Toward a Political Model of Incarceration: A Time-Series Examination of Multiple Explanations for Prison Admission Rates

by David Jacobs, Ronald E. Helms
Toward a Political Model of Incarceration: A Time-Series Examination of Multiple Explanations for Prison Admission Rates
David Jacobs, Ronald E. Helms
The American Journal of Sociology
Start Page: 
End Page: 
Select license: 
Select License

Toward a Political Model of Incarceration: A Time-Series Examination of Multiple Explanations for Prison Admission Rates '

David Jacobs and Ronald E. Helms

University of Oregon

This study examines yearly shifts in prison admissions since 1950. The effects of ~olitical and economic determinants are investigated


with measures of economic inequality, political variables, and unem- ployment. The delayed effects of broken families are measured with a lagged moving average of out-of-wedlock births. The findings show that inequality due to the presence of the rich and past out- of-wedlock birth rates matter, but unemployment is not related to prison admissions. The strength of the Republican Party and a presi- dential election year dummy also explain shifts in incarcerations. The results suggest that earlier work omitted theoretically important explanations.

Why does the punishment rate fluctuate in modern societies? This ques- tion is intriguing for many reasons, but perhaps the most critical is its relevance to sociological theory. The theorists who tried to construct a comprehensive theory of society were forced to address the Hobbesian question, How is order possible? Durkheim and Weber devoted consider- able attention to social control and to the sociology of law, and many contemporary scholars use explanations derived from Marxist and neo- Marxist perspectives to explain outcomes in the criminal justice system. Images of social control and of punishment are fundamental to grand theory.

Some modern followers of the grand theorists (Chambliss and Seidman 1980; Black 1976; Collins 1975; Turk 1969; Vold 1958) suggest that the existing social order is at least partly the result of latent political divisions created by inequality. According to this political approach, the lower class realizes the least gains from the stratified economic arrangements that

' We thank Theodore Chiricos, Allen Liska, Robert Mauro, Jim Moody, and Robert O'Brien for their helpful comments on prior drafts and Stephen Haynes and Joe Stone for their advice. Address correspondence to David Jacobs, Department of Political Science, University of Oregon, Eugene, Oregon 97403-1284.

O 1996 by The University of Chicago. All rights reserved. 0002-9602/97/10202-0001$01.50

AJS Volume 102 Number 2 (September 1996): 323-357 323

persist in current societies. It seems plausible that an expanded racial or

economic underclass with little to lose could destabilize the social order

that benefits the affluent so much. Many sociologists therefore suggest that

the criminal justice system primarily exists to control the elements of an

economic or racial underclass who threaten existing arrangements with

predatory behaviors.

A core assumption in this view is that the control of crime is fundamen- tally political. Instead of seeing the criminal justice system as impartial, these theorists claim that criminal justice organizations rarely act against dominant interests. If criminal justice outcomes are shaped by economic differences, as some political theorists allege, the rate of punishment should move in response to shifts in racial and economic cleavages after other determinants have been held constant. In contemporary societies, the degree of economic and racial stratification fluctuates substantially even within a few years. We therefore examine the effects of these shifts on prison admissions since 1950 in one advanced society.

Garland aptly summarizes some of the advantages of this political ap- proach to social control when he says that it makes us "prepared to analyze punishment not in the narrow terms of the 'crime problem' but instead as one of the mechanisms for managing the urban underclass. . . . In this broader view, criminal penal measures are shaped not just by patterns in criminality . . . but primarily by governmental perceptions of the poor as social problems and the preferred strategies for their treatment. . . . The embeddedness of these forms within wider strategies of rule is the point most crucial for their comprehension" (1991, p. 134). In this study we gauge the accuracy of this and other political perspectives with indicators that measure shifts in political climate and changes in the degree of eco- nomic and racial stratification, but we also assess the explanatory power of alternative explanations.

There is an equally plausible account for changes in the imprisonment rates. Instead of emphasizing economic or racial cleavages and political repression, some theorists have forcibly argued that family breakdowns and the resulting disruptions in socialization led to substantial increases in the amount of crime and heightened requirements for formal social control (although Sampson and Wilson [I9951 argue that shifts in public policy caused these disruptions). We assess this family breakdown hypoth- esis by looking at shifts in the relative amount of lagged out-of-wedlock births to see how well this explanation accounts for changes in prison admissions.

Even if alterations in the rate of punishment were not so theoretically important, this outcome would be interesting because it has expanded so dramatically in recent years. After fluctuating between 43.4 and 50.9 per 100,000 between 1948 and 1965, the rate of admissions to U.S. federal


----Prison Admissions per Capita

FIG.1-Variation in the imprisonment rates over time

and state prisons dropped to 35.9 in 1968. It almost doubled in the next 13 years reaching 69.7 per 100,000 by 1981. In just eight more years this rate showed another dramatic increase, rising by 84% to 127.9 in 1989 (see fig. 1).

This substantial escalation in the use of incarceration is not matched by equivalent movements in the crime rates. From 1947 to 1975 reported crimes grew rapidly, yet they only increased by 12.1 % from 1975 to 199 1. The immense expansion in the number of incarcerations is not restricted to the United States. Cohen (1985) claims that incarceration rates in most of the industrialized democracies have risen substantially, although Sa- velsberg (1994) shows that Germany is an exception (for more information about U.S. shifts, see Blumstein [1993]). With these comparisons in mind, we wonder why imprisonment has become so popular, particularly in the United States, and study this question with time-series regressions applied to yearly data on prison admission rates since 1950.

The empirical research on incarceration suffers from a focus on single- factor explanations (Garland 1991). For example, Blumstein and his col- leagues investigated Durkheim's stability-of-punishment hypothesis (Blumstein and Cohen 1973; Blumstein, Cohen, and Nagel 1976). They concluded that it was invariant, yet the current immense increase in ad- missions and analyses by Berk and his colleagues (1981, 1983) cast doubt on this claim. Most subsequent research was motivated by Rusche and Kirchheimer's (1939) neo-Marxist argument that imprisonment is used to

control the excess supply of labor in capitalist economies (for examples of

the few recent studies that did not focus on unemployment, see Sutton

[I9871 or Savelsberg [1994]).

Many researchers investigated the neo-Marxist claim with aggregate data to see if there is a positive relationship between unemployment rates and imprisonment. The results have not been convincing. Perhaps be- cause the underlying connection could be more substantial, investigators used words like "elusive" (Melossi 1989), or "contradictory" (Michalowski and Pearson 1990; Parker and Horwitz 1986) to describe this association (Chiricos and Delone 1992). When they reviewed the literature, even pro- ponents like Chiricos and Delone find that only 60% of the 147 reported relationships between unemployment and imprisonment are positive and statistically significant. Perhaps the association between unemploy- ment and incarceration rates is too weak to survive rigorous competitive tests.

For these reasons, a design that assesses alternative hypotheses about fluctuations in prison admissions therefore may be more useful than an- other study that focuses primarily on the effects of unemployment. In this investigation we do not ignore unemployment, but we also examine the effects of political, economic, and socialization hypotheses that have been largely (if not completely) overlooked in prior studies. In addition to the effects of political determinants and several forms of economic stratifica- tion, we look at lagged changes in illegitimacy to see which of these diverse explanations account for subsequent fluctuations in the incarceration rates. We also difference all variables to remove the potentially spurious effects of shared trends.

One caveat is in order before proceeding. Because our goal is to be inclusive and to assess many competing explanations, the theoretical sec- tion cannot focus on just a few hypotheses. This investigation therefore examines how yearly prison admission rates respond to prior shifts in po- litical determinants, economic and racial cleavages, unemployment, and out-of-wedlock births in the United States since 1950. Exhaustive specifi- cations have important methodological advantages (Johnston 1984, see n. 14). Hence one strength of our complex design is its evaluation of more explanations than most (if not all) of the prior longitudinal studies. An- other is our use of first differences to avoid spurious relationships often produced by trended variables.


Latent Political Divisions: Economic Cleavages

Neo-Marxist perspectives on punishment suggest there is an association between inequality and public policies that maintain order. Chambliss

and Seidman (1980, p. 31) claim, for example, that "the more economically

stratified a society becomes, the more it becomes necessary for dominant

groups to enforce through coercion the norms of conduct that guarantee

their supremacy." Large differences in economic resources are seen as poten-

tially destabilizing, endemic attributes of class-based capitalistic societies.

Garland (1990, p. 123) completes this argument for a relationship be- tween economic inequality and incarceration when he says, "Penal law, at base, concerns itself with social authority and the governing claims of those with power. It reinforces these claims by means of coercive sanctions as well as symbolic displays. . . . Where social power and authority are structured upon class lines . . . then punishment will reproduce the forms and figures of class even when its actions appear to transcend class divi- sions and protect those on the wrong side of the class divide." According to Garland and others, punishment helps reproduce an unequal social or- der. If this political explanation is accurate, fluctuations in the amount of economic stratification can be expected to lead to subsequent shifts in the number of incarceration^.^

The logic of exchange provides another theoretical link between eco- nomic inequality and punitive control measures. In societies where pro- duction is extensively coordinated by markets, exchange imbalances will be common. As Blau (1964) notes, redistributive violence is one method dependents can be expected to use to overcome their disadvantaged posi- tion in unbalanced exchange relationships. This possibility should be ob- vious to political authorities. When economic differences between the rich and the poor widen, the threat posed by the "dangerous classes" may inten- sify, and criminal justice officials may respond with harsher punishments, even after the amount of crime is held constant. According to both neo- Weberian and neo-Marxist accounts, heightened economic differences be- tween the rich and the poor should lead to enhanced penalties, so imprison- ment rates should expand after increases in economic stratification.

