collective violence: a research agenda and some strategic considerations

Collective Violence: A Research Agenda and Some Strategic ConsiderationsAuthor(s): David SnyderSource: The Journal of Conflict Resolution, Vol. 22, No. 3 (Sep., 1978), pp. 499-534Published by: Sage Publications, Inc.Stable URL: http://www.jstor.org/stable/173732 .

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Collective Violence

A RESEARCH AGENDA AND SOME STRATEGIC CONSIDERATIONS

DAVID SNYDER Indiana University

This paper is based on the premise that current empirical analyses of collective violence are largely inadequate, and takes as its primary objective a detailed specification of alternative methodological strategies. Quantitative research on violence is cited for problems of measurement and causal inference, which stem from attempts to represent important theoretical concepts (relative deprivation, resource mobilization) at levels of analysis other than those at which they are formulated. Alternative strategies for empirical investigation of violence include timeseries analyses of individual perceptions and data on organized groups, as well as studies of crowd dynamics. Methods for linking the latter type of qualitative approach to quantitative ecological analyses are indicated. In general, the conclusions strongly suggest a theoretical and empirical reorientation toward "disaggregated" approaches to collective violence, and away from global conceptual and cross-national methodological efforts. Although consideration is limited to the determinants of domestic violence, the concluding section outlines the potential relevance of international linkages and the outcomes of violence to these central concerns.

Efforts to explain a range of phenomena variously labeled civil strife (Gurr, 1968), collective violence (Tilly, 1969, 1975), revolution (Davies, 1962, 1969), and political instability (Feierabend and Feierabend, 1966) or violence (Hibbs, 1973) have advanced considerably over the past

AUTHOR'S NOTE: This is a much revised and shortened version of a paper originally completed in February 1977. Readers interested in elaboration and related issues not covered here are encouraged to request copies of the longer manuscript. I am grateful to Paula M. Hudis and Ted Robert Gurr for helpful comments on an earlier version, but retain full responsibility for the views expressed here.

JOURNAL OF CONFLICT RESOLUTION, Vol. 22 No. 3, September 1978 ? 1978 Sage Publications, Inc.

499



500 JOURNAL OF CONFLICT RESOLUTION

fifteen years.1 Several coherent lines of theoretical development- particularly those emphasizing collective discontent (Davies, 1962; Feierabend and Feierabend, 1966; Gurr, 1968, 1970) and groups' mobilization and application of resources in political arenas (Tilly, 1975; Snyder and Tilly, 1972; Oberschall, 1973; Gamson, 1975)-have stimulted abundent research on important questions. Related empirical progress has also occurred through the widespread application of quantitative methods to accumulating bodies of contemporary and historical aggregate (e.g., Gurr, 1968; Hibbs, 1973; Snyder and Tilly, 1972; Spilerman, 1970) and individual level (e.g., Rude", 1964; Caplan, 1970) data.

Despite these advances, more careful consideration of the state of research on collective violence warrants substantial pessimism. Many observers note that existing theories specify neither comprehensive (Hibbs, 1973: 3; Snyder and Kelly, 1976: 135) nor unambiguous (Grofman and Muller, 1973) explanatory models. Empirical analyses have at best slowly resolved these difficulties of theory building and trimming because much of the evidence is contradictory, both across and within types of data employed (e.g., compare Feierabend and Feierabend, 1966, and Gurr, 1968, with Hibbs, 1973; Grofman and Muller, 1973; McPhail, 1971). However, even more problematic than this reliability of findings issue is that of validity: the major premise of this article (subsequently documented) is that most quantitative analyses of collective violence do not adequately address the relevant substantive arguments. Moreover, current research largely continues to follow conventional empirical strategies (and for that matter, to refine rather than rethink available theoretical statements) that now yield diminishing marginal results.

In light of this pessimistic assessment, my objective is to indicate a set of promising, if infrequently used, strategies for (especially empirical) investigations of the determinants of collective violence. As a necessary

1. Collective violence as arbitrarily defined here encompasses events which meet some minimum criteria of size and damage to persons and/ or property. Following conventional usage of the term, international wars and acts of individual violence are excluded from consideration. However, it should be noted that many of the studies cited above variously encompass events which are neither collective (e.g., some assassinations) nor violent (e.g., elections, some protest demonstrations). While such differences in opera- tional definitions have important implications (e.g., Nardin, 1971; Jacobsen, 1973; Tilly, 1975), there is enough overlap in the phenomena of interest to warrant addressing these studies in a single context.



Snyder / COLLECTIVE VIOLENCE 501

preliminary, I sketch some major theoretical orientations and analytic methods in order to specify the lack of fit between them and identify important substantive questions. But in the bulk of the discussion, I draw on recent work in economics, political science, and sociology to suggest alternative strategies of research design, data collection, and empirical analysis that more appropriately address such substantive issues.

SOME MAJOR LINES OF ARGUMENT

This section considers two lines of theoretical development on the determinants of collective violence, here labeled "relative deprivation" (e.g., Davies, 1962, 1969; Feierabend and Feierabend, 1966; 1972; Gurr, 1968, 1970; Gurr and Duvall, 1973, 1976) and "resource mobilization" (e.g., Tilly, 1970, 1975; Gamson, 1975; McCarthy and Zald, 1977; Wilson and Orum, 1976; Oberschall, 1973; Snyder and Tilly, 1972) approaches. While this arbitrary division is not novel (see Korpi, 1974; Useem, 1975; McCarthy and Zald, 1977, for similar treatments), it is obviously selective and requires several immediate caveats. No comprehensive review of various explanations (nor even detailed exposi- tion of the two considered) is attempted. My main purpose is to outline some widely employed arguments in order to illustrate problems of conventional data and strategies in testing them. Approaches that emphasize biological factors (Nelson, 1974, 1975), linkages with international politics and/or conflicts (Rosenau, 1969; Rummel, 1963), structural-functional models (Johnson, 1966; Smelser, 1963), prior issues concerning the bases of conflict (see Fink, 1968; Dahrendorf, 1959) or neo-Marxist analysis (reviewed in Salert, 1976) are not specifically covered because of (1) failure to generate a corresponding body of empirical work; or (2) the negative weight of available evidence; and/ or (3) duplication of the core strategic issues to be raised.2

2. While space consideration preclude full documentation of these assertions, little quantitative research examines biological or strictly Marxist approaches (though excep- tions exist: e.g., Sugimoto, 1975). Also, previous research indicates little evidence of a regular relationship between international and domestic violence (see Zinnes, 1976: ch. 8, for a cogent review). And concerning specifications of functional theory, results on the dis- equilibrating effects of rapid changes such as urbanization on disorder (Hibbs, 1973; Lodhi and Tilly, 1973), participation of "dislocated" individuals in violence (Rude', 1964; Caplan, 1970), and even the intervening assumption that changes disrupt normative integration (Freedman, 1950; Lewis, 1952; Kantor, 1965) are not supportive of the theory.




For those concerned that omission of such approaches neglects too much of significance, I note that different categorizations of theories at least partly reflect heuristic convenience and taste, and that many central ideas of the types "dismissed" above are contained in the lines of argument addressed here. For example, relative deprivation theories (alternatively labeled collective discontent, social psychological, achievement deprivation; see Tilly, 1975; Gurr, 1973; Grofman and Muller, 1973) often include elements of structural-functional models.3 Similarly, resource mobilization (sometimes group conflict or power struggle theories; Gurr, 1973; Korpi, 1974) relies on both Marxian and economists' rational choice arguments in identifying the importance (and problematic nature) of the organization of discontent. What should be recognized is that relative deprivation (RD) and resource mobilization (RM) approaches represent more general differences in emphasis-on perceptions, aspirations, beliefs, and values versus the formation of and interactions among competing collectivities-which persist across explanations of collective violence (and conflict itself). What should be avoided is missing these substantive distinctions among the varieties of terminological trees.

