10 Appendix A

The Appendix includes excerpts from the original article which presented the research known as the Minneapolis Domestic Violence Experiment. The excerpts primarily focus on the methodology portions of the article. The citation to the article is provided to access the full-text article.

The Specific Deterrent Effects of Arrest for Domestic Assault1


University of Maryland, College Park and Police Foundation


University of California, Santa Barbara


42 Patrol Officers of the Minneapolis Police Department, Nancy Wester, Donileen Loseke, David Rauma, Debra Morrow, Amy Curtis, Kay Gamble, Roy Roberts, Phyllis Newton, and Gayle Gubman

The specific deterrence doctrine and labeling theory predict opposite effects of punishment on individual rates of deviance. The limited cross-sectional evidence available on the question is inconsistent, and experimental evidence has been lacking. The Police Foundation and the Minneapolis Police Department tested these hypotheses in afield experiment on domestic violence. Three police responses to simple assault were randomly assigned to legally eligible suspects: an arrest; advice “(including, in some cases, informal mediation); and an order to the suspect to leave for eight hours. The behavior of the suspect was tracked for six months after the police intervention, with both official data and victim reports. The official recidivism measures show that the arrested suspects manifested significantly less subsequent violence than those who were ordered to leave. The victim report data show that the arrested subjects manifested significantly less subsequent violence than those who were advised. The findings falsify a deviance amplification model of labeling theory beyond initial labeling and fail to falsify the specific deterrence prediction for a group of offenders with a high percentage of prior histories of both domestic violence and other kinds of crime.

Research Design

The Police Foundation and the Minneapolis Police Department agreed to conduct a randomized experiment. The design called for random assignment of arrest, separation, and some form of advice which could include mediation at the officer’s discretion. In addition, there was to be a six-month follow-up period to measure the frequency and seriousness of domestic violence after each police intervention. The advantages of randomized experiments are well known and need not be reviewed here (see, e.g., Cook and Campbell, 1979).

The design only applied to simple (misdemeanor) domestic assaults, where both the suspect and the victim were present when the police arrived. Thus, the experiment included only those cases in which police were empowered (but not required) to make arrests under a recently liberalized Minnesota state law; the police officer must have probable cause to believe that a cohabitant or spouse had assaulted the victim within the last four hours (but police need not have witnessed the assault). Cases of life-threatening or severe injury, usually labeled as a felony (aggravated assault), were excluded from the design for ethical reasons.

The design called for each officer to carry a pad of report forms, color coded for the three different police actions. Each time the officers encountered a situation that fit the experiment’s criteria, they were to take whatever action was indicated by the report form on the top of the pad. We numbered the forms and arranged them in random order for each officer. The integrity of the random assignment was to be monitored by research staff observers riding on patrol for a sample of evenings.

After police action was taken, the officer was to fill out a brief report and give it to the research staff for follow-up. As a further check on the randomization process, the staff logged in the reports in the order in which they were received and made sure that the sequence corresponded to the original assignment of treatments.

Anticipating something of the victims’ background, a predominantly minority, female research staff was employed to contact the victims for a detailed face-to-face interview, to be followed by telephone follow-up interviews every two weeks for 24 weeks. The interviews were designed primarily to measure the frequency and seriousness of victimizations caused by the suspect after the police intervention.1 The research staff also collected criminal justice reports that mentioned the suspect’s name during the six-month follow-up period.

Conduct of the Experiment

As is common in field experiments, implementation of the research design entailed some slippage from the original plan. In order to gather data as quickly as possible, the experiment was originally located in the two Minneapolis precincts with the highest density of domestic violence crime reports and arrests. The 34 officers assigned to those areas were invited to a three-day planning meeting and asked to participate in the study for one year. All but one agreed. The conference also produced a draft order for the chief’s signature specifying the rules of the experiment. These rules created several new situations to be excluded from the experiment, such as if a suspect attempted to assault police officers, a victim persistently demanded an arrest, or if both parties were injured. These additional exceptions, unfortunately, allowed for the possibility of differential attrition from the separation and mediation treatments. The implications for internal validity are discussed later.