An earlier cross-sectional study of imprisonment rates (Jacobs 1978) reports suggestive evidence. After holding other effects constant, this study shows that U.S. states with the highest levels of inequality were most likely to imprison property offenders. In additional cross-sectional work, Liska, Chamblin, and Reed (1984), Williams and Drake (1980), and Swanson (1978) report that crimes are more likely to be cleared by arrests in unequal cities. Results from cross-sectional designs may not hold in time-series investigations, but these findings provide additional reasons

Of course, we make no claims that we will test aMarxist or a neo-Marxist a~oroach to


punishment. What we can provide, however, is an empirical appraisal of one reasonable inference from neo-Marxist and neo-Weberian notions that ~ronounced economic cleav- ages lead authorities to respond by increasing the probability of incarceration.

for thinking that heightened economic stratification should lead to in-

creased imprisonments.

But what kind of inequality is most important? Two possibilities seem

equally plausible. First, during the period under study, an impoverished

urban underclass increased substantially in the United States. Second, the

economic resources of the rich grew rapidly compared to the resources of

all others during the same period. As Jasso (1979) notes, empirical compar-

isons of the effects of different gaps in distributions as gauged by disparate

inequality measures can be theoretically instructive. In this instance the

kind of economic inequality that best predicts incarceration rates should

be theoretically interesting because contrasts in these relationships may

furnish more precise information about the exact divisions that lead to

shifts in the imprisonment rates.

If an indicator of inequality that is most sensitive to the gap between the poor and middle-income recipients predicts imprisonment better than alternative measures, the threat posed by an expanding economic under- class becomes a more credible explanation for increased incarceration rates. But if a measure of inequality with a greater sensitivity to the gap between incomes of the rich and all other income recipients is a better predictor of movements in the imprisonment rates, such results would support a hypothesis that authorities who controlled the criminal justice system were most responsive to the affluent and their expanding economic resources.

Both neo-Marxists (Chambliss and Seidman 1980) and neo-Weberians (Collins 1975; Blalock 1967) claim that power in modern societies is at least partly based on comparative differences in monetary resources. If this plausible assertion is correct, increased differences between the eco- nomic resources of the rich and other classes should increase the power of the rich and their ability to influence the criminal justice system. Heightened inequality therefore gives the affluent both the need (Garland 1991; Chambliss and Seidman 1980; Blau 1964) and the capacity (Cham- bliss and Seidman 1980; Collins 1975; Blalock 1967) to enhance the sever- ity of responses to crime during periods when their economic share is in- creasing and, as a consequence, they become more attractive targets.

Another Latent Political Division: Racial Cleavages

An additional but equally important explanation for incarceration rates stresses racial divisions. Work on the police, for example, shows that cities with greater numbers of blacks have more police per capita (Jacobs 1979; Liska, Lawrence, and Benson 1981), or they spend more for police protec- tion (Jackson and Carroll 1981; Jackson 1989). A study by Liska, Law- rence, and Sanchirico (1982) supports this interpretation: after holding the crime rate constant, Liska et al. found fear of crime to be closely associated

with the percentage of African-Americans in cities. The percentage of

blacks or nonwhites does not change much over time (but see n. 12 below),

so it may not be associated with the prison admission rate. We therefore

assess a second, equally plausible version of the racial threat hypothesis

as well.

When income differences between the races increase and the potential dangers presented by a predatory minority underclass become greater, racial threat explanations suggest that subsequent expansions in the im- prisonment rates can be expected. We assess the effects of racial cleavages with the ratio of median family incomes of nonwhites and whites. When nonwhite incomes become a larger fraction of white incomes, punitive measures to maintain order should be less necessary, but when economic gaps between the races widen, the threat posed by a racial underclass should be enhanced, so this ratio should take a negative sign. Finally, we include the unemployment rate, so we can assess the neo-Marxist hypothe- sis that incarceration is used to control the supply of labor.

Direct Political Explanations: Partisan and Electoral Effects

Recent developments in political sociology suggest that political processes are not simple derivatives of social and economic arrangements (Evans et al. 1985). State managers often act autonomously, and their effective- ness may be enhanced during periods when the electorate is especially receptive to their agenda. Using a longitudinal analysis that held reported crimes and media attention constant, Beckett (1994) found that initiatives emanating from political officials were the most important determinants of public concerns about crime, although she argues that the public must be receptive. Political factors therefore may have independent effects on prison admissions. Many theorists see punishment as inherently political (Garland 1990; Savelsberg 1994; Blumstein 1993; Scheingold 1991), so we correct the neglect of these explanations in the prior empirical research by including two direct measures of political effects.

One way Republican candidates can expand their appeal to lower- middle-class and working-class individuals who do not benefit as much as the affluent from Republican economic policies (Hibbs 1987; Blank and Blinder 1986) is to campaign on a law and order platform (Chambliss 1994). An emphasis on punishment fits with Republican beliefs about indi- vidual responsibility. It has been widely alleged as well that law and order appeals allow Republicans covertly to invoke antiminority sentiments and thereby capture additional blue-collar, lower-middle-class, and Southern votes. In any case, assertions that the Democrats have been "soft on crime" have become an integral part of Republican campaign appeals since 1964 (Chambliss 1994; Scheingold 1991).

The behavior of Republican incumbents has been consistent with their

rhetoric. Republican officials at all levels tried to enhance the severity of

punishments. Caldeira and Cowart (1980) hold crimes constant and find

that, in direct contrast to Democrats, Republican presidents since 1935

have increased appropriations for corrections and total federal criminal

justice expenditures. To increase crimes cleared by arrests, Republicans

have provided greater resources for local police departments and state

prisons, and they have imposed longer mandatory sentencing provisions.

We control for the presence of Republican officeholders at various govern-

mental levels, but we weight the presence of a Republican president

heavily because this office is so influential in shaping public concerns

(Chambliss 1994; Scheingold 199 1) and because Republican presidents

have launched so many policies that have increased incarcerations (Cham-

bliss 1994; Caldeira and Cowart 1980).

Yet demands for severe measures may emanate from nonelites. To gauge public support for the law and order party and for the ideological determinants of imprisonment policies stressed by Savelsberg (1994), we use yearly fluctuations in the percentage of people who identify as Repub- licans. This measure is the most powerful indicator of partisan effects in the political science literature on voting (for reviews supporting this claim, see Shively [1980], Miller [1991], and Keith et al. [1992]) and therefore is the best continuously available measure of electoral support for the law and order party. For these reasons, we combine the presence of Republi- can officeholders at various governmental levels and the percentage of people who identify as Republicans to assess both the effects of political influence conferred by incumbency and the ideological effects stressed by Savelsberg (1994).

It would be equally interesting to see if the introduction of law and order appeals into presidential campaigns has effects on incarceration in the year after an election. If one party consistently campaigns on a popular law and order platform- as the Republicans have since 1968-incum- bents from the opposite party should find that electoral success will be jeopardized if they do not enact severe responses to crime as well (Dionne 1991).

Because electoral effects on imprisonment should be particularly salient immediately after presidential elections, we follow the precedent estab- lished in the large empirical literature on how competition for votes during campaigns determines subsequent macroeconomic outcomes (see Willett [I9881 and Nordhous [I9891 for reviews) in order to see if electoral rivalries lead Democratic and Republican administrations to enact policies that strengthen punitive responses to crime during campaigns for national of- fice. Most of the researchers who tested these political business-cycle mod- els used a lagged dummy to measure the effects of election-year rivalries on subsequent economic growth and inflation. Caldeira (1983) finds that such a nonpartisan electoral effect predicts federal outlays for criminal justice and corrections, so we also use a dummy for presidential election years to explain subsequent incarcerations.

Family Breakdowns: Out-of-Wedlock Births and Crime

An opposite explanation for incarceration is based on prior breakdowns in socialization. As Gottfredson and Hirschi (1990, p. 100) note, "There is good reason to expect, and the data confirm, that people lacking self- control do not socialize their children well." We use the percentage of the population born out of wedlock to measure a lack of parental self-control. There are important reasons for thinking that high levels of out-of- wedlock births produce social problems when the children involved reach adolescence. Mothers who must provide support and discipline without help from fathers will face greater difficulties meeting these needs (McLa- nahan and Sandefur 1994). According to Gottfredson and Hirschi, crimi- nality is not something parents must work to produce; it is something they must work to avoid. The mothers of children born out of wedlock are not as likely to have the resources to keep their children away from such haz- ards. Sampson (1987) provides additional evidence that family break- downs lead to serious crimes.

During the period in question the number of out-of-wedlock births grew substantially. A suitably lagged measure of this effect may explain incar- cerations with the crime rates held constant because increased out-of- wedlock births created numerous disruptive problems after the children involved reached adolescence (Murray 1984; McLanahan and Sandefur 1994) and some of these disruptions would not be enumerated in the crime rates. These problems should convey the impression that public order is breaking down. Criminal justice officials may respond by increasing the probability of imprisonment for all convicted offenders. Even convicted offenders who were raised in intact families therefore would be more likely to be incarcerated during times when large numbers of out-of-wedlock children reach the age when they are most likely to participate in disrup- tive activities. All of these considerations suggest that society uses impris- onment as a substitute for a deterioration in the critical social control mechanisms provided by intact families.