RELATIVE DEPRIVATION

While this theory at least implicitly underlies a broader range of analyses (e.g., inequality-violence hypotheses; see Russett, 1964; Nagel, 1974; Sigelman and Simpson, 1977), the central work of Davies (1962, 1969), Feierabend and Feierabend (1966, 1972), and Gurr (1968, 1970; Gurr and Duvall, 1973, 1976) is known widely enough that only a few main points of theory and method need be identified. The important common themes of this line of argument may be characterized as follows. The scope and intensity of the gap between individuals' expected and achieved welfare on some criterion produces the variations in collective discontent (and consequent frustration, anger, and potential aggression) that are attributed as a, and typically the, major determinant of variations in collective violence. When such discontent is focused on

3. For instance, such convergence occurs where the effects of rapid change or modernization operate indirectly via their influence on the expectations-achievments gap (Feierabend et al., 1969). More generally, Gurr (1970) treats anomie as a specific case of the global concept of collective discontent, while functional theorists such as Smelser (1963) attempt to incorporate discontent as a particular form of structural strain.




governments or related political targets, the probability of manifest conflict increases. Finally, the (especially coercive) actions of governments, and more generally a nation's institutional capacity for deflecting discontent into channels other than collective political action, are viewed as important influences (e.g., Huntington, 1968: ch. 1; Gurr, 1970: chs. 8 and 9; Feierabend and Feierabend, 1966: 250-25 1).

There are of course significant differences among particular arguments. First, while all of this work invokes frustration-aggression theory in its interpretation of aggregate patterns, the degree to which individual-level psychological explanations predominate varies considerably. For example, Davies (1969: 705) asserts:

This J-curve is a psychological, not a sociological explanation. The units of analysis are individual human beings. They may fall into visible categories (like blacks or students or working men or peasants), but their mental processes that relate to frustration and aggression are fundamentally the same.

Conversely, Gurr's (1970) model is explicitly "sociocultural" and incorporates structural variables (e.g., the balance between regimes and dissidents of coercive or institutional support) that operate largely independently of individual-level constructs.4

A second major difference concerns multiple causality and the com- pleteness of theoretical models. Many RD arguments (e.g., Davies, 1962, 1969; Feierabend and Feierabend, 1966, 1972) pay little attention to factors other than collective discontent and neglect important questions: how and why are grievances focused on political targets? how do discontented individuals come to undertake collective action? Again, Gurr's work (1970; see especially recent modifications in Gurr and Bishop, 1976; Gurr and Duvall, 1976) is exceptional insofar as it attempts to deal systematically with such issues; specifies a joint influence of discontent, justifications, and the balance of capabilities on violence; and (in response to criticisms such as Nardin, 1971) recognizes that agents of the state often play central roles as parties to, not simply regulators of, violence.

4. The foregoing discussion does not imply that any theory of collective violence is or can be entirely psychological, particularly insofar as some factors exogenous to individuals (e.g., Davies' J-curve) must be invoked to explain temporal shifts in manifest conflict.




Despite these substantive differences, empirical work that explicitly tests RD has largely converged in aggregate (usually cross-sectional) analyses of relationships between indicators of discontent, other factors such as coercion, and measures of political conflict. While most such studies (e.g., Feierabend and Feierabend, 1966; Gurr, 1968; Gurr and Duvall, 1973; Bwy, 1968; Gurr and Bishop, 1976; Cooper, 1974) report results that are consistent with expectations, some other analyses of this type (e.g., Hibbs, 1973; Snyder and Tilly, 1972; Nagel, 1974) present negative evidence. The point is not that the number of favorable and contradictory findings (the former predominate) can be used to evaluate the theory-more careful examination of the methods and results would be necessary for that-but simply that the evidence available from this conventional research strategy is mixed. Alternative research designs, including similar ecological analyses of subnational units (e.g., Spiler- man, 1970, 1971; Morgan and Clark, 1973) and individual-level data recovered from arrest records or surveys of participants (e.g., Orum and Orum, 1968; Searles and Williams, 1962; McPhail, 1971), also yield inconsistent findings, though the weight of the evidence from these studies tends to be less supportive of RD theory that reported in cross- national research.

RESOURCE MOBILIZATION

While this line of argument developed partly in response to the mixed results on RD and related conceptual approaches, RM is more explicitly an alternative to what it views as incorrect or incomplete specifications in previous work.5 A general characterization of RM approaches and (implicitly) their criticisms of other arguments include the following.

(1) Variations in discontent are either entirely (Tilly, 1975; Jenkins and Perrow, 1977; Snyder and Tilly, 1972) or at best weakly (McCarthy and Zald, 1977: 1214-1215) related to collective political action. This argument is heavily influenced by rational choice theorists such as Olson (1965), who shows that whether individuals ever organize to pursue

5. Several of the criticisms indicated here are explicitly derived from RM perspectives, though this does not suggest that such views are themselves immune to challenge (see below). Similarly, the more extensive discussion of RM rather than RD arguments proceeds on the assumption that the former is less familiar and therefore requires a more detailed presentation of content and merits.




common interests or redress shared grievances is highly problematic rather than inevitable (as is often assumed). It is also based on the premise that a large enough stock of discontents to warrant extensive political protest is invariably present.

(2) Therefore, the organization of discontent becomes a central explanatory variable (Tilly, 1975; Oberschall, 1973; Snyder and Tilly, 1972; McCarthy and Zald, 1977), particularly insofar as it helps to account for how individuals come to participate collectively (at the same place, time, and often for the same purpose) in large-scale events. Conse- quently, processes of interaction beween individuals and groups, especially the latter's mechanisms of recruitment and maintaining commitment, become important research questions.6

(3) Moreover, given that some sets of individuals will become identifiable collectivities (groups and organizations) and others will not, fluctuations in existing groups' mobilization, or collective control, of resources (e.g., loyalties, money, arms) exert important constraints on such groups' capacity to undertake collective action of any kind (see Etzioni, 1968: ch. 15; Snyder and Tilly, 1972; Gamson, 1975; Jenkins and Perrow, 1977).

(4) To the extent that their mobilization levels permit (Tilly, 1975; Gamson, 1975), and depending on important variations in strategy and tactics (e.g., McCarthy and Zald, 1977; Gamson, 1975), groups attempt to apply their resources toward acquiring collective goods. Such attempts typically occur in the context of political arenas because political decisions are so important to the flow and distribution of benefits. Some groups, of course, have already achieved a measure of regular power over allocation decisions in a polity and employ less visible influence strategies (e.g., lobbying). But others have no such routinized means of pressing their demands and necessarily use their resources in public demonstrations and shows of strength in order to gain particular benefits and to establish the legitimacy of their constituency's claims to a

6. Many of the mechanisms (e.g., ideologies that foster solidarity, calculations of success probabilities) specified as important in this literature (see McCarthy and Zald, 1977; Fireman and Gamson, 1978) do not differ qualitatively from factors underlying the development of normative and utilitarian justifications for political violence identified by Gurr (1970: chs. 6-7). The relevant distinction here is whether such justifications promote political violence by linking individuals to groups (which attempt to manipulate perceptions as a conscious strategy in the RM approach) or by focusing discontent directly on governments.




regular share of influence over political decisions (Snyder and Tilly, 1972; Gamson, 1975).7

(5) Since such demands lay claim to scarce and competitive resources, they are often met by organized resistance from other mobilized groups and (most often) from governments via their agents of official force. The subset of mobilization theorists that deal explicitly with collective violence (e.g., Tilly, 1975) hypothesize that it results largely as a byproduct of interactions among collective actors (including police and troops) in public settings,8 but recognize that violence sometimes occurs more directly because "it is simply the most efficient means of accomplishing some collective end" (Tilly, 1975: 493).

