011).
In hindsight, applying the insights of U.S. congressional scholarship to Latin America was easy. National legislatures are found in single locations, the internet facilitates data collection, and Latin American presidentialism makes the basic structures of government similar across the continent. Still, the easy development of Latin American legislative scholarship obscured something important: the absence of the “soaking and poking” tradition characteristic of early work on the U.S. Congress. The rational-choice literature on the U.S. Congress, the work of such scholars as Shepsle (1978), Fiorina (1977), Cox and McCubbins (1993) and others, all relied on the deep, qualitative, and inductively empirical tradition embodied by Richard Fenno’s Power of the Purse (1966) and Home Style (1978), John Manley’s Politics of Finance: The House Committee on Ways and Means (1970), David Mayhew’s Congress: The Electoral Connection (1974), and Aaron Wildavsky’s Politics of the Budgetary Process (1964). With a few exceptions, including Ames’s work on Brazil (200) and John Carey’s study of Costa Rica and Venezuela (1996), Latin Americanists have almost never done that kind of inductive and qualitative work. But why? Could it be that scholars whose careers are rooted in U.S. academic institutions naturally find it difficult to spend long periods of time in Latin America? Might new methodologies—both rational choice and narrowly empirical—tend to crowd out old styles of research? And did the shift in methodologies for studying legislatures parallel the general drift in political science from “sociological” to “economic” styles of thinking? Still, in legislative research the absence of qualitative, “soak and poke” analyses in Latin America probably produced not so much incorrect findings as simply limited findings, that is, findings constrained by the research interests of the U.S. rational-choice tradition.
To strengthen the argument that the decline in “soaking and poking” has adversely affected Latin American political science, consider the development of judicial politics, a field clearly enjoying a growth spurt. Most of this new judicial work, as Daniel Brinks’ chapter in this volume points out, focuses on high-level courts, especially constitutional courts. As Brinks notes, “there is very little research on the operation and politics of lower courts, even though it is clear that politics affects them just as much as it affects high courts, and they are crucial to the construction of the day-to-day experience of democracy.” Why so little on lower courts? We suspect that local court systems are understudied because (1) little or no aggregate quantitative data exists about local court decisions, (2) local courts are spread out over entire countries, (3) scholars do not understand how local courts work. Let’s postpone asking why young Latin Americanists are not doing the spade work on either in legislative or judicial politics while we turn to the third branch of government, the bureaucracy.
Do we really need to justify the importance of understanding Latin American bureaucracy? Political science is replete with mentions of “clientelism” and “patronage” (Stokes 2005; Calvo & Murillo 2004). If these ubiquitous ailments really matter, they matter in bureaucracy. Political science journals with titles like “Governance” link politics and bureaucratic capacity. And international financial organizations, including the World Bank and the Inter-American Development Bank, spend serious money on improving “administrative capacity.”
Is the importance of bureaucracy matched by the attention political scientists have paid to it? This handbook has no chapter on the subject. The only major monograph focusing on bureaucracy is Barbara Geddes’ classic Politician’s Dilemma: Building State Capacity in Latin America (1994). Not only was it written seventeen years ago, but it was not intended to analyze bureaucracy as such. Instead, it focused on the conditions under which legislatures pursue bureaucratic reform. For evidence of such reform, Politician’s Dilemma necessarily relied on secondary, mostly historical literature.
During the last ten to fifteen years, the dominant theme in discussions of bureaucracy in Latin America has been the “new public management,” the bureaucratic reform movement that began in Australia, New Zealand and the UK but has spread over Europe and now into developing countries (Barzelay 2002a,b). Articles on Latin America in specialized public administration journals are often illuminating, but usually they share three characteristics: they are delinked from mainstream Latin American political science, they rarely show evidence of field research in any existing bureaucratic agency, and they focus on “bureaucratic reform” rather than “bureaucracy” or “public administration.”
To illustrate these arguments, this section first considers the treatment of bureaucracy in three edited volumes: Ernesto Stein and Mariano Tommasi’s Policymaking in Latin America: How Politics Shapes Policies (2008), Luis Carlos Bresser Pereira and Peter Spink’s Reforming the State: Managerial Public Administration in Latin America (1999), and Eduardo Lora’s The State of State Reform in Latin America (2007).2 Stein and Tommasi have two theoretical chapters and eight supposedly parallel country chapters. The main theoretical chapter purports to be a survey of the major actors in policy making. Legislatures, though their role in policy making is often quite weak, merit sixteen pages of treatment. Bureaucracies get one page, and most of the discussion is about delegation by legislatures. The country chapters reflect this same bias: “we know more about legislative institutions, so they must be important.” The chapter on Argentina has two pages on the bureaucracy (2008: 103–105). The only empirical evidence to support the claim that Argentina’s bureaucracy is inept is the comparison of the “Weberianess” of Argentina’s bureaucracy with other countries. The empirical basis of this claim is Evans’ and Rauch’s “Bureaucracy and Growth: A Cross-National Analysis of the Effects of ‘Weberian’ State Structures on Economic Growth” (1999). Evans and Rauch make quantitative assessments of the quality of national-level bureaucracies, assessments relying totally on individual country-based expert judgments. The methodology seems blissfully unaware of the endogeneity of perceptions of bureaucratic quality to past economic growth and equally unaware that the experts may not be thinking on the same scale. The twelve years since its publication have witnessed little in terms of follow-up research, but it is often convenient, as in Stein and Tommasi, to treat these opinions as real data. The chapter on Chile notes the historically low levels of corruption in Chile and discusses bureaucratic reform post-Pinochet, but it cites no research on the Chilean bureaucracy at all. The chapter on Colombia has two paragraphs on technocrats but nothing on bureaucracy. Chapters on Mexico and Paraguay, chapters written almost exclusively by political scientists, simply do not mention bureaucracy.
Bresser Pereira and Spink are Latin America’s leading normative proponents of the “new public management,” or what Bresser Pereira calls “managerial public administration.” For Bresser Pereira, managerial public administration means
[1] political decentralization with transfer of resources and responsibilities to regional and local political levels; [2] administrative decentralization, through delegation of authority to public administrators transformed into increasingly more autonomous managers; [3] organizations with few hierarchical levels, no longer structured like a pyramid, [4] assumption of limited trust, but not total mistrust by citizens; [5] a posteriori control of results, instead of rigid, step-by-step control of administrative processes; and [6] administration based upon meeting the needs of the citizenry.
(1999: 119)
Bresser Pereira recognizes that these reforms differ from “bureaucratic public administration,” which he labels as a Weberian reform focusing on the principles of professional merit. In his view, Brazil had such reforms beginning in the early twentieth century as a substitute for patrimonial administration, which emphasized nepotism and political patronage. Bureaucratic administration turned out to be not much of an improvement: inefficient, sluggish, expensive, self-serving (Bresser Pereira & Spink, 1999: p. 118). Having tried and failed to improve bureaucracy with Weberian reforms, Brazil is now in the same position as New Zealand, Australia, the United Kingdom, and the United States, that is, among the nations adopting the managerial model.