Finally, any study of the determinants of the incarceration rate must try to control for the incidence of crime, but crimes known to the police are the only available measure. We assess two interpretations of the effects of these rates. First, in part because they are highly aggregated, the re-

ported rates may be strongly correlated with the actual amount of crime.

The untransformed crime rates may explain subsequent prison admissions

because there are more imprisonable offenses and more convictions during

periods when the crime rates increase.

Alternatively, we know that the crime rates are well publicized. After they reach a critical point, these rates therefore may trigger increased pub- lic fears and heightened demands for punitive measures. Research (Lich- tenstein et al. 1978) shows that the relationship between actual and per- ceived risk is subject to such threshold effects. Despite moderate increases in the crime rates, fear of crime increased substantially during the latter part of the study period (Skogan 1990; Yin 1985). When crime rates are modest, people may disregard the attendant risks, but once a critical level is reached, even small expansions in the reported rates may trigger en- hanced anxieties and escalated demands for punitive responses. The last hypothesis suggests that the square of the crime rates will produce stronger results than the untransformed crime rates because this transfor- mation weights higher crime rates more heavily.

Summary The conventional wisdom and the earlier literature suggest that crime, the presence of young males, unemployment, and out-of-wedlock births should explain imprisonment rates, so we begin our analysis with this orthodox model. We next see if latent political cleavages explain prison admissions by assessing the effects of racial and economic stratification. To see if two direct political effects matter, we add a comprehensive mea- sure of the political strength of the most conservative political party, and we see if election-year rivalries lead to increased imprisonments because incumbents compete for votes by enhancing punitive responses to crime.


The Dependent Variable and the Sample We analyze yearly prison admission rates rather than the number of pris- oners. Particularly after all of the recent court decrees restricting prison crowding, the number of prisoners depends on prison space. A substantial number of prisons were built many years ago, so current space in these facilities was largely determined by the prior tax base and by how much authorities decided to spend on construction in the (often distant) past. The fact that court-imposed limits on crowding become especially signifi- cant during the last part of our series imposes additional methodological burdens. For these reasons, specifying equations designed to predict total inmates therefore would be difficult.

Admissions to prisons can be determined by available space, but a nega-

tive relationship between these two dimensions does not exist, since the

correlation between per capita admissions and the per capita number of

prisoners is strong and positive. This finding and others show that admis-

sions and the number of prisoners grew together in the years covered by

this study. We therefore opt for the more methodologically defensible ap-

proach and use yearly admissions per 100,000 population instead of the

per capita number of prisoners in a given year.3 We combine federal and

state admissions because federal facilities are partial substitutes for state

institutions and because the theoretical issues that prompt this study make

the comprehensive measure more informative. Federal admissions aver-

aged a significant 12.9% of all imprisonments during the study period.

All regressors, except those which measure out-of-wedlock births and the nonwhite-white median income ratio, are lagged by one year because other lags produce weaker results. In most equations imprisonments will be measured from 1950 to 1990, but the explanatory variables will begin at 1949 and end in 1989, which yields 41 cases in the typical analysis. We select this period because data on admissions start in 1948. First differenc- ing removes a case from the beginning of the data, and the correction for autocorrelation sacrifices the first case in the remaining years. The analysis stops at 1990 because the most recent statistics on prison admissions end then. Finally, substitutes for annual statistics at the national level do not exist. These data are available only for the entire country by year. It is equally unfortunate that statistics on black or nonwhite incarcerations do not begin until 1964.

Measurement of Explanatory Variables

To measure the degree of inequality created by the presence of the rich, we follow the general precedent established earlier (Jacobs 1979) and use the variance computed on real incomes calculated from the yearly CPS surveys (the earlier study Wacobs 19791 uses the standard deviation). In-

Chiricos and Delone (1992) claim that studies of admissions rather than the number of total prisoners are less likely to find that unemployment matters. Yet the great majority (if not all) of the equations in these studies of total prisoners were incorrectly specified. We could not find any analyses of prison populations that made comprehen- sive efforts to model the historical determinants of space in these facilities, although the many recent court decisions forbidding crowding mean that space is a critical determinant of total prisoners. Without complicated attempts to include the determi- nants of prison capacity, this work is bound to be misleading. Recent increases in the explanatory power of prison space make modeling total prisoners per capita even more difficult. Garland (1990) claims that prison populations are more likely to be determined by autonomous prison officials, so there are added reasons to believe that external forces will have diminished effects on this outcome.

come distributions are sharply skewed, so measures of dispersion such as

the standard deviation or the variance that are based on the sum of

squared differences from the mean are heavily influenced by the incomes

of the most affluent (Sen 1973).4

We measure the amount of income inequality created by the presence of the poor with the Gini index supplied by the census. Gini is most sensi- tive to income differences between middle-income recipients and the least affluent (Sen 1973), so it is primarily responsive to the gap between the poor and all other^.^ We measure racial threat with nonwhite median fam- ily incomes divided by white median incomes. This variable is lagged by two years because that interval produced the strongest results. Data on median incomes for blacks are not available before 1963. The census states that 90% of the respondents in the nonwhite category are black, so varia- tion in the numerator of this measure is largely driven by fluctuations in black incomes. Because larger scores indicate diminished inequality, coefficients on this ratio should take a negative sign.

We measure political effects with a dummy scored "1" during the terms of all Republican presidents times the mean of the percentage of Republi- can governors, the percentage of Republicans in the House and Senate, and the percentage of respondents who identified themselves as Republi- cans in national Gallup surveys. The last indicator is the most important measure of partisanship in political ~cience.~

Yearly identification is com-

The census does not give means for the highest income category. The Pareto estima- tor often produced nonsensical results, so we estimated the top category means with means computed from IRS statistics on incomes. The IRS uses a different income definition than the census, but this difference is much more important for low incomes. If biases due to these differences are present, they should be roughly constant across years. The IRS gives total dollars and the number of recipients in each category, so category means can be computed by simple divisions. The highest IRS income cate- gory is $1,000,000+ in all years, but the top category in the earliest CPS data is $25,000+. The inequality variable computed using the IRS means for the last open- ended category in the CPS therefore is a much stronger predictor than measures based on estimates of the top category means using CPS data.

The two measures of inequality are closely associated with the presence of either upper or lower income classes, but not both. To see if these measures pick up different gaps in income distributions, we regressed the percentage of income recipients in the bottom and in the top two income categories in the CPS tables on these measures of inequality. Dummies were included to control for every change in category definition. The variance is positively associated with the percentage of families in the top two income categories, but this measure is not associated with the percentage in the two lowest categories. The Gini index is positively related with the percentage of families in the lowest categories, but it does not predict changes in the percentage of high income recipients. In another study Uacobs 1980) state data was used to show that Gini is sensitive to the gap between the poor and middle-income recipients, while the standard deviation is closely related to the percentage of high-income recipients.

The political science literature is filled with claims that party identification is the most important measure of affiliation with a political party and the best determinant

puted with the mean of results of 12 monthly surveys (11 in 1953) per

year, so it avoids the instabilities associated with a single yearly survey.

This combined scale taps both the incumbency of critical Republican

elected officials and their support in the electorate. It measures both na-

tional and state Republican strength. We multiply this scale by a dummy

coded "1" during Republican presidential years to emphasize the powerful

agenda-setting effects that inhere in the presidency (studies of this form

of presidential influence are extensive; see Kernel1 [1986], Tullis [1987],

and Neustadt [I9901 for historical treatments; Ingberman and Yao [I9911

and Mathews [I9891 furnish quantitative support).

To gauge the effects of competition for votes on subsequent imprison- ments, we follow the precedent in the political business-cycle literature and use a separate dummy coded "I" for presidential elections since 1964 because political campaigns emphasizing law and order became so popu- lar after the 1964 election. We assess the effects of unemployment with the total rate. Economic growth is measured in the conventional manner with real per capita GDP, and we measure the presence of likely crime participants with the percentage of the population that is male between 14 and 25 years old (%young males).

The effects of out-of-wedlock births are measured with a five-year mov- ing average of the number of out-of-wedlock births lagged by 19 years and divided by population. We divide by population because the relative number of people born out of wedlock is at issue. Moving averages are used so out-of-wedlock births over a five-year period have equal effects. We use 19-year lags because this theoretically plausible interval did best in the regressions. A five-year moving average combined with a 19-year lag means this indicator measures the percentage of the population born out of wedlock who are between 17 and 21 years old in any given year. This construction makes sense because it is unusual to send convicted adolescents under 17 to adult prison; in addition, 17- to 2 1-year-olds are especially likely to participate in street crimes and other disruptive acts. Finally, we use untransformed FBI crime rates as a potential correlate of the amount of crime. To gauge the threshold effects inherent in per- ceptions of risk, we use the square of this variable in other equations.

of support for that party's candidates. For summaries of the vast research using this measure, see Keith et al. (1992), Miller (1991), or Shively (1980). For studies of shifts in identification over time, see Knoke and Hout (1974) or Haynes and Jacobs (1994). The question used by Gallup to determine partisanship in all years is, "In politics, as of today, do you consider yourself a Republican, a Democrat, or an Independent?" Cronbach's alpha for the additive components of this scale (percentage of Republican governors, house members, senators, and identifiers) is .74. Because the components of this additive scale are uncorrelated with time, the correlations used to compute this reliability coefficient are not inflated by shared trends.