The general merits of RM approaches lie in their greater (a) attention to dynamic processes (e.g., of interactions among groups); (b) ability to address questions that are logical necessities in explaining collective violence but are neglected or underemphasized in most other theories: how do collective events occur (via organization) and why are protests so often "political" (because governments fundamentally effect the distribution of goods that constitute desired collective ends)?; and (c) focus of strategies of research on collective violence at the group level of analysis.9 But this is not to claim that RM theories lack problems. A major one (particularly in early efforts: e.g., Tilly, 1970, 1975; Snyder and Tilly, 1972) is the excessively centralized conception of mobilization, which makes it extremely difficult to account for apparently spontaneous events that lack evidence of any organizational base (e.g.,

7. Gamson's (1968) stable unrepresentation model is implicit here; a given group's probability of becoming involved in violence varies according to its position vis-a-vis a (typically, but not necessarily) national structure of power. As a specific example of this point, consider the experience of American labor organizations with respect to industrial violence.

8. More precisely, authorities' actions are importnat in two ways: first, by initiating coercive measures (e.g., restrictions on associations and assembly) that diminish a group's organizational capacity, and second, by resisting partisan collective actions that do occur.

9. However, this does not imply that RM approaches lack expectations concerning aggregate variations in collective violence over time and / or across political units. McCarthy and Zald (1977: 1124) argue that the amount of wealth in a society (and conse- quently, of discretionary resources) will be positively related to the volume of social, including political, movement activity because resources available for mobilization will be increased. Similarly, Snyder and Tilly (1972) report that nonviolent national political activity (e.g., elections and cabinet changes) is positively associated with year-to-year fluctuations in violence over a 130-year period in France. They interpret this finding to indicate that shifts in the centers of power stimulate collective demands from mobilized groups.




racial disorders in American cities). A related concern is the neglect of individual actors, especially the mechanistic assumption that their propensity to act is entirely mediated through linkages with groups. However, as with the RD arguments there are significant variations in RM approaches, and several recent treatments (Oberschall, 1973; Fireman and Gamson, forthcoming; McCarthy and Zald, 1977; Wilson and Orum, 1976) address the nature and bases of individuals' recruitment and commitment to groups and propensities to participate in collective action.

Despite these difficulties, perhaps the greatest general merit of RM (at least in principle) is that it provides a plausible alternative to previous approaches. In practice, of course, the relative advantages of RM will ultimately be substantiated or vitiated by its ability to explain observed variations in manifest political conflict, and the empirical evidence to date is sketchy. Much of the support for RM theories is indirect. For example, findings that collective violence is no more, and often less, likely to occur in periods of rapid change (Hibbs, 1973; Lodhi and Tilly, 1973), or that the "uprooted" are less likely to participate (Rude", 1964; Caplan, 1970) are consistent with organizational interpretations. If violence fluctuates with groups' capacity for collective action, then the disintegrating effects of rapid industrialization or urbanization ought to depress that capacity. Similarly, Tilly's (1969, 1975) finding that (at least in France) the modal episode of collective violence begins with protests that are not intrinsically violent and is initiated (and most of the killing and wounding done) by police and troops, are in line with the central RM arguments. To be sure, a few quantitative analyses directly link measures of group mobilization to collective protest (Aminzade, 1973; Shorter and Tilly, 1974; Snyder, 1975). However, in these studies mobilization is usually measured by crude proxies, such as shifts in groups' size, and the strongest supporting evidence pertains to fluctuations in industrial strike activity-a phenomenon that, given the importance of unions, probably best fits the assumption of heavily centralized mobilization mechanisms and neglect of individual actors.

In summary, the mainstream of work on the determinants of collective violence is largely characterized by (1) competing RD and RM theories, which are not themselves exhaustive, but instead reflective of broader differences in emphases on perceptions, symbols, and the like versus organization and interaction; (2) quantitative research strategies that are dominated by cross-sectional analyses of ecological or indi-




UNIT OF ANALYSIS "INDI)FPENDE'r" VARIABLES "DEPENDENT" VARIABLES

AGGREGATE /X1 Environmental A 1Y1 Frequency/lagnitude ofit (Nations, Cities, / Characteristics > Collective Violence in

Etc.) I SpatiosTemporal Unit

II

cOLL17(TIk'IT y x., :oIiciviti 4 Y. Collective Participation I (Groups/Organizat ions) - C:laracterist ices B \ in Violence

DUA)l' II)AI.

d. dndiviudual. Partic ipation

Characteristic'; I in (Collective) Violence/

Xi, Y1: sets of variables; AB, . N: relationships among variables; see text for further description and explanation of Figure.

Figure 1: Units of Analysis Employed and Relationships Examined in Research on

Collective Violence

vidual-level data; and (3) evidence on each line of argument that is some- what inconsistent and (even for those inclined to interpret it as favoring one approach over the other) by no means fully adjudicates or otherwise resolves the differences between alternative theories.

EMPIRICAL ANALYSES OF COLLECTIVE VIOLENCE: PROBLEMS AND ALTERNATIVE STRATEGIES

PROBLEMATIC ISSUES

While the foregoing discussion suggests that current empirical analyses adequately test the relevant arguments, any implication of a close fit between theory and evidence is highly problematic. Substanti-

ating that assertion, as well as developing guidelines for alternative empirical strategies, requires identification of major difficulties in extant quantitative work. Specification of such difficulties relies on Figure 1, which presents a heuristic diagram of units of analysis employed and relationships examined in most empirical research. Al- though no formal representation of a causal system (e.g., Duncan, 1966) is attempted, the Xi and Yi, respectively, designate sets of independent and dependent variables measured at a specified level of




analysis. Associations within sets-e.g., between GNP and governmental coercion in X1-may be neglected for present purposes. Letters A, B, . . ., N represents relationships among sets of variables-for example, E indicates the effects of aggregate political, economic, and so forth conditions on individuals' economic welfare or mental processes (perceptions of deprivation or government legitimacy). Finally, solid arrows (labeled A, C) indicate relationships that have received considerable quantitative study-the ecological and individual-level analysis cited above-while broken arrows designate those accorded little, if any, attention.

In terms of Figure 1, simple versions of RD (e.g., Davies, 1969) and RM (e.g., Snyder and Tilly, 1972) verbal statements could be specified, respectively, as ECI and DJB plus KJ sequences.'0 Of course, more synthetic treatments in each line of argument (e.g., Gurr and Duvall, 1976; McCarthy and Zald, 1977) would, with different weights, incorporate those and additional linkages in the theoretical model. But the aim here is not to accomplish an unambiguous mapping of any given argument vis-a-vis Figure 1. Instead, it is to demonstrate that any theoretical model involves linkages between levels of analysis in its a priori causal statements and its interpretation of empirical results. The problematic consequence is that the conventional analyses of areal aggregates or individual participants which dominate empirical work cannot address the theoretically specified causal processes that operate across levels (or sometimes within them: e.g., the dynamics of interactions among groups). Moreover, it is precisely such processes-e.g., "environmental" (XI) effects on individual and group characteristics, the relative importance of perceptual and organizational factors in explaining collective violence-that constitute both the central hypotheses stated by alternative arguments and the means of discriminating among them.