What is striking about this argument is the complete absence of any evidence regarding the actual implementation of “bureaucratic reform.” Bresser Pereira and Spink cite no research that includes any assessment of changes in the behavior or bureaucrats pre- and post-reform. In essence, the debate proceeds with no empirical footing. And it is not splitting hairs to suggest that perhaps Brazil’s public administration has never quite reached a high level of “Weberianness.”3
In Eduardo Lora’s The State of State Reform in Latin America (2007), Koldo Echebarría and Juan Carlos Cortázar take on the task of putting the Inter-American Development Bank’s country-level research findings on public sector reform into a comparative framework.4 The IADB commissioned studies of bureaucratic quality, with a common framework and quantitative metric, in almost every Latin American country. We learn, reasonably enough, that Brazil’s bureaucracy (in spite of constant corruption scandals) is much higher on both “merit” and “functional capacity” than the bureaucracy of Honduras. But it turns out that Argentina ranks fifth on merit and fourth on functional capacity (of eighteen countries), barely below Chile. Now compare these results with those of Spiller and Tommasi, authors of the Argentina chapter in Policymaking in Latin America: How Politics Shapes Policies (Stein & Tommasi 2008: 103): “One possible way to enforce intertemporal political agreement is to delegate enforcement to a relatively independent, yet accountable bureaucracy. Argentina, however, does not have such a bureaucracy.” Spiller and Tommasi cite Rauch and Evans’ to claim that in “Weberianness” Argentina is below all the other Latin American countries in that sample, including Colombia, Brazil, Mexico, Chile, Peru, Ecuador, and Uruguay. Finally, Spiller, Tommasi, and Bambaci (2007) approvingly cite Graham’s characterization of Argentine bureaucracy: “one of the clearest instances … of an institutionalized, non-performance-oriented bureaucracy in a society with ample numbers of skilled human resources in which the primary interest within the state apparatus is survival” (p. 221). That such contradictory conclusions can be reached by serious scholars suggests that the empirical data and/or the methodology of comparison are inherently flawed.
In addition to the absence of deep and cross-nationally comparable research, the bureaucracy subfield has been distorted by its emphasis on reform. The central problem of electoral research is not electoral reform, nor do legislative scholars focus on legislative reform. Defining development administration as administrative or bureaucratic reform creates a selection bias. The consequence, as Tendler and Freedheim put it, is that scholars fail to provide “the same rich case study material on, or generalizations about, the circumstances under which governments actually do well. Much of the advice about public sector reform is therefore derived from a lopsided understanding of developing country performance” (1994: 1771).
Tendler and Freedheim argue that too much of the conceptual thinking on administrative reform has come from models of rational choice and rent-seeking. Cutting the size of the public sector (via layoffs, contracting out, or privatization) limits the damage public-sector workers can do. Subjecting these workers to market-like pressures and incentives reduces their rent-seeking opportunities. Still, this literature not only ignores the experiences of the Asian tigers, with their greater and successful government intervention, it also ignores the sociological tradition in organization theory, a tradition that emphasizes worker commitment and trust between workers and clients (1994: 1771–1772). Tendler and Freedheim present a case study exploring a program of rural health care in Ceará, a poor state in Brazil’s Northeast. Ceará ought to be a place where clientelism and patronage rule, but the state government successfully implemented a merit-based, non-clientelistic rural health program. The government created a sense of “mission” around its program, and it relied on high levels of worker commitment. Rather than rent-seeking, workers actually took on tasks beyond their assignments. This was not a case of success through decentralization or outsourcing; in fact, the state government maintained centralized control over hiring, training and socialization of its health agents.
Of course, the Ceará rural health program is just a single case, but it does suggest that equal time should be devoted to successful as well as unsuccessful government programs. And ignoring the extensive literature on the morale and commitment of public-sector workers may well be a consequence of ideological blinders.5
The research traditions of organization theory and bureaucratic politics offer a wider theoretical lens for capturing significant characteristics of bureaucrats and bureaucratic organizations. From the organization theory perspective, consider a classic like Herbert Kaufman’s The Forest Ranger (1960). Kaufman sought to understand the U.S. Forest Service, an agency that is necessarily decentralized but maintained a strong organizational culture. By intensely studying five rangers, Kaufman delineates the administrative tools, including recruiting, staffing, reporting, training, as well as socialization efforts and control mechanisms that create the forester ethos and enable the central organization to carry out its mission while remaining flexible. Morale in the forest service was very high, with the rangers feeling they were in charge of their own futures while carrying out their assigned missions.
The Forest Ranger is really a special case of Lipsky’s Street-Level Bureaucrats (1980). For Lipsky, the front lines of state-citizen contacts are the day-to-day interactions of clients with police, teachers, judges, prison guards, and so on. These actors are policy makers because they exercise high degrees of discretion and relative autonomy from organizational authority. The inevitable shortages of resources and the ambiguity of conflicting goals lead to a permanent tension between client-centered goals, organization-centered goals, and social engineering goals. Street-level bureaucrats deal with clients who may be inexperienced or even unwilling, and the external environment is chronically short of money, time, and infrastructure. And though they are hard to measure, managers must set performance goals.
Are street-level bureaucrats relevant to the study of Latin American bureaucracy? Public opinion surveys endlessly ask respondents about their confidence in the police, judiciary, schools, and so on. Imagine how much more useful responses to these questions would be if we actually knew something about the street-level bureaucrats who deliver these services. And imagine the substance in the broad discussions of both administrative reform and the differences between clientelistic and Weberian bureaucracies if we actually knew how patronage employees function in their jobs.6
As we move from the behavior of individual bureaucrats to the behavior of an agency as a whole, we confront the issue of communication networks. Organization theorists understand that even centralized formal organizations cannot work without informal or self-organizing systems of communications. Individuals in a bureaucratic organization create informal structures to try to control the conditions that affect their situation, but these informal structures can undermine the formal ones.
A classic example of this kind of analysis is Selznick’s TVA and the Grass Roots (1966). The U.S. central government established the Tennessee Valley Authority in 1933 as a publicly owned corporation. Ostensibly created to dispose of government-owned factories producing war materials during the First World War, TVA was a quintessential development agency, constructing dams, deepening river channels, and producing and distributing electricity. Because its creation did not result from local demands, TVA had to adjust to the interests of local groups. From the beginning, TVA linked itself to its grass roots, to local organizations, and it used its grass roots theory as a protective ideology (Selznick 1966: 262). TVA became so committed to its local agricultural constituencies that local TVA bureaucrats kept other New Deal programs from operating in their communities, and TVA went far astray from one of its central initial missions, that of conservation.7
TVA and the Grass Roots is the paradigmatic study of cooptation, “the process of absorbing new elements into the leadership or policy-determining structure of an organization as a means of averting threats to its stability or existence” (Selznick 1966: 13). Cooptation can take two forms, formal and informal. Formal cooptation brings people from outside an organization into participatory positions in decision processes and administration. Organizations engage in formal cooptation to legitimize themselves, but this form of cooptation involves no real sharing of power. At times organizations bring in outsiders simply to facilitate administration. Consultation with labor unions, for example, may reduce absenteeism. Though the purpose of this kind of cooptation is to increase efficiency, the process once again may boost the organization’s legitimacy. The second form of cooptation, informal cooptation, is not an attempt to establish or increase legitimacy; rather, it occurs when forces outside the organization are so strong that they have to be conceded policy-shaping power.
Cooptation by local power holders means that policy-shaping influences flow from the grass roots to bureaucratic authority, but influence can flow in the other direction as well. Bureaucrats may successfully pursue autonomy from politicians and political parties. The best example of this approach is found in the work of Daniel Carpenter. In The Forging of Bureaucratic Autonomy (2001), Carpenter examines a series of agencies during the U.S. Progressive era, including the Post Office, the Forest Service, the Interior Department, and the Chemistry Bureau (part of the Department of Agriculture). Of these agencies, some—but not all—successfully legitimated themselves by establishing links to citizens and to their civil society organizations. By doing so, by creating reputations for their agencies of efficiency, expertise, and moral protection, these agencies built autonomy; that is, they were able to enact policies that the bureaucracies’ leaders wanted but that legislators did not.
The concept of bureaucratic autonomy, the idea that bureaucrat-politicians proactively bypass legislators to establish links directly with citizens and their civil society organizations, fits well with traditional arguments in American public administration, but it runs counter to the more recent tradition of “principal-agent” models. In these models, voters or parties control bureaucracies; the former are principals, the latter agents. In the cases Carpenter considers, however, legislators could not control the agencies without incurring unacceptable political and electoral costs, because the agencies were implementing popular policies, policies that the agencies themselves had helped make popular. And since these agencies’ policy innovations occurred long after their original creation, their autonomy cannot be explained by the enacting mix of legislators, parties, and interest groups.