The experiment began on March 17, 1981, with the expectation that it would take about one year to produce about 300 cases (it ran until August 1, 1982 and produced 330 case reports). The officers agreed to meet monthly with the project director (Sherman) and the project manager (Wester). By the third or fourth month, two facts became clear: (1) only about 15 to 20 officers were either coming to meetings or turning in cases; and (2) the rate at which the cases were turned in would make it difficult to complete the project in one year. By November, we decided to recruit more officers in order to obtain cases more rapidly. Eighteen additional officers joined the project, but like the original group, most of these officers only turned in one or two cases. Indeed, three of the original officers produced almost 28 percent of the cases, in part because they worked a particularly violent beat, and in part because they had a greater commitment to the study. Since the treatments were randomized by officer, this created no internal validity problem. However, it does raise construct validity problems to which we will later return.

There is little doubt that many of the officers occasionally failed to follow fully the experimental design. Some of the failures were due to forgetfulness, such as leaving the report pads at home or at the police station. Other failures derived from misunderstanding about whether the experiment applied in certain situations; application of the experimental rules under complex circumstances was sometimes confusing. Finally, from time to time there were situations that were simply not covered by the experiment’s rules.

Whether any officers intentionally subverted the design is unclear. The plan to monitor randomization with ride-along observers broke down because of the unexpectedly low incidence of cases meeting the experimental criteria. The observers had to ride for many weeks before they observed an officer apply one of the treatments. We tried to solve this problem with “chase-alongs,” in which the observers rode in their own car with a portable police radio and drove to the scene of any domestic call dispatched to any officer in the precinct. Even this method failed.

Thus, we are left with at least two disturbing possibilities. First, police officers anticipating (e.g., from the dispatch call) a particular kind of incident, and finding the upcoming experimental treatment inappropriate, may have occasionally decided to void the experiment. That is, they may have chosen to exclude certain cases in violation of the experimental design. This amounts to differential attrition, which is clearly a threat to internal validity. Note that if police officers blindly decided to exclude certain cases (e.g., because they did not feel like filling out the extra forms on a given day), all would be well for internal validity.

Second, since the recording officer’s pad was supposed to govern the actions of each pair of officers, some officers may also have switched the assignment of driver and recording officer after deciding a case fit the study in order to obtain a treatment they wanted to apply. If the treatments were switched between driver and recorder, then the internal validity was again threatened. However, this was almost certainly uncommon because it was generally easier not to fill out a report at all than to switch.

Table 1 shows the degree to which the treatments were delivered as designed.2 Ninety-nine percent of the suspects targeted for arrest actually were arrested, while only 78 percent of those to receive advice did, and only 73 percent of those to be sent out of the residence for eight hours were actually sent. One explanation for this pattern, consistent with the experimental guidelines, is that mediating and sending were more difficult ways for police to control the situation, with a greater likelihood that officers might resort to arrest as a fallback position. When the assigned treatment is arrest, there is no need for a fallback position. For example, some offenders may have refused to comply with an order to leave the premises.

TABLE 1 | Designed and Delivered Police Treatments in Spousal Assault Cases

Designed Treatment

Delivered Treatment









































Such differential attrition would potentially bias estimates of the relative effectiveness of arrest by removing uncooperative and difficult offenders from the mediation and separation treatments. Any deterrent effect could be underestimated and, in the extreme, artifactual support for deviance amplification could be found. That is, the arrest group would have too many “bad guys” relative to the other treatments.