Empirical practitioners, particularly of ecological analyses, often acknowledge these limitations (Gurr, 1970: 63ff.; Snyder and Tilly, 1972: 527-530) but do not appear unduly concerned by them. Standard

justifications for such analyses take several forms. One is that ecological

10. For example, Davies' RD treatment indicates that structural variables such as economic fluctuations affect (E) individuals' perceptions, which in turn determine (C) the probability of participation in collective violence. Aggregate levels of violence are sums of these individual probabilities (I), while any collective pattern of participants is an inci- dental consequence (H) of individuals' shared sources of deprivation, frustration, and anger (Davies, 1969: 705).




studies address "the relevance of the theory for the most general case ...

but not. . . the microanalysis that would account more precisely for the forms, timing and targets of civil strife" (Gurr and Ruttenberg, 1971: 189). Other, typically more subtle, warrants include reference to high R2, other studies with similar findings and interpretations or (sometimes explicit) assumptions that areal measures adequately capture the disaggregated concept of interest. However, the objections raised here concern explanation (i.e., interpreting relationships) more than predic- tion, validity more than reliability, and examination of the very cross- level correspondence assumed to warrant research using ecological data in the first place. In principle, such objections could be met if aggregate variables closely and linearly determine (and therefore serve as adequate proxies for) the disaggregated variables of interest. 11 But available evidence on that association is far from reassuring. One major case in point is that all ecological studies infer RD from measures of objective welfare in some populations (e.g., in Gurr, 1962; Feierabend and Feierabend, 1966, Bwy, 1968; Davies, 1962, 1969). However, recent survey results reported by Grofman and Muller (1973) and Miller et al. (forthcoming) show no close or linear correspondence between individual-level objective and perceptual indicators of deprivation. In addition, Hibbs' (1974) study of industrial strike activity contains serious implications for aggregate analysis of RD.12 He pools yearly timeseries data for ten nations in order to test different specifications of expectations-achievements gap arguments. Of three plausible representations of the gap between workers' expected and actual real wage changes, only one of them (in which expectations are based on a long- run increase parameter and on actual wage shifts over several previous periods) manifests much power in explaining strike fluctuations. However, the two weak models in Hibbs' analyses are important for present purposes. Despite several advantages of the RD criterion data compared to those of cross-national investigations-Hibbs' measures are dynamic (and permit explicit specification of how expectations are formed), more obviously salient to the population (in this case, workers)

11. It should be stressed that the core theoretical constructs in RD and RM treatments, respectively, concern individuals' perceptions and group formation and interactions.

12. Although labor-management disputes are not usually conceptualized as "collective violence," there is a very close correspondence between theoretical explanations of the two phenomena (Hibbs, 1974; Snyder, 1975; Shorter and Tilly, 1974).




at risk (than, say, indicators such as physicians per capita in Feierabend and Feierabend, 1966) and almost certainly measured with less error- two a priori plausible representations of RD are empirically inadequate. Given such results, the validity of aggregate measures of RD that employ objective indicators and less appropriate data surely warrants considerable skepticism.

Such criticisms are by no means limited to analyses of RD. Problems in testing mobilization theories with ecological data are more serious insofar as even heroic justifications for aggregate proxies of groups' collective control over resources are lacking. In fact, the only quantitative analyses of RM explanations of collective violence that employ ecological data (Snyder and Tilly, 1972; Lodhi and Tilly, 1973) are unable to include any empirical representation of the central mobilization variable. Moreover, the dynamic elements of groups' interactions specified in RM theory are entirely lost with such research designs.

It should be further emphasized that the levels of analysis issue is not only a problem of measurement validity, but also concerns the ambiguous interpretation of results where all measures are entirely valid. For instance, assume that governmental coercive capacity is perfectly reflected (it is not; see Hibbs, 1973: 85) in national budget or defense expenditures or coercive force sizes (e.g., Bwy, 1968; Gurr, 1968; Snyder and Tilly, 1972). Should a negative effect of such indicators be attributed to an increase in individuals' anticipated punishment for participation in violence (Bwy, 1968) or to greater costs of collective action for mobilized groups (Snyder and Tilly, 1972), or both, or neither? There is, of course, no unambiguous means of distinguishing among those alternatives with ecological data, and interpretations of such results typically reflect preexisting theoretical inclinations.

These problems of empirically representing the core RD and RM concepts (and those of other arguments as well) by far constitute the most serious impediments to close fits between quantitative research and theories of collective violence. But additional difficulties warrant mention, particularly since they are addressed by the alternative strategies proposed subsequently. While the following points have been developed elsewhere, they continue to be ignored by the large bulk of empirical work.

Several studies question the measurement of the dependent variable ("collective violence") in ecological analyses. Most researchers now recognize that newspapers and related sources of event data do not




adequately count and describe the behaviors of interest, and often employ multiple sources as a corrective. However, measurement error as a function of media bias remains problematic in many respects. Recent work indicates that (a) multiple sources are typically not independent insofar as they are mutually reliant on wire service reporting networks; (b) bias increases greatly with wider ranges of conflict behaviors included; and (c) the degree of underreporting of some types of events is enormous (e.g., Danzger, 1975; Snyder and Kelly, 1977). More- over, all of the efforts to reduce measurement error occur at the data collection stage; empirical analyses then proceed on assumptions of entirely reliable and valid indicators, even when there are strong con- trary suspicions. Given the resources invested in ecological measures of violence, it is both remarkable and disconcerting that virtually no research investigates the extent to which results and substantive conclusions are altered by measurement error.

Even less attention is accorded to specification of appropriate measurement models (e.g., Jacobsen, 1973), especially with respect to which indicators are included and the consequences of different opera- tionalizations across studies. Empirical treatments range from single indicators (e.g., Russett, 1964), to factor analyses of several dozen phenomena (Feierabend and Feierabend, 1966), to all events meeting certain criteria of size and damage regardless of "type" (Snyder and Tilly, 1972). As an example of plausibly important differences, Feiera- bend and Feierabend treat elections and cabinet changes as components of political instability, while Snyder and Tilly consider these indicators to be distinct from but causally related to collective violence. Dimen- sionality distinctions between partisan and elite violence raise similar issues that are at least now being recognized (Nardin, 1971; Gurr and Bishop, 1976; Morrison and Stevenson, 1973). But the standard factor analytic measurement models provide no real solutions. They are "unable to discriminate the covariation which arises because separate measurements represent partially overlapping indicators of a common underlying variable from that which arises between separate causally related variables" (Nardin, 1971: 21).

Individual-level studies do not require the detailed consideration given to ecological analyses because they are seldom proposed as complete tests of the arguments and, in any case, manifest problems similar to those already discussed (e.g., inferring RD from objective indicators). However, some criticisms of individual studies suggest more general




difficulties. For example, McPhail (1971) addresses weak relationships between a person's objective and subjective characteristics and measures of participation in racial disorders. He indicates that the typical individual's involvement is very intermittent and heavily dependent on situational factors such as interactions with other people and location with respect to the flow of events. Based on these observations, McPhail (1971: 1068) argues that the "singular and continuing tendency" implied in measures of prior attributes necessarily produces inadequate explanations of actual riot behaviors. Although McPhail focuses illustra- tively on racial violence, his points reflect broader criticisms of "formu- lating theory in terms of variables that describe initial states, on the one hand, and outcomes, on the other, rather than in terms of processes whereby acts and complex structures of action are built, elaborated and transformed" (Cohen, 1965: 9; cited in McPhail, 1971: 1070; Stark et al., 1974: 866; see Couch, 1970; Berk, 1974; McPhail and Miller, 1973, for similar arguments). Researchers often acknowledge the substantive importance of such "processes"-e.g., how individuals assemble in time and space for collective participation (McPhail and Miller, 1973; Weller and Quarantelli, 1973); patterns of escalation and deescalation after the initiation of violence; and the interactions that produce violence in some "intrinsically nonviolent" events and not in others (Tilly, 1970). However, critics concur that quantitative analyses either ignore or fail to capture these and other relevant processes.