These approaches are important for scholars of Latin American bureaucracy, because they are conceptually more open than the dominant principal-agent models. They assume neither that politicians control bureaucracies nor that bureaucracies always create their own policy space. They see the independent influence of bureaucrats as natural rather than anomalous, but they recognize as well that local interests can deflect the policy designs of national-level leaders.
Latin Americanists have analyzed cooptation processes at very abstract levels, most notably in government-labor relations and with reference to the policies Mexico’s PRI utilized to maintain power (Erickson 1977; Cockroft & Anderson 1966), but the field is bereft of serious research on the relationships between particular bureaucratic organizations and their environments.
The neglect of bureaucratic policy shaping has two possible roots. One is the historic instability of Latin American institutions. When regimes are themselves unstable, intra-institutional and institution-society relationships may be considered secondary or tertiary issues. Bureaucratic policy autonomy has also been neglected because of the influence of U.S. scholars, who typically assume that bureaucratic organizations are simply creatures of the legislature and the president. In the dominant perspective, the perspective of delegation, voters, parties, legislators, and presidents are “principals”; bureaucracies are “agents.” Such models have no room for an initiating, policy-shaping role on the part of already existing bureaucratic agencies.
Whether Latin America’s democratic regimes continue to stabilize, and whether Latin America’s civil society organizations continue to develop, scholars of bureaucracy must maintain an open, unbiased theoretical framework, one that allows for reciprocal influences between parties, legislators, and bureaucratic organizations. Bureaucratic leaders in Latin America may in fact rarely build policy autonomy, but at least the possibility remains open. Indeed, prime candidates for bureaucratic policy shaping exist: consider the influence of Brazil’s agricultural research and extension agency, EMBRAPA. Established by the military regime as a public corporation in 1973, EMBRAPA has played a crucial role in the rapid expansion of the Brazilian agricultural export sector (see, for example, “The Miracle of the Cerrado,” 2010). A principal-agent explanation might explain EMBRAPA’s inception—its bias toward large-scale agriculture fit the predispositions of the military regime—but EMBRAPA has thrived during every subsequent democratic administration as well, including the administrations of the PT. Its imported strains of grass have transformed unproductive areas of the Northeast into export platforms, and it successfully lobbied for the adoption of genetically modified plant strains over strong opposition from the PT’s more radical factions and the environmental left. EMBRAPA’s policies have created a class of large-scale farmers who depend on its research programs (but not on state subsidies). The politics of EMBRAPA remain an untold story, but the case for bureaucratic autonomy seems strong, and we suspect that similar cases exist across Latin America.
Curiously, the linkage between U.S. and Latin American legislative scholarship has no parallels in the area of lobbying and interest groups. Interest group behavior has received little attention by Latin Americanists despite its obvious importance in policy making. This section begins by reviewing evidence of interest group influence in Latin America. We then provide some guidelines for further research, focusing on both theoretical and methodological avenues for advancement.
Research on lobbying in Latin America has mostly dealt with business and agricultural interests. Karcher and Schneider’s chapter in this volume, which provides an excellent review of the literature, concludes that the study of business lobbying has suffered from benign neglect. “Research on business politics is first characterized by how little there is. Beyond scarcity, research on business politics suffers from some biases and blind spots.” Neglect, clearly, and, we would agree, perhaps a biased neglect.8
In order to help explain the absence of interest group literature, we examine one important case of an interest that has been pushed aside: business interests. Because business associations in Latin America have seemed largely incapable of solving their collective action problems, and because at times state actors have stimulated or initiated organized business behavior, Latin Americanists have mostly downplayed the role of business interests and agricultural interests in policy making. Indeed, some authors actively dismiss their importance, especially pre-liberalization. Bates and Krueger (1993) and Haggard and Kaufman (1995) contend that business associations played very small parts in the ISI-liberalization transition. Bates and Krueger in particular argue that business associations were too fragmented to be powerful. As a result, technocrats and political elites were the primary actors throughout the economic transitions of the eighties and nineties.9 Durand and Silva (1998), accepting the weakness of business, look for less direct means of influence, such as agenda-setting and demand-raising. Because business associations were initially organized by and became largely dependent on the state, business was sometimes regarded as a basically passive, state-dependent actor, an actor allowing the state and its technocrats to dominate public policy (Schneider 2004).
Perhaps business influence in the policy process really is something new in Latin America. Some scholars argue that the corporatist structure of Latin American states during most of the twentieth century led to a dependent relationship between interest groups and regimes, and it was precisely the transition between ISI and neoliberalism that activated interest groups vis-à-vis the state (Frieden & Stein 2001; Mancuso 2007; Collier & Handlin 2009). The renewed autonomy of business interests left business more empowered vis-à-vis a state inexperienced in dealing with international competition, but it also left business more vulnerable, unable to depend on the state to protect its interests against foreign competitors. Thus business was simultaneously more capable of influencing the state and more motivated to do so.10
Whether or not organized business and agricultural interests were really weak in the era of ISI, there is considerable evidence that they are weak no longer. Signs of successful lobbying—mostly by business interests, but some agricultural interests as well—come from a wide variety of countries, a variety suggesting that most Latin American countries probably follow suit.
Chile is important because it has the longest history of uninterrupted neoliberal policies. Benedicte Bull’s (2010) interviews with Chilean businessmen revealed that they felt they had played central roles in policy making, particularly in the negotiation of free trade agreements. Chilean businessmen actively negotiated policies typically opposed by business (especially regulations of labor and the environment) in order to gain increased market access.
Interest group research in Central America has also shown substantial business influence. Indeed, small countries sometimes depend on the expertise and knowledge of businessmen when forming agreements with powerful countries like the US, countries that would otherwise dominate the negotiation processes (Carrión 2009, 2010). Local business interests pressured for the privatization and deregulation of telecommunication sectors in Costa Rica, Guatemala, and Honduras (Bull 2004). Perez-Aleman’s (2010) analysis of the Mexican and Central American coffee industry confirmed the significant influence of small business interests through NGOs and transnational organizations.
Interest group politics in Colombia has long revolved, not surprisingly, around coffee.11 Jaramillo, Steiner, and Salazar (2001) demonstrated that Colombia’s coffee producers have been a strong and vocal interest group throughout the twentieth century. Before the 1990s, the producers focused on maintaining the domestic price of coffee in order to control their incomes directly. Post-1991, their strategy shifted from strictly domestic concerns to a defense against international competition through the exchange rate. Though the goals and methods of coffee producers have changed, they have always had an important voice in politics.
Since the mid-1990s, Francisco Durand has dominated, through research relying on interviews, news monitoring, and secondary sources, the study of Peruvian business interests. In his most recent publication, Durand argues that in the 1990s business “captured” the state and has maintained strong, decisive influence over policy making in both authoritarian and democratic regimes. He argues that this level of power is problematic for all actors involved, including business actors themselves, who suffer from notorious reputations and a confrontational political environment. Though political regimes have changed drastically, the role of business has remained consistently powerful (2010).
Though scholars have portrayed Brazil as a country where business wields little political influence (Bartell 1995; Durand & Silva 1998; Schneider 2004), Brazil has the most developed interest group literature in Latin America. Wagner Pralon Mancuso’s O lobby da indústria no Congresso Nacional: Empresariado e política no Brasil contemporâneo (The industry lobby in Congress: Entrepreneurs and Politics in Contemporary Brazil, 2007) is surely the most thorough account of interest group influence. Mancuso argues that business began to involve itself heavily and successfully in policy negotiations after Brazil opened its economy. He succeeds in identifying political pressure in both official and informal settings, in part because business interests are unconcerned with hiding their motives and behavior. By using the Agenda Legislativa da Indústria, published annually since 1996, and by sending out questionnaires to industries involved in the RedIndústria, Mancuso documents the influence of business groups at various points in the policy-making process: proposals, formulations, discussions, and decisions.