Logging variables weakens the results, so this transformation is not em-


The theoretical discussion suggests that the coefficients on all of the

explanatory variables but one (the nonwhite, white median income ratio)

should take positive signs. One of the more general specifications of the

model therefore is

where d indicates a first-differenced variable, IMPRIS is the yearly num- ber of admissions to prisons per 100,000 population, INEQ is the variance of incomes, ILLEGITMAS is a five-year moving average of the percent- age of people who are born out of wedlock, CRIME2 is the square of the crime rate, REPSTR is the combined measure of the presence of Republi- can elected officials and individuals indentifying as Republicans, and ELCTLT is a dummy for presidential election years after 1964. In addi- tional models we assess the effects of another measure of income inequal- ity (Gini), percentage unemployed, economic growth, the ratio of nonwhite to white median incomes (lagged by two years rather than one), and %young males.



If the variables are left in level form, the estimates are extremely unsta- ble due to substantial intercorrelations between explanatory variables.

'Readers who think we should have controlled for other effects should note the severe problems finding reasonably complete series. In particular, the only data on nonwhite incarcerations begin in 1964. Since no predictors definitionally related to this outcome exist, we cannot estimate missing values (we do estimate some state admissions for drug offenses with federal admissions; see n. 15 below). Other measures of family breakdowns, such as the proportion of older children raised in single-parent house- holds, are unavailable. Data on prison admissions before 1971 come from Historical Statistics of the United States. Admissions from 1971 to 1988 come from The Statisti- cal Abstract, while the Bureau of Justice Statistics Bulletin: Prisoners in 1992 gives 1989 and 1990 admissions. Total crime, violent crime, and murder rates before 1960 come from Social Indicators, 1973 published by the Office of Management and the Budget. After 1959 we used The Sourcebook of Criminal Justice Statistics, 1992. These sources follow those used by Cantor and Land (1985), although we use more recent statistics if they are available. Data on unemployment and GDP come from the Economic Report of the President. The variance of incomes is computed with CPS Series P60 data and the IRS income statistics; Gini comes from Series P60 as well.


Levels First Differences

Intercept ...........................................................................-4.6758
Imprisonment rate ......................................................... ,1223
(2 .03)a
d(imprisonment rate) ................................................... -.2960

R2(corrected) ............................................................. .051

"elevant t-statistic. For these, MacKinnon critical values for rejection of a unit root hypothesis are t of -2.94 5 .05 level; t of -3.60 5 .O1 level. Nos. in parentheses are t-values. dd indicates a second-differenced variable, or a variable constructed by subtracting first differ- ences.

* P > .05.

** P > .01.

Shared trends are present in most of the variables if they are not differ- enced, but the use of a time-trend variable on the right side of the equa- tions to remove spurious relationships caused by trending may produce misleading significance tests. A formal test illustrates this problem and shows that our remedy is appropriate. According to the new literature in time-series econometrics, if a Dickey-Fuller (1981) unit root test indicates that the slope of a variable regressed on itself at t -1 equals unity, then using variables in level form and controlling for spurious associations by entering a time-trend may result in type I errors (Green 1993; Gujarati 1995; see Raffalovich [I9941 for a discussion in sociology). The unit root test for a regression coefficient of unity transforms equation (2) to equation (3)and tests whether the regression coefficient in equation (3) is zero using critical t-values supplied by MacKinnon (1991).

Y,-Yt-I= by,-,+ u,. (3)

As Green (1993, p. 565) notes, the augmented Dickey-Fuller test pre- sented in table 1 is preferable. The test presented in column 2 of table 1 is a simple extension of the test in column 1. The results show that first differencing will be necessary. Additional (unreported) Dickey-Fuller tests show that unit roots are present in most of the continuous explanatory variables if they are not differenced. We therefore follow the recom

mended procedure (Green 1993, pp. 558-68; Nerlove and Diebold 1990)

and first-difference all variables in the regression models that fol10w.~ As

long as both the dependent variable and all regressors are first differenced,

a significant coefficient on an explanatory variable has the same interpre-

tation as it would if the data were in level form, and this generality holds

for dummy variables that should be differenced as well.

As the discussion in note 8 below implies, unit root tests and differenc- ing are not panaceas. Estimates produced by differencing are conservative because differencing completely eliminates shared trends in variables, but differencing removes information about levels and long-run relationships. Results based on differenced series are far less likely to be spurious be- cause joint time-related movements in variables are eliminated. Yet as Gujarati (1995) notes, differencing to produce stationarity is a severe rem- edy that only should be used when other corrective steps fail (as they have in this case). In direct contrast to (unreported) analyses conducted in lev- els, the regressions show that differencing provides coefficients that are robust when specifications are altered, but this does not mean that such a drastic procedure must be automatically employed in all time-series analyses.

Analysis: Regression Results in Table 3

Table 2 gives the correlations together with the means and standard devi- ations. Despite the degree of aggregation, because all variables have been first differenced, the intercorrelations between explanatory variables are modest (the largest correlation between any two explanatory variables in the same equation is .362).' This undoubtedly helps account for the stabil- ity of the estimates compared to the coefficients computed on variables in level form. Table 3 shows the first four regression equations (to correct

Dickey-Fuller tests are not without criticism in econometrics. One issue concerns the statistical power of the test. As Green (1993, p. 563) and Maddala (1992, pp. 582-88) note, if the actual root in a series is .95 or even .99 rather than unity, the issue becomes moot and estimation in levels will be more appropriate, but the available unit root tests cannot make such fine distinctions. In the absence of a consensus, sociologists should not indiscriminately use these tests to justify conclusions that almost all time- series work must use differenced series. In this analysis, however, estimates based on levels are unstable, but first differencing corrects these problems. It removes problems with multicollinearity as well, so we have ample reasons to use this specification.

The two inequality indicators are sensitive to different gaps in the income distribu- tion, and these variables have been differenced, so they should be weakly correlated. Jasso (1979) argues that modest associations between the variance and Gini should not be surprising for other reasons. Van der Vaart (1968, pp. 293-95) shows that "Gini's mean difference and the variance are distribution specific functions of one another. That is, there is no general relation between them. . . . Only within a distribu- tional family are all measures of inequality monotonic functions of each other" (as quoted in Jasso 1979, p. 870).




Intercept .....................................

%young males, 14-25,-, ...........

Crime rate,-, ............................

Crime rate2,-, ..........................

Variance of incomes,-," ............

R2(corrected) .............................

p ..................................................
D-W ......................................

NOTE.-N = 41; t-values are in parentheses. "cores for the variance of incomes have been divided by 10,000,000; scores for crime2 have been divided by 100,000.

* P 5 .05 (one-tailed test).
** P 5 .01.

for autocorrelation, all equations but one are estimated with the Mar- quardt AR1 procedure in Micro TSP; see Hall, Lilien, and Johnson [I9941 for a description).

We begin the analysis with the most orthodox model. We then add measures of latent political cleavages in the last equations in table 3 and the first equations in table 4; finally, in the last two equations of table 5, we add two direct measures of political effects. The first equation in table 3 presents the findings based on the most conventional set of explanatory variables using out-of-wedlock births, %young males, unemployment, and the untransformed crime rates. Equation (2) shows what happens if the crime rates are squared. Because these and the other results show that crime rates in squared form are a superior control and because there are good theoretical reasons for this transformation, all subsequent equations will be estimated using the square of the crime rates (additional implica- tions are discussed below). In equations (3) and (4) in table 3 we begin to


(1) (2) (3) (4)"
Intercept ................................. -1.4464 -1.3752 -2.8589* -2.6784*
  (-1.11) (-0.99) (-2.32) (-2.00)
Out-of-wedlock births,-lp ......... 88.3903** 85.2906** 103.6861** 99.5728*
  (2.73) (2.54) (3.09) (2.75)
Crime rate2,-, ............................ .5618* .6501* .5966* .6018*
  (1.90) (1.99) (2.06) (1.99)
Variance of incomes+," ............ .1996** .1996** .1437* .1466**
  (3.14) (3.08) (2.38) (2.55)
Economic growth,-, .................. -.0369 -,035 1 ... ...
  (-1.65) (-1.49)    
Nonwhite-white median in- ... -35.7976 ... ...
come,-, ........................... ......        
Republican strength,-, .............. ... ... .1130* .1079*
      (2.35) (2.25)
Dummy for presidential elec- ... ... 2.9976* 3.1534*

tion year,-, .............................

(2.11) (2.38)
R2 (corrected) ......................... .396** .389** .462** .463**
p ................................................ -.248 -.233 -.I34 -.085
D-W ......................................... 1.973 1.944 2.036 2.176
N ............................................ 41 40 41 42

NOTE.-t-values are in parentheses. " Eq. (4) is estimated with OLS, but all other equations are corrected for autocorrelation. Scores for the variance of incomes have been divided by 10,000,000; scores for crime2 have been divided by 100,000.

* P 5 .05 (one-tailed test).
** P 5 .01.

enter measures of economic cleavages, but we avoid redundant indicators by substituting these variables for one another, although the appendix shows that using Gini and the variance together does not alter the conclusions.

Many of the conventional explanatory variables that have been empha- sized in the time-series literature on crime and imprisonments are poor predictors. Shifts in unemployment never explain subsequent changes in prison admissions, and this outcome persists if we measure unemployment in a variety of ways.'' The presence of young males often explains crime

lo To adjust for the secular growth in unemployment since the 1940s, economists have computed the natural unemployment rate or the point where further reductions in unemployment would lead to enhanced inflation (see Gordon [I9931 for an enumeration and discussion). When he analyzes the political effects of unemployment, Hibbs

rates (Land, Cantor, and Russell 1995), but changes in the percentage of

young males in the population evidently are not associated with subse-

quent movements in prison admissions.