In summary, the range and extent of problems in empirical treatments of the determinants of collective violence are quite serious. That is not to deny that conventional studies have any merits, or that some aggregate or individual-level investigations address hypotheses at the level of analysis on which they operate. However, considerable reorientation of empirical work appears necessary if past errors are to be avoided and further progress accomplished.

STRATEGIC ALTERNATIVES FOR EMPIRICAL INVESTIGATION

Not surprisingly, the proper cures are less obvious and tractable than diagnosing the ills themselves. However, alternative directions for empirical investigation of collective violence are specified or implied in




some recent research. These alternatives are developed according to the general categories of empirical problems identifed above.

(1) MEASUREMENT OF CENTRAL THEORETICAL CONSTRUCTS

Relative deprivation. Although RD is an individual-level theoretical construct and ecological approaches often suggest disaggregated measures (e.g., Gurr, 1970), serious attempts to index it with survey data are very recent. The Grofman-Muller (1973; see also Muller, 1972) study is novel in its use of both objective conditions and individuals"'expectations" concerning their welfare, and in relating the latter measures to an indicator of (potential for) political violence (PPV). Despite its importance in addressing RD more directly with perceptual indicators ("achievement deprivation," or AD) and demonstrating nonlinearity in the objective welfare-AD and AD-PPV relationships, the Grofman- Muller approach is not generally optimal. The cross-sectional survey evidence introduces possible biases (e.g., in retrospective assessments) and precludes identification of the exogenous conditions that affect individuals' perceptions (at a single time point, such conditions do not vary across observations). In addition, the dependent variable (PPV) reflects respondents' assessments of their probable behavior, on the assumption (from Gurr, 1970) of a direct causal linkage between potential for political violence and its manifestation. However, it is precisely such links between individual propensities and the occurrence of violent events that constitutes a central dispute between RD and RM approaches. '3 And, given the negative evidence on attitude-behavior consistency (e.g., Wicker, 1969), the Grofman-Muller results plausibly bear more on "political radicalism" attitudes than on political violence.

Miller et al. (forthcoming) retain this emphasis on perceptual measures, but make strategic advances in using such information. They employ repeated questions in the biannual Michigan election surveys

13. In fact, even if a strong relationship were demonstrated between individual AD and participation in violence, such findings could not by themselves indicate the relative importance of perceptual versus organizational factors. It would remain plausible that organizational variables are crucial in transforming the subjective states into collective events and that violence would not generally occur in situations which are comparable except for the absence of such mechanisms. The appropriate research design for investigating this alternative would require information on several settings, across which varia- tion in the organizational factors could be observed.




(1956-1968) to examine relationships between fluctuations in RD and the timing of racial disturbances. The time-ordering of these data permits analyses of (a) the correspondence between perceptions of deprivation and the extent of violence itself (rather than "potential"); and (b) the effects of changes in objective conditions on the perceived welfare of the subpopulations of interest. Furthermore, given the costs of initiating surveys and necessary lags in waiting for several "waves," as well as the increasing availability of comparable series (Glenn, 1973), such use of archival survey timeseries may be the most promising strategy for assessing RD at the individual level.

Despite these advantages, no survey design will by itselfconstitute an optimal strategy for isolating determinants of collective violence. For example, difficulties in ascertaining the relative importance of perceptual and organizational factors remain. An even more serious limitation is that appropriate survey information is not regularly available, particularly for historical and some comparative research.

Researchers will therefore necessarily continue to rely largely on ecological measures and tests of RD concepts, but need not repeat past strategic errors of aggregate data collection and analysis. For instance, economists' general work on the formation of price expectations (Toyoda, 1972; Turnovsky and Wachter, 1972) and related specifications of expectations-achievements gap models of strike fluctuations (Ashenfelter and Johnson, 1969; Hibbs, 1974; Snyder, 1975) indicate empirically feasible and substantively informed procedures. These studies employ timeseries information in which (typically economic) deprivation criterion variables, such as wage changes, are periodically observed. Measures of RD are constructed from these objective indicators on the plausible assumption that a population's current expectations are based largely on actual conditions over several previous periods. Substantively different expectations processes are represented by varying the time lags and weights assigned to them (e.g., very recent experience may be weighted more or less heavily).'4 These models'

14. In the simplest case, the difference between periods t-l and t are in some objective indicator makes the (usually unrealistic) assumption that current expectations are based only on the experience of the most recent period. However, analyses of collective violence might be informed by the findings of studies of industrial strike activity, which generally indicate tht the best fit is achieved with an inverted-U shaped lag structure (see Ashenfelter and Johnson, 1969; Hibbs, 1974, for details on underlying assumptions and model specification). It is also plausible that, in comparable analyses employing data for subpopulations within some national polity, the objective gap between "reference groups" should be incorporated in such RD specifications.




successful applications to industrial conflict (Ashenfelter and Johnson, 1969; Hibbs, 1974; Snyder, 1975) suggest their utility for investigations of theoretically similar phenomena such as collective violence.'5

Implementing this empirical strategy involves two further considerations. First, results from aggregate specifications do not necessarily indicate that people actually make the hypothesized economic calculations, only that they act as if they do (Ashenfelter and Johnson, 1969). Comparisons with the survey timeseries on perceptions would more conclusively validate aggregate procedures. Moreover, construction of mathematical representations of survey and aggregate measures in terms of the other would increase both the precision of and confidence in ecological proxy variables in the typical situation where only they are available. Second, these procedures obviously demand parallel development of timeseries information on collective violence as well as deprivation criteria. The very few attempts to provide data along these lines (Taylor and Hudson, 1972; Banks, 1971) are not entirely adequate because (a) measures of violence are limited to frequency and typically insensitive to the validity problems discussed earlier; and (b) economic and other indicators are not reported in a comparable (yearly) format (Taylor and Hudson, 1972), or else the intervening observations are often interpolated (Banks, 1971). Therefore, collection of timeseries data on political conflict and other variables with the care and detail generally reserved for single nation studies (e.g., Tilly, 1969; Levy, 1969) is required. But such efforts must be implemented for several countries in order to investigate the effects of institutional and cultural factors that cannot be captured in a single nation analyses (see Hibbs, 1974, for appropriate technical procedures with pooled timeseries). More generally, these considerations suggest a partial moratorium on the use of widely available cross-sectional data and reorientation toward developing longitudinal information that will more appropriately address the substantive arguments.

RESOURCE MOBILIZATION

Empirical representations of resource mobilization are still extremely primitive (e.g., usually limited to group membership as a global proxy).

15. The criteria for "successful applications" in this case include the consistency of results across studies, the sensitivity of findings to alternative specifications, and the strong relationship with the dependent variable.




My discussion therefore emphasizes general strategies of research design and data collection, and ignores the conceptual and methodological complexities that detailed measurement practices would require. 16 The measurement of mobilization actually involves two separate issues: first, identifying the conditions under which collectives will form (as well as the particular ones that will emerge from an enormous set of potentials) before they actually do; and second, measuring the collective control of resources by already identifiable groups.17 While there is some overlap in strategies, the first (labeled "protomobilization") issue is obviously less easily tractable.