Demonstrating that business has political influence is hardly a trivial undertaking, but the study of interest group politics needs to progress. The field should focus more broadly on interests and organized interest groups, not simply on organized business. A wider lens reveals that the precise definition of interest groups varies greatly, and few interest group characteristics are accepted by all scholars (Leech & Baumgartner 1998). A very restrictive definition centers just on groups actively applying pressure on policy makers through lobbying (Crawford 1939). Broader definitions take in both associations and individual firms (Key 1964), and some scholars adopt a sociological definition that includes all groups open to voluntary membership (Knoke 1986). In this perspective, interest groups may include organized social sectors in the population, social movements, institutions like corporations and government agencies, or individual lobbyists.
Latin American research on lobbying seems continually to ask different versions of the same question, i.e., “Do outside interests affect policy content”? If a research question poses a simple dichotomy between influence and no influence, there is little room for comparison, little room, that is, for asking how influence varies between countries or time periods. We need more analytic questions: How do interest groups work together? Under what conditions do they affect the content of policy? At what stage of the policy-making process do they have the greatest access?
Consider the development of the American interest group literature. U.S. interest group research mainly began with the assumption that groups were the most powerful actors in the political process (Bentley 1908; Truman 1951; Schattschneider 1960; Dahl 1961; Lowi 1964). Over time, more nuanced theories placed organized interests within a context of institutional and electoral influences. Americanists now focus on networks between and among groups, the biases and normative implications of organized interests in policy, and the ways groups influence legislation.
Of course, Latin Americanists should not blindly imitate U.S. scholars. Americanists focus on interest group influence over the legislature; Latin Americanists are more likely to stress influence over the executive (Oliveira & Onuki 2007; Batista Araujo 2008; dos Santos 2008). Still, American theories provide some hints about useful questions, questions beyond the “yes” or “no” of group influence.
Do Latin American groups intertwine to build professional networks? Analysts of American interest groups established long ago that groups often do not behave as individual actors; instead, they overlap and cooperate (Truman 1951; Rae & Taylor 1970). In The Hollow Core, Heinz et al. (1993) implement an extensive series of interviews to identify an intricate web of inter-group networks. Similar groups within particular policy areas work together, but no single lobby connects all the groups. As the name Hollow Core suggests, a sphere with a hollow center spatially represents lobby networks. This pattern occurs, the authors suggest, because client groups distrust mediating brokers, brokers who might work with opposing groups.
Lobbyists are political actors who connect with outside interests and politicians. Network methodologies illuminate these connections by analyzing the conditions facilitating network density, creating partisan divisions, and forming cliques.12 Network effects determine cooperation between interest groups even when controlling for group preferences (Carpenter, Esterling, & Lazer 2004).
Precisely because Latin Americanists know little about the basic structure of interest politics, network analysis could be productive. Do lobbyists work alone or in professional networks. With whom do they network? How do professional networks, when they exist, affect lobbying tactics and policy outcomes?13
Since the Federalist Papers, American scholars have worried about bias, about the detrimental effects of particular interests on broad policy making. Do particular interests add “a strong upper-class accent” to legislation (Schattschneider 1960: 35)? An empirical response requires extensive knowledge of the groups involved in a policy area, their constituencies, and their membership incentives. In the United States the response has led to a clear conclusion: major sectors of the population are blatantly unrepresented, and the collective-action problem is a real concern for groups producing public goods (Strolovitch 2006; Yackee & Yackee 2006; Schlozman et al. 2008; Schlozman 2010). This conclusion should be tested in Latin America as well. What are the implications of interest group influence? Which voices have the most sway over policy?
Some groups function more as information conveyers than as policy makers, and this divergence in goals can yield divergences in lobbying strategy. Because most lobbyists spend their time with legislators who already agree with them, persuasion effects may be minimal (Bauer, Pool, & Dexter 1963; Leech & Baumgartner 1998; Hojnacki & Kimball 1998). Measures of interest group pressure should include the roles that groups play as informers, policy monitors, and momentum builders teaming up with like-minded legislators (Ainsworth 1997; Heaney 2006; Baumgartner et al. 2009). When legislators trust an interest group to supply them with policy details and information, the group has more space to shape the policy-making process (Burstein & Hirsh 2007). And, of course, groups influence policy through manipulating public opinion (Danielian & Page 1994; Berry 1999; Smith 2000). Examining the varying roles of interest groups would be particularly fruitful in Latin American countries, where some scholars are hesitant to believe that interest groups directly influence legislative negotiations.
Interest group research requires fieldwork beyond interviews and lists of registered groups. Interest group scholars attend committee hearings, content analyze news articles, and document the progress of bills. They follow prominent issues along with those unnoticed in the policy-making process.14 Perhaps these techniques seem obvious, but the modal style of Latin Americanists is quite different. Most Latin American interest group research has been retrospective. An outcome occurring as the result of noticeable business influence, ipso facto, becomes evidence of interest group pressure. Not only does this build in selection bias, but what happens during the negotiating process is harder to determine retrospectively.
Without question, implementing these research strategies in Latin America is difficult. Perhaps as a result, most Latin American interest group scholarship has been based on secondary sources and small numbers of interviews.15 Research on American interest groups, by contrast, typically incorporates hundreds of interviews or probability-based surveys of lobbyists and related government officials. With such techniques, scholars can begin to understand the structure of a network of lobbying and the ways in which individuals work together to influence policy.
Of course, the availability of high-quality, credible data facilitates the research process. The U.S. law requiring registration of lobbying activity and campaign contributions led to a huge amount of empirical work. Scholars use these data to test, for example, the consequences of and strategies behind campaign contributions.16 Latin Americanists, on the other hand, have not been blessed with similarly accessible data. Nonetheless, Brazil, Chile, and Colombia have begun to require most lobbying activity to be made public, even to the point of recording financial contributions. Recent work on Brazil, for example, utilizes archives of lobbyists registered in the Chamber and Senate, campaign contributions recorded in the electoral tribunal, and the lobbying initiatives found in the Agenda Legislativa da Indústria.
Treat official lists of registered interest groups with caution. Luis Alberto dos Santos used official lists to compare the regulation of interest groups in Brazil and the United States, but his examination of Brazilian regulation comes with a disclaimer: “The paucity of records, which results from the incapacity to regulate their activities, or the low number of registered groups in the House or the Senate, hides the existence of interest groups and makes it difficult to measure their dimension using these data” (dos Santos 2008: 419). Some newer Brazilian work uses the campaign data base maintained by the Tribunal Superior Eleitoral (dos Santos 2008; Lance 2010), but David Samuels, who organizes these data on his website, estimates that the TSE files contain only about 25% of all contributions; the other 75% is the famous under-the-table “caixa dois.”17 In sum, official lists do exist, but with limitations.
An alternative research strategy—one requiring no pre-existing data base—involves following a single set of issues over an entire policy cycle. Peter Van Doren’s Politics, Markets, and Congressional Policy Choices (1991), for example, focuses on energy policy. Van Doren monitored news, conducted numerous interviews, observed legislative proceedings, and analyzed formal documents. Obviously no single issue is “representative”: issues should be chosen deliberately, with a most-different or a most-similar strategy.
In sum, interest groups in Latin America are understudied. One source of this neglect comes from the belief—largely unsupported by research findings—that interest groups, especially business groups, have been weak. A second cause has been the framing of research questions. Too often our questions have been dichotomous: “Do interests affect policy?” Fortunately, methodological innovations from the U.S. context, innovations like network analysis, can help Latin Americanists contribute to the study of interest politics in a comparative framework. Still, the biggest constraint on understanding Latin American interest groups remains the paucity of empirical research, whether quantitative or “soaking and poking.”
Would the study of Latin American politics benefit from the use of analytic narratives? This section begins by defining the concept of “analytic narratives” as a branch of rational choice institutionalism, a branch Latin Americanists currently ignore. We then briefly distinguish between this approach and historical institutionalism. Finally, we explore potential avenues for research that would benefit from the use of analytic narratives.