A Gini index computed on incomes does not predict changes in the incarceration rates in the next year, but the variance of incomes provides a strong explanation for these shifts. The contrast in the performances of these alternative inequality measures suggests that different measures of inequality should not be thoughtlessly substituted for one another as has so often been done in the past. Finally, and perhaps surprisingly in light of its prior neglect, the presence of adolescents and young adults born out of wedlock is significant (all t-tests are one-tailed) in all four equations, and the values of the coefficients on this regressor seem to change only when another strong explanatory variable (the variance) is added in the last equation. Most of the conventional explanations therefore do not ex- plain incarcerations, but out-of-wedlock births and one measure of eco- nomic cleavages are associated with subsequent movements in the prison admission rates.

The results in table 3 therefore suggest that three factors explain shifts in incarcerations. First, when the crime rates are transformed to reflect threshold effects, they become significant, although these rates are not effective if they are left unaltered. Second, the percentage of 17- to 21- year-olds born out of wedlock provides a robust explanation for imprison- ments in the next year. Finally, the results suggest that a positive relation- ship between changes in the variance of incomes and subsequent shifts in the admission rates is present, but this association needs to be subjected to additional tests. We should see if these findings hold when measures of racial inequality and economic growth are held constant, and we need to test political explanations.

Additional Analyses

Table 4 provides additional information about the determinants of impris- onment rates. In equations (1) and (2) we retain the three variables that were significant in the regressions reported in table 3, but we add per capita real GDP to see if a potentially spurious association between eco- nomic growth, the variance of incomes, and incarceration rates is present. In equation (2) we continue to enter cleavage measures by adding the ratio of nonwhite to white median incomes. In equations (3) and (4) we again

(1987) removes this upward trend by subtracting the increasing natural rate from the total unemployment rate, but this corrected measure does not explain incarceration rates. The percentage of unemployed males over 19 years of age, mean weeks unem- ployed times the total unemployment rate, or the ratio of blacklwhite unemployment rates have the same negligible effects.

remove measures that were insignificant in our prior analyses and enter

the two political measures. Finally, in these two equations we also see

how robust the final results are by comparing OLS and GLS estimators

computed on what evidently is the best model.

Equations (1) and (2) show that the standard measure of economic growth does not explain incarcerations. Real per capita GDP is insignifi- cant, and its sign is not even in the expected direction. The inclusion of this variable does not alter the significant coefficients on the variance of incomes, and this result holds if similar measures like real median family incomes or real mean family incomes are used in place of real per capita GDP. Differences in the incomes of nonwhites and whites appear to be unrelated to subsequent shifts in the imprisonment rates as well. This finding persists when this variable is used in other models (see the ap- pendix).

In equations (3) and (4) of table 4 we add the two political indicators and find that the coefficients on both are significant. The coefficients on the election variable indicate that, since 1968, administrations enacted policies that expanded imprisonments in the year following a national election. The nonpartisan nature of this election effect is corroborated when a different dummy is substituted for the election year dummy. If a variable coded "1" for all presidential election years when a Republican administration was in office is used in place of the dummy coded "1" for all presidential election years after 1964, the substitute measure is insig- nificant (additional measures of period effects are ineffective as well). The results also show that incarcerations are likely to increase after expansions in the political strength of the Republican Party, and both political find- ings hold no matter how the equations are plausibly specified (see the appendix).

In equation (4) we report OLS results to see what happens when we use identical specifications with a different estimation routine. There are slight differences in the magnitudes of the coefficients and only one trivial difference when the significance tests in the last two equations are com- pared (cf. the t-values for the variance). When OLS is used to estimate the final model, the Durbin-Watson test indicates only a modest amount of autocorrelation.

If we look at effects across the equations, the three variables that are statistically significant in table 3 remain significant in table 4. No matter how the specifications are altered, shifts in out-of-wedlock births, the vari- ance of incomes, and the crime rates explain subsequent changes in the incarceration rates (see the appendix as well). The political variables intro- duced in equations (3) and (4) of table 4 also explain subsequent changes in prison admissions. National campaigns for office evidently produce in- creased incarcerations after law and order appeals began to appear in

presidential campaigns. Finally, as one might expect from Republican

rhetoric and the public policies enacted by the party, changes in a compre-

hensive measure of the political strength of the most conservative political

party produce shifts in prison admissions.

Five factors therefore are associated with subsequent shifts in the incar- ceration rates. Movements in the crime rates explain changes in prison admission rates after this variable is transformed to make it responsive to threshold effects. Economic inequality also predicts movements in the incarceration rates after a year's delay, but a measure of this concept that is sensitive to the presence of the poor is ineffective. The percentage of late adolescents and young adults who were born out of wedlock is an- other regressor with robust effects. Two political variables clearly matter as well. A comprehensive indicator of the political strength of the Republi- can Party has positive effects on subsequent shifts in prison admissions, and presidential campaigns after 1964 lead to increased incarcerations in the following year.

Other plausible hypotheses are not supported. We found no evidence that unemployment explains shifts in imprisonments. We suspect this variable was significant in many prior studies because the investigators did not first difference. Severe collinearity is present when longitudinal analyses of imprisonment rates are conducted using variables in level form. We find that unemployment has less extreme intercorrelations than the other explanatory variables in equivalent models computed on levels. For this reason, the coefficients on unemployment sometimes are signifi- cant particularly when important explanatory variables are omitted, but these results are not robust.

Although the shifts in the presence of young males explain changes in crime, this measure is unrelated to shifts in prison admissions-probably because the percentage of young males reaches its maximum in 1968 when prison admission rates fell to their lowest levels. As prison admission rates subsequently expanded, the percentage of young males in the population slowly ebbed. Nonwhite-white income differences, the measure of in- equality most sensitive to the gap between middle-income recipients and the poor (Gini), and economic growth also do not explain subsequent shifts in the incarceration rates. It follows that one latent cleavage indicator (the variance of incomes) and two political variables explain subsequent shifts in prison admissions. With the possible exception of out-of-wedlock births, however, the conventional indicators that received the most attention in earlier work do not explain incarcerations in this study.

These results are robust. First, the addition of a case because equation

(4) of table 4 is estimated with OLS or the removal of a case because the nonwhite-white income variable does better with a two-year lag (see eq.

FIG.2-Graph of the fitted (or predicted) versus the actual values of the depen- dent variable and the residuals plotted on time.

[2], table 4) has negligible effects." Second, the same explanatory variables explain prison admission rates no matter how the reported equations are specified. In the appendix, for example, we add each insignificant explana- tory variable in tables 3 and 4 to the final model. The insignificant vari- ables in tables 3 and 4 remain insignificant, but the five significant inde- pendent variables continue to explain shifts in prison admissions and the values of their coefficients remain similar when different independent variables are entered.

The top half of figure 2 shows the predicted and actual values of the first-differenced dependent variable plotted on time, while the bottom part of figure 2 shows the residuals graphed on time using the coefficients from the final model (eq. [3], table 4) to produce both plots. The upper part of this graph shows that first differencing has removed the severe trending in the dependent variable that is so apparent in figure 1. Figure 2 also shows that the distribution of the residuals does not suggest the presence of systematic errors or omitted variables. The modest p values,

" Alternative explanations that require reverse causation from the dependent variable to the explanatory variables cannot explain these results. Causation cannot go back- ward in time, and all of the explanatory variables have been lagged. While we do not include a lagged dependent variable on the right side of the equations (if this is done, the results do not change), we eliminate autocorrelation. Deterrence effects or the idea that increased imprisonment rates reduce the amount of crime are unlikely to bias these estimates.

Durbin-Watson scores near the ideal, and the similar results when the final model is estimated with either OLS or GLS enhance the credibility of these estimates.

Additional Tests

Given an apparent nonlinear expansion in the imprisonment rates after 1967 (shown in fig. 1) and the success of the variance of incomes and the squared transformation of the crime rates, it is reasonable to wonder about the effects of quadratic specifications. When the standard deviation and the variance of incomes and the untransformed and squared crime rates are included in otherwise identical seven-variable models, the squared crime rates are significant, but the untransformed crime rates again are not. The coefficients on the inequality measures suggest that, after in- equality reaches a threshold, the likelihood of incarceration increases. Some statistical purists question the use of quadratic models when the number of cases is restricted. Quadratic specifications cost additional de- grees of freedom, and the squared and untransformed terms are highly correlated. We therefore adopt the most conservative strategy and avoid this specification, but the theoretical implications do not change if it is used.''

Tests for heteroscedasticity using White's (1980) method indicate that this problem is not present. As one would expect from figure 2, Chow and other tests show that the coefficients are equivalent within various subperiods. To see if changes in the severity of crimes account for shifts in incarceration rates, we use violent crime rates or murder rates in place of the total crime rate in unreported equations. The findings persist, so we probably can eliminate this compositional argument. If we include the percentage of the population fighting in foreign wars to see if the removal of so many young males alters the results, we find no evidence for this effect.