As a first approximation to defining an exhaustive list of groups that could mobilize in some population, Tilly (1970: 11-12) proposes a strategy that entails identifying every status distinction (which implies a difference in "interests") employed in the population; generating the immense list of all combinations; and "eliminating those which have no real persons within them (e.g., Chinese-Jewish-cowboy-grandmother)." Tilly (1970: 12) concedes that such procedures are virtually impossible "for large populations organized in complicated ways," because the very detailed attribute and relational (interaction/communication network) data for each individual are unlikely to be available. Research on protomobilization processes will, at least in the short run,necessarily involve populations in which (a) the potential interest/ cleavage dimensions and total number of members are both relatively small and (b) relational data can be recovered for each person.

Those guidelines mitigate against studies randomly selected "natural" populations, and instead favor data collection in more strategically chosen settings. Natural sites that have fairly rigid boundaries constitute one viable option. For example, formal organizations are bounded settings in which numbers of potential interests and members may be

16. Such complexities are illustrated by the following questions: what should be included in an exhaustive list of resources that could be collectively controlled (mobilized) by groups? how should qualitatively different kinds of resources, such as loyalties, money, and weapons, be weighted in constructing collectivities' mobilization scores? how should "substitution effects" among different types of resources be calculated? should the weight- ing scheme vary across "types" of groups (i.e., are some resources intrinsically more valu- able to certain kinds of groups than others)?

17. In strict terms, mobilization is defined as an increase in collective control over resources [Etzioni, 1968; Tilly, 1970] (which also specifies some conditions under which demobilization occurs). In the present context, "mobilization" is considered to be the level of resources controlled by a group, which must be adequately measured before changes can be assessed.




limited by selection of cases.18 Moreover, characteristics of each individual in the "population" would be available (personnel records, questionnaires), and a full matrix of communications networks could be generated by observations and interviews. Opportunities for this type of study will also occasionally occur in settings isolated by ecological boundaries (e.g., Loukinen's [1975] analysis of networks in a Michigan farming community) or for which uniquely rich data exist (Aminzade, 1976).

Experimental designs in which the relevant parameters (population size, communication opportunities) may be constrained by the re- searcher are a second possibility. Gamson's effort (see Fireman et al. [1976] for a complete description) to induce rebellions-anticipated by his (1969) simulation game-is one promising approach. Of course, problems of external validity may be considerable, but the relative ease of gathering and analyzing experimental data may also inform subsequent investigations of protomobilization in natural populations.

Whatever the data collection strategy, RM and RD approaches suggest several plausible explanatory variables for models of the conditions under which this first stage of mobilization occurs. Such factors include the number of potential members (i.e., those who share the common interest or grievance), demographic (e.g., better educated people may have greater organizational skills), and perceptual (depriva- tions, loyalties) characteristics of individuals, the presence of leadership, communication patterns, and so on. In fact, the detailed information available in bounded settings may provide unusual opportunities to examine the relative importance of determinants specified by the alternative theoretical statements.

The measurement of mobilization in its "second stage"-i.e., assessing collective control over resources in already organized groups- presents less formidable difficulties. The very "visibility" of such groups increases the identifiability of the units of analysis, the feasibility of sampling operations, and the likelihood of existing documentary evidence. Assuming solution in principle of the problem of specifying

18. Zald and Berger (1978) demonstrate several analogues between macropolitical events and comparable phenomena that regularly occur in organizations but are rarely investigated there. Those analogues suggest the current strategy, which is opposite Zald and Bergers' (i.e., organizations may be convenient arenas within which to study processes that also occur in macropolitical settings).




which resources to measure (see Aminzade, 1973; Clark, 1968: 57-67; Tilly, 1970, for suggestions), procedures that generate such information for large numbers of groups over long time spans would be most desirable. Gamson's (1975) study of the conditions under which "challenging groups" gain entry into and advantages from the national polity most closely approximates these specifications. He employs a wide variety of historical accounts and sampling procedures to generate an unbiased list of protest groups and information on their characteristics (including the outcomes of their political challenges). Gamson's strategy approaches the ideal framework for generating data on mobilization processes, except for the important drawback that information on each collectivity is culled exclusively from the historical accounts. These accounts are sketchy (even group size, the most frequently reported indicator, can be coded only in crude intervals), as they will be for any random sample. Moreover, the temporal dimension is at- tenuated because data are not available at regular period-to-period intervals.

Modifications of Gamson's strategy must develop far richer detail of information while preserving the essential design of following groups over time. As in the analysis of protomobilization, only "samples of convenience" in this case, explicitly choosing groups for which data sources such as membership lists, financial statements, and so on, are known or likley to exist-will generate the necessary information. The bias introduced by such procedures is obvious (Gamson, 1975: 22-23). However, difficulties arise not because of sampling bias per se but in the (frequent) circumstance that the direction and extent of the bias (and therefore the validity of inferences to the population of interest) are unknown. In light of that consideration, researchers could implement a dual strategy that incorporates the advantages of representativeness and detailed information. First, Gamson's methods could be used to define the entire population of groups and make rough assessments (from the secondary accounts) of characteristics, such as size, success, and so forth, for a sample of them. Data could then be collected for a second sample of well-documented collectivities to be analyzed intensively. Analyses of the latter would be weighted according to differences in comparable characteristics of the biased and unbiased samples.

Although empirical representation of collective resource control is the principal issue in quantitative testing of RM arguments, two related matters warrant brief mention. The first deals with the employment of




these longitudinal data once they are collected. A pooled timeseries design (see Hibbs, 1974) in which fluctuations in groups' measured level of mobilization are related to their (sometimes violent) collective actions is the most appropriate analytic framework. This, of course, assumes that data on actions of each group are available from the newspaper, archival, and secondary sources whose use has become standard (see Jenkins and Perrow [1977] for a recent group-specific example). Second, the relationship between mobilization and collective violence (as well as levels of each) should vary according to several other factors (e.g., a group's political position, the "openness" of the polity, repression). While measurement of these additional variables is important, a detailed treatment is not strictly necessary insofar as (a) such measures can be easily incorporated into the longitudinal design specified above and (b) preliminary indexing procedures have been developed. For example, Pearson (1970) employs the number and content of discussions concerning all groups mentioned in roll call votes of the French Chamber of Deputies as a rough measure of these collectivities' political positions,19 and a variety of strategies for representing governmental coercion exist (e.g., Taylor and Hudson, 1972; Jenkins and Perrow, 1977). This is not to claim either that the procedures involved will be anything but labor-intensive or that the finer points of measurement have been satisfactorily worked out. However, two points should be stressed: first, that the data and methods for intensive research on mobilization are available in fact rather than "in principle"; and second, that such investigation must be undertaken if RM arguments aie to be empirically specified and tested.

(2) PROBLEMS OF INFERENCE

While the foregoing prescriptions for measuring the independent variables of RD and RM arguments should alleviate improper construction and interpretation of empirical models, two further sources of ambiguous inference must still be addressed. Both of them are related to level of analysis problems. The first deals with more refined testing of

19. Tilly (1977) provides a detailed and more accessible report of these procedures, their limitations (e.g., such methods are "best suited to the detection of groups whose position is changing, rather than [those] calmly enjoying long-established benefits"), and some alternative strategies.




the "indirect linkages" (represented by dotted lines in Figure 1), specified by various arguments. For example, longitudinal data on groups and aggregate economic timeseries could indicate whether mobilization levels tend to increase in prosperous times, but not whether that occurs because individual members of those groups have more resources upon which collective claims can be made (linkage EF). The second and more important issue concerns empirical adjudication among alternative arguments where the respective concepts of interest are (assume perfectly) measured at different levels of analysis. Consider, for instance, the situation where timeseries survey data on relative deprivation and mobilization information for a sample of groups are available. A critical test of these alternatives would require the inclusion of both measures in the same analysis. But in most cases there will be a lack of fit between the populations "at risk" in the respective indicators and consequent difficulties in undertaking such tests.