Rational-choice institutionalism (RCI) puts institutions at the center of research methodology. Institutions limit the array of choices available to individuals in the political arena. They serve as a script determining the rules of the game, i.e., which players can participate in a given political game, what strategies are available for the actors involved, in what sequences the players can develop these strategies, and what sorts of information actors possess when they make their choices (Shepsle 2008; Weingast 1996). The development of RCI has led to many fruitful applications contributing to the study of structured (i.e., formal) political institutions.
RCI has often been criticized on the grounds that it presents institutions as a given set of rules affecting outcomes but fails to provide an accurate explanation of the creation of these institutions. This criticism, of course, is a serious one: if institutions simply reflect preexisting informal practices, then serious endogeneity problems threaten RCI (Weyland 2002).18
“Analytic narratives” provide a new framework to study the creation and evolution of political institutions, a framework that specifically addresses RCI’s limitation by analyzing the moment in which the rules are set. In other words, this approach explores the sources of institutional arrangements. It is narrative because it traces the historical process leading to the outcome of interest. The focus is always on explaining a specific outcome—institutional formation or institutional change—by conducting an in-depth investigation of the context in which the decision process is embedded. Analytic narratives identify the relevant actors participating in the process, the interests and the resources of each actor, and the way in which the actors’ choices led to the outcome of interest (Bates et al. 1998). Although analytic narratives provide micro-level explanations, the actors involved in the processes of institutional change are not necessarily individuals; they can be social groups, professional organizations, or political institutions such as political parties.
This approach is also analytic through its use of “explicit and formal lines of reasoning” (Bates et al. 1998: 10). Analytic narratives use formal models to explain political outcomes. An outcome, such as the modification of an existing institution, is presented as an equilibrium representing the optimal strategy for all the actors involved in the game, given the preferences of the actors and a series of exogenous constraints. Note that scholars using this framework do not assume the preferences of the various actors in the game. Instead, they implement process tracing: reading documents, consulting archives, and interviewing. This methodology diverges sharply from a traditional “rational choice” approach to the study of institutions.
Analytic narratives have been fruitfully implemented in comparative politics to understand the formation and development of formal institutions. The approach is especially useful when applied to critical junctures in which political institutions are either created or fundamentally transformed. Gary Cox (1987) develops an analytic narrative to explain the decisive shift in British political institutions that took place in the second half of the nineteenth century. Cox found that three factors: the expansion of the electorate, the introduction of equally sized single-member districts, and particular technological innovations, together produced an alteration in the preferences of individual legislators. Members of Parliament became less independent and began to rely more on established political parties to run their campaigns and channel their legislative activities. As a result, the cabinet and political parties became the central players in British politics, and high levels of discipline in Parliament were institutionalized.
Analytic narratives are more than just devices allowing researchers to explain institutional change. Once the original equilibrium is reached and an institution created, behavior becomes stable and predictable. In the words of Bates et al. (1998: 8), “should exogenous factors remain the same we would expect behavior to remain the same.” In other words, by understanding the factors that influenced the preferences of the agents and led to the original equilibrium, it is possible to explain institutional stickiness and then to focus on the impact of institutions on political behavior.
Analytic narratives also contribute to comparative research. Because they are based on strong theoretical foundations, analytic narratives are well-suited for developing hypotheses testable in comparative analysis. An analytic narrative is confirmed if similar exogenous factors affect the preferences of relevant actors in similar ways and lead to a parallel process of institutional transformation. For instance, in accounting for the abolition of “buying one’s way out of military service,” Levi (1998) presents three separate narratives (United States, France, and Prussia) in which the same theoretic process is at work.
In sum, analytic narratives have the potential to be much more than explanations of specific cases. The causal mechanisms a narrative identifies can be subsequently tested with evidence from other cases.
Analytic narratives and historical institutionalism (HI) can each contribute to the study of Latin American political phenomena, but they are distinct research approaches. The first distinction is the type of event or process that the two approaches seek to explain. HI asks questions about macro-historical processes and large-scale outcomes (Mahoney & Rueschemeyer 2003). Scholars within this tradition raise questions about such topics as the causes of social revolution (Skocpol 1979), the link between capitalist development and democracy (Rueschemeyer, Stepens, & Stephens 1992), and the relationship between patterns of colonization and post-colonial development (Mahoney 2010). Analytic narratives, by contrast, are better equipped to study critical junctures, specific moments of institutional transformation. In her critique of the analytic narratives approach, Skocpol (2000: 674) points out that “game-theoretic models are likely to make sense only of certain kinds of historical situations, where there really were sets of actors deliberately maneuvering in relation to one another.” In other words, analytic narratives are more valuable when used to explain specific political decisions rather than broad sociopolitical processes. Analytic narratives can contribute greatly to our understanding of moments of change or evolution in formal political institutions, such as the adoption of new constitutions, reform of electoral laws, and expansion of the suffrage. These changes all result from processes of negotiation that involve a series of key actors maneuvering to obtain their preferred outcome under situations of uncertainty.
The second main distinction between HI and analytic narratives is the former’s focus on continuity versus the latter’s emphasis on change. HI tends to emphasize path-dependent choices that become increasingly hard to modify as they become institutionalized (Pierson 2000, 2003). Path dependence implies that “once a country or region has started down a track, the costs of reversal are very high” (Levi 1997: 28). Still, fundamental institutional changes do occur. Countries democratize, party systems break down, constitutions are revised, geographic distributions of power are amended. The analytic narratives approach has much to offer to scholars interested in explaining these institutional transformations. In other words, in spite of their common interest in utilizing historical and qualitative information to explain political phenomena, HI and analytic narratives are distinct traditions serving different purposes. HI has already produced major contributions to the study of Latin American politics (Collier & Collier 1991; Mahoney 2010; Wickham-Crowley 1992); analytic narratives remain largely unexplored.
Over the last thirty years, the most startling reality of Latin American politics has been the acceleration of sociopolitical change. Countries with weak or nonexistent democratic traditions have become relatively consolidated democracies. Everywhere ISI has yielded to some version of neoliberalism. Many countries adopted new constitutions or made wide-ranging reforms to their existing constitutions (Colombia in 1991, Argentina in 1994, Venezuela in 1999, Ecuador in 2008). A significant number of countries decentralized, breaking with a tradition of Jacobinism. Although scholars from the historical-institutionalism tradition often claim that they are raising the “big questions” (Mahoney & Rueschemeyer 2003), the region’s sweeping institutional changes continue to pose fundamental but unanswered questions.
Analytic narratives are particularly well-suited to explain these processes of institutional change. The most consequential are certainly the democratic transitions from the late 1970s to the early 1990s. Though these transitions had wide-ranging consequences for the political organization of Latin American countries, we know very little about the actors involved, their preferences, and the institutional equilibria reached.
The study of democratization in Latin America has been dominated by the “transition paradigm” (O’Donnell & Schmitter 1986; Rustow 1970). The democratic transitions are presented as contingent, uncertain processes in which political actors (moderate representatives of both the authoritarian regime and the political opposition) struggle to define the rules and procedures the political game will follow. Without question, this paradigm has contributed greatly to our understanding of the democratization process, but the transitions framework also has some important limitations. First, there is a methodological and theoretical concern. In the last volume of their seminal contribution, O’Donnell and Schmitter point out that they “did not have (…) a ‘theory’ to test or to apply to the case studies and the thematic essays in these volumes” (1986: 3). They further argue that “‘normal science’ methodology is inappropriate in rapidly changing situations, where [the] parameters of political action are in flux.” In essence, the transitions scholars built a useful general framework for understanding the complex processes of democratic transition in the third wave of democratization, but it is fair to say that they did not have a social science theory as we normally understand it. This framework was then “implicitly or explicitly followed in most other contributions [to the democratization literature]” (Collier 1999: 5).
The transitions framework has also been limited by its focus on certain actors (individual elites) while neglecting others (collective actors). In fact, the transitions paradigm presents the democratic transition as an uncertain game played by strategically defined state actors, moderate representatives (soft-liners) of the authoritarian regime and of the opposition. Societal actors, working-class movements, and civil society organizations are conceptualized as exogenous actors playing a secondary role during the negotiation of the transition pact (Collier 1999: 8). This is very problematic. Some studies have shown that societal actors did play an essential role in the democratic transitions in at least some countries (Collier & Mahoney 1997; Collier 1999; Valenzuela 1989).