Other issues concern measurement. Some inequality indicators such as Gini are insensitive to units. This property is called scale invariance, but

'' Stockard and Johnson (1991) claim that married men are less likely to engage in crime, so we include the percentage of single adult males in some equations to see if incarcerations increase after these informal controls diminish. When immigration rates expand, authorities may feel that enhanced punishments are necessary to control potentially dissident newcomers, but neither factor explains prison admission rates. We also included the percentage of nonwhites in our equations to see if this effect matters. In level form this variable ranges from 10.45% to 15.94% with a mean of 12.67%, but its variation relative to its mean is much greater after it is first differenced (the coefficient of variation for this variable equals a reasonable ,5275 after differenc- ing; it is ,1272 in level form). This measure of minority effects is insignificant as well if it is added to the final five variable model (eq. [3], table 4).

the variance is not scale invariant because it measures absolute differ-

ences. Because many scholars question scale invariance as a criterion for

measures of inequality (Dalton 1920; Kolm 1976a, 19766; Schwartz and

Winship 1980), there is no reason to restrict analyses to such measures

(Jasso 1979).13 In this study the variance is computed on real incomes, so

currency units are identical. Real incomes and real differences in incomes

increase with economic growth, however, so relationships between the

variance of incomes and prison admissions could be a spurious function of

growth. Yet the use of a standard control for growth leaves the significant

coefficient on the variance irrtact (see eqq. [I] and [2] in table 4). In unre-

ported equations we use real mean family incomes or median family in-

comes also in constant dollars, but these equivalent measures do not alter

the results.

Readers may wonder if the Republican strength measure should include just those periods after Republicans explicitly invoked law and order cam- paign appeals, but removing the Eisenhower years from this measure would be a mistake. Eisenhower and other Republicans in this period devoted much effort to strengthening criminal sanctions. Eisenhower re- peatedly advocated increased federal expenditures for state and local law enforcement (New York Times Index 1956). These themes were echoed by other administration officials. Republicans in Congress introduced much legislation that increased the penalties for criminal acts during these years (see the Congressional Quarterly Almanac, 1954-5 7). Caldeira (1983) used separate dummies for different administrations and found that, in contrast to the Truman or the Kennedy administrations, presidential requests for expenditures on corrections and prosecution rose substantially in the Eisenhower period. The years when Eisenhower was president therefore should be retained in the measure of Republican strength.

Finally, readers who question the number of explanatory variables in these analyses should remember that greater accuracy can be expected if many explanatory variables are included in regression models. Johnston (1984) states that exhaustive specifications are most likely to furnish con-

l3 J~SSO'S are worth repeating. After suggesting that the variance is a useful

c~nclu~ion~ measure, she says (1979, p. 870), "It is important to become familiar with the properties of many measures of inequality, to learn of their particularities and idiosyncrasies. . . . For the task of the social scientist is not so much to choose [from] among them one to use in every case. Rather the task is to fit the choice of inequality measure to the problem under study. The task is to find for each social dependent variable the particular manifestation of inequality that is most highly related to it." In this case the variance is the empirically superior measure. It is the indicator of dispersion that best predicts movements in prison admission rates because it combines exhaustive coverage (the variance is computed on all incomes in a distribution) with a pronounced sensitivity to the gap between the incomes of the rich and all others.

sistent estimates,14 while Blalock (1979) recommends that sociologists drastically increase the number of regressors in their equations. The ratio of explanatory variables to cases in many econometric studies is far greater than it is in this analysis, so there is ample precedent for the number of independent variables in these regressions.


Evidence for Alternative Explanations for Prison Admission Rates

Several conventional hypotheses stressed in the literature on crime and imprisonments are not supported. In one major departure from existing work, we find that unemployment is not related to prison admission rates when more thorough tests than those used in earlier studies are conducted. This negative result is noteworthy because so many inconsistent findings about this relationship have been reported. Second, while changes in the presence of young males often explain shifts in the crime rates, this indica- tor is unrelated to changes in prison admission rates.

Third, as expected, the crime rates predict prison admissions, but this relationship is present only if the square of this variable is used to test for threshold effects. Such results and the recent heightened anxieties about crime-although recent expansions in these rates have not been dra- matic-suggest that, when reported crimes are modest, people may not be unduly disturbed by significant increases in these rates. Yet after these well-publicized rates reach a critical point, even small surges in the crime rates probably lead to rapidly escalating fears and strident demands for harsh punishments because the perception of risk is subject to threshold effects.15

l4 Johnston's exact remarks on this issue are instructive. He says, "It is more serious to omit relevant variables than to include irrelevant variables since in the former case the coefficients will be biased, the disturbance variance overestimated, and conven- tional inference procedures rendered invalid, while in the latter case the coefficients will be unbiased, the disturbance variance properly estimated, and the inference pro- cedures properly estimated. This constitutes a fairly strong case for including rather than excluding relevant variables in equations. There is, however, a qualification. Adding extra variables, be they relevant or irrelevant, will lower the precision of estimation of the relevant coefficients" (1984, p. 262), so inclusive specifications will typically lead to more conservative significance tests.

l5 The crime rates do not include drug offenses, so we estimate the total number of drug incarcerations. Data on state imprisonments for drug offenses are available for 16 years. This information is intermittently present between 1960 and 1978 with full enumeration thereafter, but federal imprisonments for drug offenses are continuously available. We estimate missing state drug incarcerations with coefficients produced by a regression of the 16 available state drug admissions on yearly federal drug admis- sions plus real GDP per capita, a time trend, and its square. This regression gives a corrected RZof ,941. We substitute the predicted values when data on state drug offense incarcerations are missing. When drug imprisonments are removed by using

The results also corroborate accounts that stress family breakdowns

due to out-of-wedlock births. We measure this effect by lagging a five-

year moving average of the proportion of people who are born outside

marriage by 19 years. The results show this indicator to be a robust pre-

dictor of imprisonment rates because the 19-year lag adjusts this five-year

moving average so the children in question can reach 17-2 1 years or the

ages when they are most likely to participate in street crime and end up

in adult prisons.

One indicator of latent political cleavages explains incarcerations as well. The findings show that shifts in economic inequality produce subse- quent movements in the incarceration rates, but the effects of measures of inequality that are especially sensitive to differences between poor and middle-income recipients are negligible. This finding and the insig- nificant effects of the racial economic cleavage measure do not support hypotheses that authorities react to an expanded underclass by increasing prison admissions. Yet income inequality produced by the gap between the rich and other income recipients consistently explains subsequent movements in the imprisonment rates. Although we do not have informa- tion about the intervening processes that lead to these outcomes and there- fore should not speculate about these links, the results are consistent with neo-Marxist and other radical theories that emphasize the political po- tency of the affluent as an important cause of shifts in the imprisonment rates.

Political effects neglected in the empirical literature also seem to matter. The performance of the combined indicator of Republican strength sug- gests that increases in the political resources of the more conservative party lead to increased incarcerations. The results showing that presiden- tial election years after 1964 result in increased prison admissions in the following year imply that the competitive nature of elections induces in- cumbents to enact policies that lead to increased incarcerations. The suc- cess of the political variables also suggests that national politics have inde- pendent effects on movements in the prison admission rate. A design that uses national-level data therefore seems appropriate (see Savelsberg [I9941

this combined measure of drug incarcerations as an explanatory variable, the five explanatory variables in the last two equations in table 4 are significant predictors of these "purified" prison admissions. When we conduct a separate analysis of total drug incarcerations, the crime rates no longer are significant, but the other four explanatory variables continue to explain this outcome with expected signs (t-values must be cor- rected for heteroscedasticity if the dependent variable is estimated [Saxonhouse 19761; we use White's [I9801 correction). Almost all of the estimates appear before 1968 when prison admissions were relatively stable (see fig. I), so these analyses using the combined estimated and actual values should give accurate results.

and Chambliss [I9941 for supporting arguments about the importance of

national politics).16

The modest intercorrelations between explanatory variables, together with the extensive statistical controls and the first-difference specifications that remove the effects of shared trends make it difficult to believe the relationships found in this study are spurious. The robust results when we use different specifications furnish additional reasons for suspecting that the effects we have isolated represent some of the primary underlying political, economic, and social processes that determine changes in puni- tive practices in at least one important developed democracy.


The results support one hypothesis that perhaps can be classified as ortho- dox. The evidence fits with accounts that stress family breakdowns. We find that out-of-wedlock births consistently explain imprisonment rates after these children reach 17-21 years of age. The resulting derelictions in child rearing and the reduced resources that go to children born out of wedlock (McLanahan and Sandefur 1994) evidently lead to increased incarcerations after the children in question reach the time in their life when they are most likely to participate in street crime and other disrup- tive acts that threaten public order. Such findings suggest that society uses prisons to correct for a deterioration in the informal but far more effective social control mechanisms provided by intact families.

A latent political cleavage also affects imprisonment. Garland (1990, p. 92) approvingly quotes Rusche (1933) who writes that "the history of the penal system is . . . the history of relations (between) the rich and the poor." If this assertion is correct, it is reasonable to expect that fluctua- tions in economic differences between the rich and the poor ought to be related to subsequent shifts in the prison admission rates. In this case we find that economic gaps between the rich and all other income groups

l6 The Clinton administration's recent crime initiatives may produce increases in the incarceration rates, but the data to test this effect are not available. The data we have confirm hypotheses that the tenure of presidents from the Republican Party has positive effects on the incarceration rates. Entering a dummy scored "I" for all years after 1967 supports this interpretation. Probably because this dummy includes the Carter years, it does not predict incarcerations. Yet a dummy scored "1" only for Republican presidents is significantly related to the imprisonment rates although its t-value is not as strong as the t-value for the combined Republican strength index. The behavior of the new Republican majority in Congress suggests that a Republi- can president would be even more likely than Clinton to support severe measures. In any case, until hypotheses about the effects of the Clinton administration's crime policies can be tested with multivariate procedures, we will not know if they are correct.

consistently explain these shifts. Our results therefore support neo-Marxist

and Weberian arguments that heightened economic cleavages create la-

tent political conflicts that lead authorities to react in a more punitive


The findings also support arguments by Garland (1990), Savelsberg

(1994), and others who see incarceration as intrinsically political. Com-

bined shifts in the percentage of people who identify with the most conser-

vative political party and the incumbency of elected officials from this

party explain shifts in the incarceration rate. These political effects are

not limited to the Republican Party. The results suggest that during all

presidential election years since 1964, the incumbent administration, re-

gardless of party, was likely to enact policies that led to increased incarcer-

ations in the next year. These findings corroborate suspicions that state

managers in both parties use criminal justice policies for their own paro-

chial ends.