The ideal solution to both of these problems is the accumulation of data on large numbers of groups, individuals, and the links between them. However, it is again unrealistic to expect such data to be readily accessible. A more tractable procedure is employment of mobilization and deprivation indicators which fortuitously apply to the same (sub)- population and to aggregate one set of measures to correspond to the level of analysis of the other. The timeseries investigations of industrial conflict cited earlier, in which labor organizations are the relevant groups, provide an example of this strategy. Wage series aggregated from survey data have been used to construct measures of labor's expectations-achievements gap, which are then incorporated with union membership indicators of mobilization in a single analysis (e.g., Snyder, 1975). However, it need not always be the RD measures that are aggregated. Consider a national-level representation of an expectations- achievements gap that is known to be valid (on the verification recom- mendations proposed earlier). In this case, procedures for constructing an aggregate series of mobilization scores (i.e., summing over all groups for each observation period) could be implemented. The general point concerning ambiguous results and inferences is that problems of "fit" between units of analysis should be resolved by measuring the concept of interest at the appropriate level and then aggregating if necessary. This strategy is opposite the conventional (and highly dubious) one of inferring umeasured group- or individual-level phenomena from aggregate indicators.




(3) MEASUREMENT: DEPENDENT VARIABLE

Previous criticisms of collective violence measures identified two problems: (a) measurement error, particularly differential underreporting across types of events and ecological units; and (b) dispute, largely engendered by different substantive models, concerning precisely which indicators should be included in "collective violence" (or related phenomena). Some of the alternative research designs suggested above will reduce these problems to an extent. For instance, the strategy of following collectivities over time would specify groups' involvement in violence as the dependent variable. Therefore, certain often included event types that pertain to political systems (e.g., national elections, cabinet changes) would not be incorporated in "collective violence" on logical grounds. However, that is in no sense a solution, particularly because much research will necessarily continue to rely on aggregate (ecological) data.

First consider the specification issue, which has not been empirically tractable because standard ("exploratory") factor analysis cannot discriminate among alternative causal structures (e.g., Nardin, 1971). For example, assume (for the moment, perfectly measured) four standard indicators: the number of riots, civil wars, cabinet changes, and elections for some sample of nations. Figures 2a and 2b present two simple causal models which characterize predictions of RM (Snyder and Tilly, 1972) and RD (Feierabend and Feierabend, 1966) theories of violence or political instability, respectively. A factor analysis of all four indicators could not choose between models 2a and 2b. Although a priori decisions to delete or include cabinet changes and elections as indicators of the (bracketed) unmeasured construct are of course possible, there are simply no consensual substantive criteria for such decisions.

Some possibility for settling these disputes derives from methods developed by J6reskog (1969, 1970) and his collaborators (Werts et al., 1973; Jdreskog and Van Thillo, 1972) for the analysis of structural equations models that include multiple indicators of unmeasured variables. While the cited works fully explicate the details of these techniques (sometimes labeled "confirmatory" factor analysis), their advantage over standard approaches may be briefly summarized. First, a single (maximum likelihood) procedure is used to estimate an entire system of coefficients (equations), including those pertaining to the




(a)

EXOGENOUS VARIABLES

Cabinet Changes[C follective Violence]

National Election

Riots Civil

Wars

(b)

EXOGENOUS VARIABLES -[Political Instability]

Cabinet National Riots fivil

Changes Elections Wars

Figures 2a and 2b: Alternative Causal Models of Interrelationships Among Selected Political Variables

unmeasured factors. This contrasts with the typical situation in which factor scores are calculated and only then included in the desired analyses. More important, Jdreskog's methods provide a (chi-square) goodness of fit measure which tests the null hypothesis that the posited causal structure could have generated the observed interrelationships in the data at a given probability level. The relative goodness of fit achieved by alternative specifications such as those in Figures 2a and 2b may be evaluated. Moreover, assumptions concerning measurement error are easily incorporated, and the fit of entire models may be assessed according to differential indications of the location and degree of such error.

Despite the obvious utility of these empirical techniques, substantive criteria cannot be neglected in constructing and estimating measurement models of collective violence. For example, indicators of official force should not be included in measures of collective violence and of coercion (as in Feierabend and Feierabend, 1972). There are strong arguments (that cross-cut most of the theoretical approaches) for treat- ing violence and repression as conceptually distinct but mutually




dependent variables (Nardin, 1971; Tilly, 1975; Gurr and Duvall, 1976; Hibbs, 1973). Similarly, guidelines that specify the conditions under which particular indicators of conflict events are likely to be invalid (e.g., Snyder and Kelly, 1977) will inform efforts to capture the effects of measurement error in these models. Greater attention to these issues is mandatory if the results and conclusions of ecological analyses of collective violence are not to be vitiated by improper measures of the dependent variable.

(4) INTERACTION AND PROCESS VERSUS INPUT-OUTPUT ANALYSES

Most empirical analyses of collective violence-including the alternatives proposed here-primarily attempt to explain how much violence will characterize groups, nations, and the like. These analyses generally (even necessarily) specify some "outcome" variable (frequency or magnitude of violence) in terms of prior characteristics of groups, areas, and the like. Researchers who are critical of such "input-output" studies for neglecting processes typically address questions concerning how rather than how much violence (more broadly, collective behavior) occurs. In doing so, they generally focus intensively on single episodes of crowd behavior, often use observational methods, and attempt to understand the interactions of individuals with each other and the immediate ecological environment (cf. McPhail and Miller, 1973; Berk, 1974; Couch, 1970; Stark et al., 1974, which illustrate various approaches to crowd dynamics).

Although the purpose of these studies has largely been empirical assessment of theoretical statements on crowds per se, several points of

direct relevance to the determinants of violence provide strong warrants for pursuing this relatively neglected line of inquiry. First, studies of interaction and process can be quite useful in theory construction. For example, McPhail and Miller's (1973) examination of assembling processes explains "mobilization" for certain (spontaneous) forms of collective violence that conventional RM perspectives treat inade- quately. They argue that the occurrence of (in this case, nonperiodic) asemblies or collective events depends on the interaction of three broad classes of factors: (1) "instructions" or "cues" (both verbal and non-

verbal); (2) the availability of individuals in time and space; and (3) the




propensities of those individuals to respond toward rather than from the cue. Specifically, certain events (e.g., hostile police-citizen encounters in racial disorders) constitute nonverbal instructions to assemble for individuals within visual and/or aural proximity. The likelihood that individuals will be "available" depends on the distribution of their activities (e.g., extent of competing demands) in time and space. Participants are also "mobilized" indirectly, through verbal instructions transmitted via informal communications networks. McPhail and Miller demonstrate that this account of how assembling occurs is consistent with a variety of evidence on patterns of racial disorder participation and related phenomena.

Two further justifications for investigating event dynamics have not been explicitly recognized by analysts of crowd behavior, but illustrate even more direct linkages to quantitative analyses of violence. Once violence initiates, patterns of interaction among individuals and/ or groups (including authorities) are likely important in determining regularities of escalation and deescalation. Knowledge of those regularities should inform empirical studies that incorporate dimensions of violence (e.g., participants, damage, duration) other than frequency. Spilerman (1976) and Bergesen (1976) provide preliminary examples that indicate the significant effects on riot severity of temporal shifts in police tactics.