As the transitions paradigm developed, then, it gradually forgot the advice—from one of the founding fathers of the transitions framework—that “we need not assume that the transition to democracy is a world-wide uniform process, that it always involves the same social classes, the same types of political issues, or even the same methods of solution” (Rustow 1970: 345).
Analytic narratives can be used by scholars interested in the transition processes and their consequences to overcome the limitations of the mainstream paradigm. Analytic narratives can serve precisely to address the methodological weaknesses of the transition paradigm by (1) devising solid theories to be tested in specific transitions in different Latin American countries, and (2) reaffirming the possibility of conducting rigorous social science research even in contexts where the rules of the game are blurred and the outcome uncertain. As for the more substantive concern—the failure to include relevant collective actors in the analysis—analytic narratives are less prone to error. Building a narrative involves a process-tracing effort that should lead to the identification of all actors influencing the process of institutional change. Moreover, existing analytic narratives often include collective actors in the analysis. Bates et al. (1998: 11) point out that one of the essential steps in designing a narrative is to “identify agents; some are individuals, but others are collective actors, such as elites, nations, electorates, or legislatures.” In sum, analytic narratives can usefully be applied to the study of democratic transitions in Latin America. A good analytic narrative will identify the different individual and collective actors involved in the transition process, and it will build a rigorous theoretical model explaining how these different agents form their preferences and then reach a negotiated equilibrium. Given the huge consequences of the transition “pacts” for political institutions in Latin America, the development of analytic narratives will be most welcome.
Let us now turn, as an illustration of the analytic narrative approach, to the adoption of the 1912 Sáenz Peña law in Argentina. The Sáenz Peña law had three main components: (1) secret vote, (2) compulsory vote, (3) proportional representation. Together, the three elements of the reform undermined the political power of the landed elite, a landed elite that through electoral fraud, clientelism, and repression had dominated politics between 1880 and 1912. The rare opposition parties stood no chance of winning elections, because the electoral machine functioned such that only the incumbent could win. Incumbent administrations at both the regional and national level controlled the lists of registered voters, lists systematically favoring the parties in power. Clientelistic practices were effective because the vote was not secret (voto cantado). The use of a majoritarian electoral system insured that no real opposition group would be present in Congress (Rock 1975). Why, then, did the political elite adopt a reform that had the potential to undermine its political power and influence?
Previous historical accounts have emphasized the structural transformation of Argentinean society in the first decade of the twentieth century, a transformation that “required” an adjustment in the political system. According to the conventional historical account, the massive influx of immigrants in the late nineteenth century led to the strengthening of two social groups threatening the power of the landed elites: the working class and the middle class. The working class began to organize politically at the end of the nineteenth century. Socially mobile immigrant families joined the middle class. As these groups became more powerful and influential, their complete exclusion from politics became more problematic (Gallo 1986). In the words of Rock (1975: 17), “the more the political role of the immigrants developed, the more likely it was that the position of the landed elite would be threatened.” Politicization of the urban sectors created political unrest and threatened the oligarchy with rebellion. A new party (the Unión Cívica Radical) symbolized the aspirations of the middle class by advocating free and fair elections. Confronted with the impossibility of an electoral victory, the UCR staged rebellions in 1890, 1893, and 1905. This view of the Sáenz Peña law is also espoused by Acemoglu and Robinson (2006: 28) who argue that the reform was “driven by the social unrest created by the Radical Party and the rapid radicalization of urban workers.”
While changes in these “exogenous factors” certainly played a role in the adoption of the Sáenz Peña law, there are many inconsistencies in the conventional historical account. First, it is unclear why elites succumbed to the societal pressure for democratizing reforms in 1912 and not before, given that the first rebellions took place in the late nineteenth century. The oligarchy had not hesitated to repress severely the revolutions of 1890 and 1893. If anything, it appears that the Radical Party was less successful at threatening the stability of the regime in the first decade of the twentieth century than it had been possible in the past. As Rock points out (2002: 193) “the [1905] rebellion fell far short of its predecessors of either 1890 or 1893. The movement commanded virtually no popular support and remained confined to small military mutinies and civilian uprisings in Buenos Aires.” The newspaper La Nación went so far as to describe the 1905 rebellion as a “parody of a sedition” (cited in Rock 2002: 193). In fact, all sectors of Argentinean society were benefitting from the exceptional economic boom that the country was experiencing in the beginning of the twentieth century. The quality of life was improving for the middle and lower classes in the urban centers (Rocchi 2000). In sum, the prospects for a successful revolution appeared very low in the first decade of the twentieth century. Any radical rebellion could have been easily wiped out. In sum, the prevailing historical account does not give us the key to solving the puzzle of the timing of the reform.
Extant accounts of the adoption of the Sáenz Peña law also present the Radical victory in 1916 as a big surprise to the Conservatives. The party in power believed it could defeat the UCR in democratic elections. This elite group clearly overestimated its own popularity and underestimated the UCR’s support in the rising middle class (Díaz 1983). Similarly, Rock (1987: 190) argues that “Sáenz Peña and his supporters had espoused electoral reform in the belief that the old oligarchic factions would adapt to the new conditions and unite into a strong conservative party that would enjoy large popular support.” But why, then, did the Sáenz Peña law promote a reform that implemented proportional representation? Offering free and fair elections would probably have been enough to force the UCR to abandon its decision to boycott elections. The Radical Party would have been discredited if it had chosen not to participate in clean elections. If the oligarchic elites were convinced they would beat the Radicals, why didn’t they design an electoral reform that maintained a majoritarian electoral system?
The conventional wisdom, then, offers us an incomplete explanation of the adoption of the Sáenz Peña law, an explanation with important inconsistencies. In particular, the adoption of a proportional electoral system and the timing of the reform are poorly explained in most historical accounts. Two questions remain unanswered: (1) Why did the oligarchic regime decide to accept the demands of the Radical Party in the second decade of the twentieth century when the option of repressing potential rebellions was still clearly available? (2) Why did the oligarchic regime design a proportional electoral system instead of a majoritarian regime that appeared more favorable? In a sense, we are asking a question about something that did not happen (i.e., continued repression of Radical and other urban rebellions). Avner Greif (1998: 26) lucidly points out that analytic narratives are particularly useful when applied to these kinds of research questions. He argues that “addressing these questions requires an appropriate model for linking what we observe with what we do not observe, namely analyzing expectations regarding off-the-path-of-play behavior and on-the-path-of-play outcomes.”
Space constraints and the complexity of the issue do not permit a full-blown analytic narrative, but we can at least sketch a preliminary model, a model based on a more careful reading of the secondary literature.19 The first essential step of analytic narratives is the identification of the key actors who played roles in the process of institutional transformation. In this case, the key actors were the political organizations negotiating the reform. The conventional historical account of the electoral reform presents a simple game with two actors: the elite (represented by the conservative coalition in power) versus the middle-class/urban sectors (represented by the Radical Party). As we demonstrated above, it is difficult to understand why the elites accepted this reform at a moment where the Radical threat seemed lower than in the past. The key to the puzzle lies in the fact that the elite was divided into two groups: the “intransigents” (opposing all forms of reform) and the “modernists” (in favor of an electoral reform but strongly opposed to the Radical rebellions).