Such results are consistent with hypotheses about the effects of politics on macroeconomic outcomes in political science and economics. Two views prevail. Political business-cycle theories hold that incumbent ad- ministrations deliberately expand the economy in the period immediately before an election to enhance their electoral support. Evidence shows that votes for national officeholders are increased by economic growth during a campaign. Voters probably overlook the costs of these manipulations because the inflationary consequences are delayed until well after the elec- tion (see Schneider and Frey [I9881 or Nordhaus [I9891 for reviews; for robust statistical evidence, see Haynes and Stone [1989]). We find evidence for an equivalently politically driven imprisonment cycle. During cam- paigns, incumbent administrations from both parties evidently compete for votes by enacting measures that lead to greater incarcerations in the year after presidential elections.

The alternative political explanation for macroeconomic outcomes stresses partisan differences. Republican administrations curb inflation at the expense of greater unemployment because their affluent but less nu- merous supporters realize the greatest financial gains from this policy mix. Democratic administrations opt for the opposite macroeconomic trade- off and reduce unemployment even though these policies often increase inflation. They choose this path because their more abundant but less affluent supporters do best during periods of low unemployment and tight labor markets (for extensive evidence, see Hibbs [I9871 or Alesina and Sachs [1988]). Net of election effects we find evidence that Republican incumbents widen their narrow economic appeal by instituting more pu- nitive responses to crime than Democrats. The results of this study there- fore support both the partisan and electoral cycle explanations for shifts in imprisonment.

Wider Implications

Research designs that use aggregate data to investigate explanations for

outcomes in the criminal justice system have important advantages. Such

designs link fundamental theories about the nature of society to important

outcomes in the criminal justice system. With such methods we can use

explanations from core subdisciplines such as stratification and political soci-

ology to explain critical issues in the study of social control. Before the crimi-

nological research stimulated by theories from these subdisciplines appeared,

criminology was in danger of becoming a theoretically isolated endeavor.

Perhaps the primary distinguishing characteristic of sociology is an em- phasis on structural arrangements. Since valid inferences about the be- havior of individuals or their beliefs are difficult to obtain with aggregate data, studies based on these data typically concentrate on social organiza- tion. Research on social control with aggregate data therefore begins to get at questions at the heart of the discipline. The empirical studies of criminal justice outcomes reviewed in the beginning of this paper do not tell us precisely what the structural basis of social order is in advanced societies or exactly when it will change. The generalities that are starting to emerge from this research nevertheless give us far more leverage when we try to answer the big questions about social order that so intrigued the classical theorists.

Of course, there may be limits on the generality of these results. In com- parison to the European democracies, the United States has an excep- tional political system with comparatively frail parties, candidates deter- mined by primary elections, direct voting for national offices, and a relatively weak bureaucracy. These conditions probably give U.S. voters greater influence over decisions that are largely made by experts in Europe. For these reasons, it may be that the political factors that explain shifts in prison admissions so well in the United States do not have such strong effects on prison admissions in the more bureaucratic European states.

This study, however, has isolated historical associations that lead to theo- retically instructive generalities about the determinants of imprisonment rates in one important industrial democracy. Imprisonments evidently shift in response to prior fluctuations in economic inequality, so the results sup- port those theorists who claim that incarceration is one method the modern state uses to manage the latent political conflicts created by economic cleav- ages. Our finding that conservative shifts in political climate are likely to produce punitive reactions to crime provides additional corroboration for this political perspective, but the results also suggest that incumbents from both political parties compete for votes by enacting policies that expand prison admissions in the year after a national election.

Accounts not based on hypotheses derived from political economy ex- plain imprisonments as well. The results show that socialization failures

that stem from out-of-wedlock births and the reduced resources that go to such children lead to subsequent increases in prison admissions. More generally, the findings suggest that additional time-series research that makes a concerted effort to assess diverse political, economic, and demo- graphic explanations should give us a better understanding of the histori- cal forces that combine to shape the social control apparatus of contempo- rary states. These results also suggest that further attempts to use political concepts to explain how formal social control systems operate may be theoretically productive.


Additional Regression Analysis


Intercept ................................

Out-of-wedlock births,-,, .............................

Crime ratei,+, ........................

Variance of incomesa,-, ........

Republican strength,-, .........

Dummy for presidential election year,+, ..................

% males, 14-25,-, .............

Economic growth,-, ........

Nonwhite-white median


R2(corrected) ........................
p ...............................................
D-W ....................................

NOTE.-t-values are in parentheses. See notes to tables 3 and 4

* P 5 .05 (one-tailed test).
** P5 .01.


Alesina, Alberto, and Jeffrey Sachs. 1988. "Political Parties and the Business Cycle in the United States." Journal of Money, Credit, and Banking 20:63-82. Beckett, Katherine. 1994. "Setting the Public Agenda: 'Street Crime' and Drug Use in American Politics." Social Problems 41:425-47.

Berk, Richard A., D. Rauma, S. L. Messinger, and T. F. Cooley. 1981. "A Test of the Stability of Punishment Hypothesis: The Case of California." American Sociological Review 462305-29.

Berk, Richard A,, S. L. Messinger, D. Rauma, and J. E. Berecochea. 1983. "Prisons as Self-Regulating Systems: A Comparison of Historical Patterns in California for Male and Female Offenders." Law and Society Review 17547-86.

Black, Donald. 1976. The Behavior of Law. New York: Academic Press. Blalock, Hubert. 1967. Towards a Theory of Minority Group Relations. New York: Capricorn Books. . 1979. "Measurement and Conceptualization Problems: The Major Obstacle to Integrating Theory and Research." American Sociological Review 44:881-94.

Blank, Rebecca, and Alan Blinder. 1986. "Macroeconomics, Income Distribution, and Poverty." Pp. 180-208 in Fighting Poverty, edited by Sheldon Danzinger and Daniel Weinberg. Cambridge, Mass.: Harvard University Press.

Blau, Peter. 1964. Exchange and Power in Social Life. New York: Wiley.

Blumstein, Alfred. 1993. ''Rationality and Relevance." Criminology 3 1:l-16.

Blumstein, A,, and J. Cohen. 1973. "A Theory of the Stability of Punishment Hypothe- sis." Journal of Criminal Law and Criminology 64:198-207. Blumstein, A,,J. Cohen, and D. Nagin. 1976. "The Dynamics of a Homeostatic Pun- ishment Process." Journal of Criminal Law and Criminology 67:317-34.

Caldeira, Greg A. 1983. "Elections and the Politics of Crime: Budgetary Choices and Priorities in America." In The Political Science of Criminal Justice, edited by Stuart Nagel, Erika Fairchild, and Anthony Champaign. Springfield Ill.: Charles C. Thomas.

Caldeira, Greg A,, and Andrew T. Cowart. 1980. "Budgets, Institutions, and Change: Criminal Justice Policy in America." American Journal of Political Science 24:413


Cantor, David, and Kenneth C. Land. 1985. "Employment and Crime Rates in the Post-World War I1 United States: A Theoretical and Empirical Analysis." American Sociological Review 50:317-32.

Chambliss, William J. 1994. "Policing the Ghetto Underclass: The Politics of Law and Law Enforcement." Social Problems 41:177-94. Chambliss, William J.,and R. Seidman. 1980. Law, Order, and Power, 2d ed. Reading, Mass.: Addison-Wesley.

Chiricos, Theodore G., and Miriam Delone. 1992. "Labor Surplus and Punishment: A Review and Assessment of Theory and Evidence." Social Problems 39:42 1-46. Cohen, Stanley. 1985. Visions of Social Control: Crime, Punishment, and Classifica- tion. New York: Basil Blackwell.

Collins, Randall. 1975. Conflict Sociology. New York: Academic Press.

Congressional Quarterly Almanac. 1954-59. Vols. 10-15. Washington, D.C.: Govern- ment Printing Office. Dalton, H. 1920. "The Measurement of the Inequality of Incomes." Economic Journal 30:349-61. Dickey, D., and W. Fuller. 1981. "Likelihood Ratio Tests for Autoregressive Time

Series with a Unit Root." Econometrica 49:1057-72.

Dionne, E. J. 1991. Why Americans Hate Politics. New York: Touchstone.

Evans, Peter B., Dietrich Rueschemeyer, and Theda Skocpol, eds. 1985. Bringing the

State Back In. New York: Cambridge University Press.

Garland, David. 1990. Punishment and Modern Society: A Study in Social Theory. Chicago: University of Chicago Press.

. 1991. "Sociological Perspectives on Punishment." Pp. 115-66 in Crime and Criminal Justice: A Review of Research, edited by Michael Tonry. Chicago: Univer- sity of Chicago Press.