Finally, there are further possibilities for integrating "process" into quantitative analyses of the occurrence (i.e., frequency) of violence. For instance, McPhail and Miller's description of how assembling occurs can be extended to construct a model of the probability (i.e., how much) of violence across ecological units. In the case of racial disorders, frequency could be specified as a function of intercity differentials in (a) the probability of a precipitating incident or "nonverbal cue" to assemble (see Morgan and Clark, 1973: 616-617, for modeling suggestions); (b) the "availability" of persons for assembling (e.g., number of young or unemployed black men); (c) ecological conduciveness to assembling at the scene of a precipitating incident (e.g., the number of major intersections within ghetto areas, coded from detailed maps, or patterns of housing concentration); and (d) the density of informal communications networks (possibly represented by ghetto population densities, though this is the weakest of all these proxy measures). Such a model plausibly interprets the (substantively equivocal) effect of non- white population size that predominates empirically in ecological




studies of disorder proneness (e.g., Spilerman, 1970, 1971). While the measures of the relevant conditions that facilitate assembling are admittedly crude, they indicate a potentially promising direction for merging qualitative analyses of crowd dynamics into quantitative ecological treatments.20 This is not to claim that "processes" per se can be directly captured in such studies. It does suggest that specifying the conditions under which such processes are likely to occur can both inform substantively and improve empirically models of collective violence.

The alternative strategies advocated here range from longitudinal surveys of individual perceptions to intensive analyses of organized groups' life histories to examinations of crowd dynamics. Perhaps the only common features of these strategies are their reliance on types of data that are less readily available than those usually employed and their consequent labor-intensive character. But given the difficulties of conventional empirical approaches, methodological shifts in the directions proposed here must be implemented if the continuing problematic issues in collective violence are to be adequately addressed.

A NOTE ON THEORY

Although this paper has been oriented toward quantitative strategies, a brief note on theory is warranted because it guides the design and interpretation of empirical research. In particular, the most serious impedi- ment to further advances in theories of collective violence is the general (though sometimes implicit) assumption of universal applicability in each line of argument. Such assumptions appear untenable in view of contradictory empirical findings on the major approaches and some evidence (e.g., Snyder, 1975) that explicitly indicates differential validity of RD and RM arguments according to variations in structural settings.

In light of these considerations, two alternative theoretical strategies are more promising. One is theoretical integration of alternative

20. Snyder (forthcoming) provides a (partially complete) application of these procedures, but one that still indicates their empirical superiority over conventional ecological models of the distribution of racial disorders across cities.




approaches.2' Korpi's (1974) "power balance" model of political conflict is illustrative. While not yet empirically tractable, the power balance model is theoretically appealing because it introduces more behavioral content (via motivational components and actors' calculations) than most RM arguments while continuing to specify the mechanisms through which collective action occurs. Equally important for present purposes, Korpi's treatment plausibly reconciles contradictory empirical evidence in that his integration of RD and RM approaches generates empirical predictions that differ from those of either argument separ- ately (1974: 1576).

A second possibility concerns specification of the structural conditions or "critical dimensions" across which the validity of explanations varies. For example, the relationship between income inequality and political violence (e.g., Sigelman and Simpson, 1977) likely depends on a nation's economic structure (predominantly agricultural versus industrial), which in turn determines the relative salience of income versus other inequality criteria (e.g., land) for individuals' perceptions of deprivation. As another case in point, the applicability of conventional mobilization theories (Tilly, 1975) appears to vary according to the degree of centralization associated with particular forms of collective action. RM variables' strong empirical relationships with highly organized forms of conflict such as strikes (Shorter and Tilly, 1974; Snyder, 1975) and their inability to account for spontaneous events of the type specified by McPhail and Miller (1973) support that conten- tion. Similarly, RM arguments (e.g., Tilly, 1975; Gamson, 1975; McCarthy and Zald, 1977) have been developed largely in the context of Western political processes and may not hold so well elsewhere. Addi- tional hypotheses could of course be suggested. But the point to be underscored is that conditional theories along these lines constitute more promising strategies for organizing, explaining, and generating further empirical work. Attempting to fit all results within one or another of the major arguments is simply not a tractable endeavor.

21. Despite some important trends toward convergence (e.g., Gurr and Duvall, 1976; McCarthy and Zald, 1977), most efforts to do so still fall mainly within one line of argument (either RD or RM). Similarly, multivariate causal analyses, such as Hibbs (1973), should not be considered as theoretical integration.




CONCLUSIONS

The general prescriptions for research on collective violence offered here strongly suggest shifts toward "disaggregated" treatments, both theoretically and empirically. No theoretical explanation as currently formulated is universally valid. Even more modest attempts to explain certain relationships (e.g., between coercion and violence) rather than "violence in general" should avoid assumptions of relational univer- sality that characterize most analyses.

Similarly, there are compelling reasons for disaggregation in empirical investigations of collective violence. Many difficulties in quantitative studies stem from attempts to measure relevant conceptual variables at (aggregate) levels of analysis other than those (individuals, groups) at which they are formulated. Probably the most important methodological guideline is to measure core concepts with respect to the appropriate units of analysis. This prescription does not mean that aggregate studies should be expunged from researchers' analytic repertoires. In some cases they may constitute the logically most suitable level of analysis. In others, aggregate investigations will be necessary if not optimal, but can be undertaken with some confidence if the measures employed have either been independently validated or cumulated from data gathered at the appropriate level. Another necessity that trans- cends all of the specific research strategies concerns development of longitudinal data and implementation of time-ordered analyses. Although virtually every substantive argument is specified in dynamic terms, cross-sectional investigations continue to dominate empirical work on collective violence.

These global summary statements are not to claim that all relevant issues in the determination of collective violence have been considered. In particular, relationships between (1) international linkages (including but not limited to conflict) and domestic violence and (2) violence and "social change" are two areas of inquiry that are potentially very salient to the central concerns of this paper. The former is ignored partly in view of the practical considerations imposed by the enormous literature on international-domestic linkages, but more so because the bulk of empirical work has yet to demonstrate regular strong effects of international on domestic conflict (as conventionally measured). Conse- quently, an implicit assumption of the present treatment is that the




major influences on collective violence are located within national political systems, or at least that exogenous determinants are largely mediated by intranational factors. This assumption may of course be proven wrong, either by new developments in the study of international and domestic conflict, or by research which examines the impact of other types of transnational linkages on domestic violence. For example, some recent empirical work indicates both the influence of international economic dependency on domestic economic growth and inequality (Chase-Dunn, 1975) and the importance of patterns of export agriculture for understanding third world agricultural protest movements and revolutions (Paige, 1975). This evidence suggests the promise of further research on such linkages.

The relationship between violence and social change (more broadly, collective action and its outcome) is not only largely neglected (see Eckstein, 1965: 136; Bienen, 1968: 66; Gamson, 1975: 73; Marx and Wood, 1975: 403), but also treated as an issue entirely separate from the determinants of violence. However, some analyses indicate that the two issues must be explicitly linked for the informed treatment of either. For example, Snyder and Kelly (1976: 134) demonstrate the conceptual and empirical utility of an approach which specifies "the preconditions, occurrence and consequences of violence as a temporal process in which consequences depend on the preconditions as well as the violence itself." It is also possible to venture considerably beyond the argument for inter- related analyses, on the grounds that the consequences of violence in turn should have direct effects on groups' mobilization of resources, individual perceptions, and so forth at subsequent points in time.

Despite the potential importance of these additional issues, the research agendas concerning appropriate theory, measurement, and analysis are simply more immediately pressing. Concerted efforts to reformulate conceptual and methodological approaches to these central questions must take priority if substantial progress is to be made in analyzing and understanding collective violence.

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David Snyder is Associate Professor, Department of Sociology, Indiana Univer- sity. His primary research endeavors are in the comparative and historical analysis of changes in the frequency and form of collective protest and violence.



collective violence: a research agenda and some strategic considerations

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