The second step of any analytic narrative involves identifying the resources and preferences of the main actors, given a set of exogenous factors. In the case of the Sáenz Peña law, we rapidly realize that the elite were not a monolithic bloc opposed to the reform. On the contrary, the “modernist” faction was as interested as the Radical Party in obtaining free and fair elections. As we will show, this is central to understanding the timing of the reform. The oligarchic regime began in 1880 with the arrival in power of General Roca. Roca was president between 1880 and 1886 and again between 1898 and 1904. He was an astute politician who held the strings of power until the first decade of the twentieth century even when was not formally serving as the nation’s president. Although Roca made agreements with porteño politicians, his power was based on a broad coalition with the governors of Argentine provinces. Roca represented the positivist philosophy of the oligarchy. He believed that order and progress were more important than the fairness of the elections. As a result, the negotiated choice of the oligarchic elite was always imposed through corrupt and fraudulent elections. This disdain for democratic elections was soon challenged by the Unión Cívica (and later the Unión Cívica Radical). The conventional wisdom holds that the Radical Party represented the aspirations of the people (or at least the “middle class”). On the contrary, Rock (2002: 149) argues that the Radical movement “largely consisted of a front for the propertied classes of the metropolis and the army (…) [retaining] strong conservative orientations.” The UCR did not have a clear reformist program. It simply wanted to limit the worst abuses of the oligarchic regime. The main element distinguishing the Radical Party from other elite factions opposed to Roca is that it was willing to use force to obtain free and fair elections. The third—and often neglected—actor in the process of institutional reform is the “modernist” faction of the elites. This faction emerged very rapidly as a reaction to the fraudulent practices of the oligarchic regime. Modernist politicians were also positivists, but they believed that the best policies would come from the emergence of modern parties and the open debate of ideas. Only an electoral reform could achieve this goal. In 1892 (twenty years before the adoption of the Sáenz Peña law), Roque Sáenz Peña was selected as the presidential candidate of the Modernist faction. Roca reacted by counter-proposing the candidacy of Luis Sáenz Peña, Roque’s father, as the candidate of the regime. Roque Sáenz Peña dutifully withdrew his candidacy, which represented a serious blow weakening the Modernist faction for years to come (Rock 2002: 151–152). In sum, two political groups (the Radicals and the Modernists), supported the electoral reform. However, both actors were politically weak. The Modernist faction had few political resources against the political and electoral machine of the oligarchic regime headed by Roca. The Radical Party lost momentum after the failed rebellions of the early 1890s and was incapable of threatening the regime militarily. Moreover, an alliance between Modernists and Radicals was impossible, because Modernists disliked the use of force more than they disliked the fraudulent practices of the regime. Of course, the dominant faction of the oligarchic regime would not support any electoral reform threatening their position of power. Since the coalition orchestrated by Roca had more political resources and more military power than the other political groups, an electoral reform was unconceivable until the first years of the twentieth century.
The puzzle, then, is to explain what upset this previous equilibrium, allowing the adoption in 1912 of the Sáenz Peña law. The prevailing historical wisdom presents the reform as a defensive reaction by the elites against the pressures of the rising middle classes (especially in Buenos Aires). Our analytic model allows us to evaluate this historical narrative. Before analyzing the preferences and resources of the three key political actors in the first decade of the twentieth century, it is important to consider some important exogenous factors that were redesigning these preferences and resources. The start of the oligarchic regime in 1880 coincided with the rebellion of the province of Buenos Aires, a rebellion that was harshly repressed by federal forces. Out of a sense of political opportunity, most porteño politicians—most notably Mitre and Pellegrini—decided to enter the oligarchic coalition led by Roca. For twenty years, Roca reached agreements with politicians from Buenos Aires and maintained his position of preeminence. However, these agreements could not avoid a distinct provincial bias in the oligarchic regime. According to Rock (2002: 185), “controlling the Senate and the provincial governors, Roca could usually ignore the city of Buenos Aires.” In fact, the metropolitan vote was unneeded to maintain the viability of the oligarchic regime. Still, things were changing at the beginning of the twentieth century. The structure of the economy was changing, especially the weight of the industrial sector. In 1890, the industrial sector accounted for only 13.4% of the GDP. By 1916, it represented 27.8 % of the GDP (Rocchi 2000). Most industrial goods were produced in the cities, and the major industrial center was Buenos Aires. This structural transformation of the economy increased the dissatisfaction with the political status quo of politicians from Buenos Aires. In addition, reformist and democratic movements were beginning to form in Buenos Aires. A student riot in July, 1901, made it clear that discontent with the oligarchic regime was growing. Politicians from Buenos Aires realized that “the new currents were about to tilt the balance against the old” (Rock 2002: 181). As a result of these structural transformations, political leaders from Buenos Aires—led by Pellegrini—abandoned Roca and joined the reformist camp. These desertions changed completely the balance of power between the two elite factions. While the Modernist faction gained momentum with the support of porteño politicians, the Roca faction lost much of its power. The position of the Radical Party, however, did not evolve so markedly. As we sketched above, the UCR seemed less threatening to the regime in the first decade of the twentieth century than in the 1890s. Still, the unsuccessful rebellion in 1905 was used by the reformist faction of the regime to exaggerate the threat and push for a reform in their own interest.
When Sáenz Peña took power in 1910, the three main political actors remained the same, that is, the modernist and the intransigent factions of the oligarchic regime along with the Radical Party. Their interests also remained the same. The Radical Party and the Modernists wanted free and fair elections, while the most conservative faction of the elites wanted to maintain the status quo. The balance of power, however, had changed. The modernist faction was now in a much stronger position, because it controlled state resources. But Sáenz Peña wanted to take advantage of this window of opportunity. It was uncertain who would be the next president, and the most conservative faction of the regime still had a lot of political resources, especially in the provinces.
The timing of the reform is better explained with this analytic model than with the conventional historical account. Pressure from the middle classes was not overwhelming, and the threat represented by the Radical Party was lower than it had been in the past. The reform was introduced in 1912 because the balance of power was more favorable than ever to the reformist faction of the oligarchic regime. Social unrest is an important exogenous factor that contributed to changing the preferences of the main players in this game of institutional transformation. But the link is not as direct or as evident as previous studies have argued.
Why did the Sáenz Peña law introduce a proportional electoral system rather than a majoritarian system? This question is a puzzle in previous historical accounts, because these accounts also hold that the oligarchy expected a clear victory in the next elections. Once again, our analytic model provides a better answer. The post-reform period was a highly uncertain one in which many parties representing the different political groups we have analyzed would co-exist. Proportional representation assured the main players in this negotiation that at a minimum they would be represented in Congress in proportion to their electoral force. By showing that the oligarchic regime was divided into two clear and irreconcilable factions—at least with respect to electoral reform—we are in a better position to understand the specificities of the Sáenz Peña law.
In sum, by illuminating the preferences of the different political actors involved in the process of institutional transformation, a good analytic narrative would help solve this important puzzle in Argentine politics. True, the politicization of urban sectors in the beginning of the twentieth century may have pressed the regime to move in the direction of free and fair elections, but the timing and the form of the institutional transformation are better understood through a careful analysis of the preferences of the key players involved in this game.
Research initiatives in these three areas will require a greater investment in what we call “soaking and poking.” Bureaucracies (like the equally neglected area of lower courts) are diffuse, with within-country geographical as well as hierarchical spread. Bureaucracies are also heterogeneous, with differences across countries, across levels of government within countries, and across types of programs administered. Put simply, research on one agency in one country cannot be generalized to “Latin American bureaucracy.” Similarly, lobbying research will involve tracing group-specific or industry-specific involvement in the legislative process from the introduction (or non-introduction) of bills to their ultimate failure, modification, or passage. An analytic narrative of an event distant in time will involve extensive interviews along with archival research in documents, memoirs, and letters.
In an increasingly quantitative and formal political science, can we ask scholars, especially younger scholars, to engage in what sounds suspiciously like the dreaded “case study”? Is this not a prescription for unemployment? One response is that case studies and theory are not antithetical. The modal dissertation in comparative politics builds a theoretical argument and tests that argument on carefully chosen cases. Still, this response is disingenuous, because it ignores the sequence of research development in areas like legislative politics. Shepsle, Fiorina, and McCubbins needed the “soaking and poking” of Fenno, Manley, and Wildavsky. Carpenter’s theory of bureaucratic autonomy built on Pendleton Herring.20
How can we provide incentives for more intensive field research in areas with diffuse and heterogeneous research sites? One solution is scholarly collaboration. Particularly at the dissertation level, data can be shared even when theoretical arguments are distinct. For example, two scholars can share data on lobbying techniques in different countries even though their theoretical arguments differ, and data on informal networks in varying bureaucratic agencies can be shared among multiple scholarly projects.