With the interviews of the victims, only 205 (of 330, counting the few repeat victims twice) could be located and initial interviews obtained; a 62 percent completion rate. Many of the victims simply could not be found, either for the initial interview or for follow-ups: they either left town, moved somewhere else or refused to answer the phone or doorbell. The research staff made up to 20 attempts to contact these victims, and often employed investigative techniques (asking friends and neighbors) to find them. Sometimes these methods worked, only to have the victim give an outright refusal or break one or more appointments to meet the interviewer at a “safe” location for the interview.

The response rate to the bi-weekly follow-up interviews was even lower than for the initial interview, as in much research on women crime victims. After the first interview, for which the victims were paid $20, there was a gradual falloff in completed interviews with each successive wave; only 161 victims provided all 12 follow-up interviews over the six months, a completion rate of 49 percent. Whether paying for the follow-up interviews would have improved the response rate is unclear; it would have added over $40,000 to the cost of the research. When the telephone interviews yielded few reports of violence, we moved to conduct every fourth interview in person, which appeared to produce more reports of violence.

In sum, despite the practical difficulties of controlling an experiment and interviewing crime victims in an emotionally charged and violent social context, the experiment succeeded in producing a promising sample of 314 cases with complete official outcome measures and an apparently unbiased sample of responses from the victims in those cases.


Two kinds of outcome measures will be considered. One is a police-recorded “failure” of the offender to survive the six-month follow-up period without having police generate a written report on the suspect for domestic violence, either through an offense or an arrest report written by any officer in the department, or through a subsequent report to the project research staff of a randomized (or other) intervention by officers participating in the experiment. A second kind of measure comes from the interviews with victims, in which victims were asked if there had been a repeat incident with the same suspect, broadly defined to include an actual assault, threatened assault, or property damage.

Overall, the police data indicate that the separation treatment produces the highest recidivism, arrest produces the lowest.

When self-report data are used, these results suggest a different ordering of the effects, with arrest still producing the lowest recidivism rate (at 19%), but with advice producing the highest (37%).

An obvious rival hypothesis to the deterrent effect of arrest is that arrest incapacitates. If the arrested suspects spend a large portion of the next six months in jail, they would be expected to have lower recidivism rates. But the initial interview data show this is not the case: of those arrested, 43 percent were released within one day, 86 percent were released within one week, and only 14 percent were released after one week or had not yet been released at the time of the initial victim interview. Clearly, there was very little incapacitation, especially in the context of a six-month follow-up. Indeed, virtually all those arrested were released before the first follow-up interview.


1 The protocols were based heavily on instruments designed for a NIMH-funded study of spousal violence conducted by Richard A. Berk, Sarah Fenstermaker Berk, and Ann D. Witte (Center for Studies of Crime and Delinquency, Grant #MH-34616–01). A similar protocol was developed for the suspects, but only twenty-five of them agreed to be interviewed.

2 Sixteen cases were dropped because no treatment was applied or because the case did not belong in the study (i.e., a fight between a father and son).


Cook, Thomas D. and Donald T. Campbell 1979 Quasi-Experimentation: Design and Analysis Issues for Field Settings. Chicago: Rand McNally.


1 Direct all correspondence to: Lawrence W. Sherman, Police Foundation, 1909 K Street N.W., Washington, D.C. 20006.This paper was supported by Grant #80-IJ-CX-0042 to the Police Foundation from the National Institute of Justice, Crime Control Theory Program.
Points of view or opinions stated in this document do not necessarily represent the official position of the U.S. Department of Justice, the Minneapolis Police Department, or the Police Foundation.
We wish to express our thanks to the Minneapolis Police Department and its Chief, Anthony V. Bouza, for their cooperation, and to Sarah Fenstermaker Berk, Peter H. Rossi, Albert J. Reiss, Jr., James Q. Wilson, Richard Lempert, and Charles Tittle for comments on an earlier draft of this paper.
American Sociological Review 1984, Vol. 49 (April:261–272)© Sherman, Lawrence W. and Richard A. Berk. 1984. “The Specific Deterrent Effects of Arrest for Domestic Assault” American Sociological Review 49:261–272.


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