Gordon, Robert. 1993. Macroeconomics. New York: Harper Collins.
Gottfredson, Michael A,, and Travis Hirschi. 1990. A General Theory of Crime. Stan-

ford, Calif.: Stanford University Press. Green, William H. 1993. Econometric Analysis. New York: Macmillan. Gujariti, Damodar N. 1995. Basic Econometrics, 3d ed. New York: McGraw-Hill. Hall, Robert E., David M. Lilien, and Jack Johnson. 1994. Econometric Views User's

Guide. Irvine, Calif.: Quantitative Micro Software.

Haynes, Stephen E., and David Jacobs. 1994. "Macroeconomics, Economic Stratifica- tion, and Partisanship: A Longitudinal Analysis of Contingent Shifts in Political Identification." American Journal of Sociology 100:70-103.

Haynes, Stephen E., and Joe Stone. 1989. "An Integrated Test for Electoral Cycles in the U.S. Economy." Review of Economics and Statistics 71:426-34. Hibbs, Douglas. 1987. The American Political Economy. Cambridge, Mass.: Harvard University Press. Ingberman, Daniel, and Dennis Yao. 1991. "Circumventing Formal Structure through Commitment: Presidential Influence and Agenda Control." Public Choice 70:151

79. Jackson, Pamela Irving. 1989. Minority Group Threat, Crime, and Policing: Social Context and Social Control. New York: Praeger.

Jackson, Pamela Irving, and Leo Carroll. 1981. "Race and the War on Crime: The Sociopolitical Determinants of Municipal Police Expenditures." American Sociolog- ical Review 46:290-305.

Jacobs, David. 1978. "Inequality and the Legal Order: An Ecological Test of the Con- flict Model." Social Problems 25:515-25. . 1979. "Inequality and Police Strength: Conflict Theory and Coercive Control in Metropolitan Areas." American Sociological Review 44:913-925. . 1980. "Dimensions of Inequality and Public Policy in the States." Journal of Politics 42:291-306. Jasso, Guillermina. 1979. "On Gini's Mean Difference and Gini's Index of Concentra- tion: A Comment on Allison." American Sociological Review 44:867-70.

Johnston, J. 1984. Econometric Methods. New York: McGraw-Hill.

Keith, Bruce E., David R. Magleby, Candice J. Nelson, Elizabeth Orr, Mark Westlye,

and Raymond E. Wolfinger. 1992. The Myth of the Independent Voter. Berkeley and Los Angeles: University of California Press. Kernell, Samuel. 1986. Going Public: Strategies of Presidential Leadership. Washington, D.C.: Congressional Quarterly Press. Knoke, David, and Michael Hout. 1974. "Social and Demographic Factors in American Political Party Affiliations, 1952-72." American Sociological Review 391700

13. Kolm, S. 1976a. "Unequal Inequalities I." Journal of Economic Theory 12:416-41. . 19766. "Unequal Inequalities 11." Journal of Economic Theory 13:82-111.

Land, Kenneth C., David Cantor, and Stephen E. Russell. 1995. "Unemployment and Crime Rate Fluctuations in the Post-World War I1 United States." Pp. 55-79 in Crime and Inequality, edited by John Hagan and Ruth Peterson. Stanford, Calif.: Stanford University Press.

Lichtenstein, S., P. Slovak, B. Fischoff, M. Layman, and B. Combs. 1978. "Judged Frequency of Lethal Events." Journal of Experimental Psychology, Human Learn- ing, and Memory 4:551-78.

Liska, Allen E., J. J. Lawrence, and M. Benson. 1981. "Perspectives on the Legal

Order: The Capacity for Social Control." American Journal of Sociology 87:412

26. Liska, Allen E., J. J. Lawrence, and A. Sanchirico. 1982. "Fear of Crime as a Social Fact." Social Forces 60:760-71.

Liska, Allen E., Mitchell B. Chamblin, and Mark D. Reed. 1984. "Testing the Eco- nomic Production and Conflict Models of Crime Control." Social Forces 64:119


MacKinnon, J. J. 1991. "Critical Values of Cointegration Tests." In Long-Run Eco- nomic Relationships: Readings in Cointegration, edited by R. F. Engle and C. W.

J. Granger. New York: Oxford University Press. Maddala, G. 1992. Introduction to Econometrics. New York: Macmillan. Mathews, Steven A. 1989. "Veto Threats: Rhetoric as a Bargaining Game." Quarterly

Journal of Economics 104:347-69. McLanahan, Sara, and Gary Sandefur. 1994. Growing Up with a Single Parent. Cambridge, Mass.: Harvard University Press. Melossi, Dario. 1989. "An Introduction: Fifty Years Later, Punishment and Social Structure in Comparative Perspective." Contemporary Crises 13:311-26.

Michalowski, Raymond, and Michael Pearson. 1990. "Punishment and Social Struc- ture at the State Level: A Cross-Sectional Comparison of 1970 and 1980." Journal of Research on Crime and Delinquency 27:52-78.

Miller, Warren E. 1991. "Party Identification, Realignment, and Party Voting: Back to the Basics." American Political Science Review 85:557-68. Murray, Charles A. 1984. Losing Ground: American Social Policy, 1965-1980. New York: Basic Books.

Nerlove, M., and F. Diebold. 1990. "Unit Roots in Economic Time-Series: A Selective Survey." Pp. 3-69 in Advances in Econometrics, edited by T. Bailey. New York: JAI Press.

Neustadt, Richard F. 1990. Presidential Power and the Modem Presidents. New York: Macmillan. New York Times Index for the Published News of 1955. 1956. Vol. 43. New York: New York Times.

Nordhaus, William D. 1989. "Alternative Approaches to the Political Business Cycle." Brookings Papers on Economic Activity 2:l-68. Parker, Robert Nash, and Allan V. Horwitz. 1986. "Unemployment, Crime, and Im- prisonment: A Panel Approach." Criminology 24:751-73. Raffalovich, Lawrence A. 1994. "Detrending Time Series: A Cautionary Note." Sociological Methods and Research 22:492-519.

Rusche, Georg. (1933) 1980. "Labor Market and Penal Sanction: Thoughts on the Sociology of Punishment." In Punishment and Penal Reform, edited by T. Platt and P. Takagi. Berkeley and Los Angeles: University of California Press.

Rusche, Georg, and Otto Kirchheimer. 1939. Punishment and Social Structure. New York: Russell & Russell. Sampson, Robert J. 1987. "Urban Black Violence: The Effect of Male Joblessness and Family Disruption." American Journal of Sociology 93:348-82.

Sampson, Robert J., and William Julius Wilson. 1995. "Toward a Theory of Race, Crime, and Urban Inequality." Pp. 37-54 in Crime and Inequality, edited by John Hagan and Ruth D. Peterson. Stanford, Calif.: Stanford University Press.

Savelsberg, Joachim J. 1994. "Knowledge, Domination, and Criminal Punishment." American Journal of Sociology 99:911-43. Saxonhouse, Gary R. 1976. "Estimated Parameters as Dependent Variables." American Economic Review 66:178-83. Scheingold, Stuart A. 1991. The Politics of Street Crime. Philadelphia: Temple Uni- versity Press. Schneider, Fredrich, and Bruno S. Frey. 1988. "Politico-Economic Models of Macro-

economic Policy: A Review of the Empirical Evidence." In Political Business Cy- cles, edited by Thomas D. Willett. Durham, N.C.: Duke University Press. Schwartz, J., and C. Winship. 1980. "The Welfare Approach to Measuring Inequality." Sociological Methodology 12:l-36.

Sen, Amartya. 1973. On Economic Inequality. New York: Norton.

Skogan, Wesley G. 1990. Disorder and Decline. New York: Free Press.

Shively, W. Phillips. 1980. "The Nature of Party Identification: A Review of Recent Developments." Pp. 2 19-36 in The Electorate Reconsidered, edited by John C. Piece and John L. Sullivan. Beverly Hills, Calif.: Sage. Stockard, Jean, and Miriam M. Johnson. 1991. Sex and Gender in Society. Englewood Cliffs, N.J.: Prentice Hall. Sutton, John R. 1987. "Doing Time: Dynamics of Imprisonment in the Reformist State." American Sociological Review 52:612-23. Swanson, C. 1978. "The Influence of Organization and Environment on Arrest Policies in Major U.S. Cities." Policy Studies Journal 7:390-98. Tullis, Jeffrey K., 1987.The Rhetorical Presidency. Princeton, N.J.: Princeton Univer- sity Press.

Turk, Austen. 1969. Criminality and the Legal Order. Chicago: Rand McNally.

Van der Vaart, H. Robert. 1968. "Variances, Statistical Study of." 16:232-40 in Znter

national Encyclopedia of the Social Sciences, edited by David L. Sills. New York:


Vold, George. 1958. Theoretical Criminology. New York: Oxford.

White, Halbert. 1980. "A Heteroscedasticity-Consistent Covariance Matrix and a Di- rect Test for Heteroscedasticity." Econometrica 48:817-38. Willet, Thomas D. 1988. Political Business Cycles. Durham, N.C.: Duke University Press.

Williams, Kirk R., and Susan Drake. 1980. "Social Structure, Crime, and Criminaliza- tion: A; ~m~iricalExamination of the Conflict ~ers~ectiv;." sociological Quarterly 21563-76.

Yin, Peter. 1985. Victimization and the Aged. Springfield, Ill.: Charles C. Thomas.

  • Recommend Us