Many years ago the American Political Science Association regularly published subfield-specific lists of “dissertations in progress.” Graduate students in the early stages of thesis preparation regularly consulted these lists to see what others were doing, to avoid duplication, and to get ideas. For reasons that are unclear to current staff, the APSA stopped publishing these lists in 1989.21 Such lists today could serve as invitations to data sharing and collaboration.
The rapid development of high-quality research traditions on the part of political scientists based in Latin American universities also provides new opportunities for collaboration. In terms of field research, Latin American scholars face weaker time pressures than those faced by scholars based outside the region, and they are likely to have useful social and professional networks. Collaborations with U.S. scholars would be particularly attractive to Latin American scholars as they move beyond single-country research.
Ultimately, responsibility for encouraging new directions in research and for rewarding risk-taking projects falls to senior scholars, especially those in programs with a major Latin American component. The vitality of the study of Latin American politics depends on avoiding the trap of “political science as usual,” that is, ever-narrower questions answerable only with quantitative data. Doubtless there are other research questions and strategies as compelling as those we have put forward; in the end we simply want to encourage debate on what’s next.
1 We are grateful for comments to Guy Peters, Jennifer Victor, and the editors of this volume.
2 For a thorough treatment of the policy process as it affects the shape and implementation of administrative reform, see Ben Ross Schneider and Blanca Heredia, Reinventing Leviathan: The Politics of Administrative Reform in Developing Countries (2003). Schneider and Heredia provide an excellent discussion of models of administrative reform, and various authors contribute chapters on Latin America and other developing countries, but there are no discussions of the actual functioning of any bureaucratic agency. When reform is the objective, it is simply taken for granted that the diagnosis of bureaucratic disfunctionality is correct.
3 Guy Peters argues that Weberian reforms ought to precede NPM: “Most governments in the world face pressures, either psychological or more tangible, to adopt the modern canon of administration in the form of NPM. For Central and Eastern Europe and Latin America, those pressures are likely to do more harm than good. Despite the appeal of ideas such as deregulation and flexibility, governments attempting to build both effective administration and democracy might require much greater emphasis on formality, rules, and strong ethical standards. The values of efficiency and effectiveness are important but in the short run not so crucial as creating probity and responsibility. Once a so-called Weberian administrative system is institutionalized, then it may make sense to consider how best to move from that system towards a more “modern” system of PA. (2001, p. 176; see also p. 164)
4 These data come from the Bank’s “Network on Public Policy Management and Transparency” (Lora 2007).
5 Tendler and Freedheim note the growing literature on industrial performance and workplace transformation in political science, a literature that emphasizes worker commitment and client-worker trust. See, for example, Piore and Sabel (1984). Finally, it might be helpful to compare this kind of program with the administrative style of Bolsa Família
6 See Sotiropoulos (2004) for a very abstract comparison of Southern European (and by extension Latin American) bureaucracy with the rest of West European bureaucracy. Tendler and Freedheim’s (1994) project on Ceará’s rural health program is precisely a study of street-level bureaucrats.
7 TVA linked itself to the land-grant college system and to the American Farm Bureau Federation. Their pressure led TVA to exclude the Farm Security Administration and the Soil Conservation Service from its area of operation (Selznick 1966). It also led to discriminatory policies against Black farmers.
8 This bias sometimes reveals itself all too clearly. Clive Thomas’s Research Guide to U.S. and International Interest Groups classifies Latin America as a developing society, starkly different from a developed, pluralist society. “In [developing] societies interests as opposed to interest groups are more significant politically … In developing societies the major type of interest is the primordial group based on kinship, tribe, lineage, neighborhood, religion, and so on” (2004, 325). In describing the tactics that interests use in places like Latin America, Thomas suggests that “Such formalized and institutional channels are minimal or nonexistent in non-pluralist, transition, and developing societies. In these systems informal personal contacts and power plays within and between government entities and related organizations, such as the ruling party or the court circle around a monarch, are the most significant” (2004, p. 325). Not exactly the Latin America we know.
9 Bates and Krueger note that their country studies “fail to attribute a decisive role to the pressure of organized interests” (1993: 457). Perhaps (and of course “decisive” is a murky term), but their three Latin American cases provide lots of evidence to the contrary. Post-Allende Chile was a dictatorship (hello?), and the import-competing sector favored the general policy line of the government even though it opposed draconian trade liberalization (Stallings & Brock 1993). Brazilian industrialists opposed the government’s ill-fated stabilization program of 1979–1984. Payne (1994) and Boschi (1978) found that industrialists used “social ties and personal contacts to influence government both within and outside the context of bureaucratic rings” (cited by Lal & Maxfield 1993: 45). In Ecuador, Grindle and Thoumi discovered that presidents introduced but could not sustain policy innovations, partly as a result of regional and sectoral interest group pressures (Grindle & Thoumi 1993).
10 The ambivalence of the literature is thoughtfully treated in Peter Kingstone’s Crafting Coalitions for Reform: Business Preferences, Political Institutions, and Neoliberal Reform in Brazil (1999). Kingstone focuses on establishing the preferences of various industrial sectors and the ways in which market and political factors interact to shape preferences and behavior.
11 See also Eduardo Sáenz Rovner’s investigation of Colombian interest groups in the 1940s, La Ofensiva Empresarial: Industriales, Políticos y Violencia en los Años 40 en Colombia.
12 On network density, see Lowery and Gray (1995). On the creation of partisan divisions, see Grossmann and Dominguez (2009). On cliques, see Chwe (2000).
13 Ames, for example, found evidence in Brazil in the early 1990s that some deputies—it is unclear how many—run mini-lobbying enterprises directly from their offices, utilizing staff to lobby the ministries in the name of the deputy but for the benefit of fee-paying private firms.
14 Consider Baumgartner et al.’s Lobbying and Policy Change (2009). Utilizing a random sample of approximately one hundred issues between 1999 and 2002, the authors interviewed more than three hundred lobbyists and government officials. With these and follow up interviews, plus official reports and monitoring news throughout all four years, they were able to map the progress made on each issue.
15 Some work uses economic proxies of interest group influence, such as weight of the sector’s economic influence as a percentage of GDP (e.g., Frieden, Ghezzi and Stein 2001; dos Santos 2008).
16 On the consequences of campaign contributions, see Hall and Wayman (1990), McCarty and Rothenberg (1996), and Wawro (2001). On the strategies behind such contributions, see Apollonio and La Raja (2004), Gordon et al. (2007), and Wright (1985).
17 Lance (2010) used the data while acknowledging Samuels’s disclaimer, arguing that the data serve as conservative estimates. He contends that if he can prove that only the 25% most reputable contributions affect legislation, then the relationship should hold for all contributions.
18 Sophisticated reviews of rational-choice institutionalism present two levels of analysis within the tradition. The first takes institutions as exogenous and fixed; the second allows endogenous institutions and observes their formation and survival (Shepsle 1986). But even adherents of RCI recognize that the former is “far more well developed” than the latter (Weingast 1996: 167)
19 Of course, dressing an analytic narrative of this case would require scholars to consult such primary sources as newspapers, archives, and political memoires.
20 Note, once again, Karcher and Schneider’s claim that “The study of business in Latin America may also suffer from a bias in political science for quantitative methods.” This bias is only part of the problem of Latin American interest group research, but it also affects work on bureaucracy. One cause of the shallowness of the administrative reform literature is its reliance on easily quantifiable indicators. This bias advantages the approach of “bureaucrats as opportunistic rent-seekers.” As we saw in our discussion of Daniel Carpenter’s work on U.S. bureaucratic development, a more open theoretical lens, one in which bureaucrat-politicians may try to create policy space for themselves, is critical.
21 Communication with senior APSA staff, June, 2011.
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