Locks, lights, and lines of sight: an RCT evaluating the impact of a CPTED intervention on repeat burglary victimisation

Abstract

Objectives

This study tested whether a police-led initiative providing a CPTED (Crime Prevention by Environmental Design) intervention to residential burglary victims reduced revictimisation.

Methods

Victims of eligible burglaries were randomly allocated to intention-to-treat and control groups in three New Zealand Police districts. Following the qualifying burglary, intention-to-treat victims were offered free installation of window and door locks, security lights and improved lines of sight (foliage trimming). Revictimisation, perceptions of safety and police, and displacement outcomes were measured using police administrative data and a survey of victims.

Results

During the first trial year, there was no effect on revictimisation but positive effects on victims’ perceptions. Supplementary analyses suggest implementation and contextual factors which contributed to the lack of effect on revictimisation.

Conclusions

The findings highlight the limitations of CPTED interventions in particular contexts and confirm the importance of delivering prompt, contextually tailored interventions for the prevention of repeat burglary victimisation.

Appendices

Appendix A Detailed procedural information about the intervention

Eligibility criteria: technical specifications

The specific technical criteria for eligibility were based on codes used in the NIA system as follows:

• 1. The offence was coded as a burglary in the National Intelligence Application (NIA).

• 2. The burglary occurred between 8 June 2018 and 7 June 2019.¹¹

• 3. The case was not recoded to an ineligible offence code or closed with a Closure Reason code of ‘error’, ‘duplicate’, ‘not an offence’. This criterion removed cases which on further investigation were either not burglaries or had been entered in error.

• 4. The Scene Subtype code was ‘dwelling’ or ‘vacant dwelling’. This criterion filtered to burglaries of residential dwellings, excluding burglaries of outbuildings or yards, other residential premises such as hotels and campervans, and commercial premises.

• 5. The Method of Entry code was: ‘jemmy/pry’, ‘smash/break’, ‘secure with no sign of forced entry’ or ‘rare’. This criterion excluded burglaries where entry was gained through an unlocked door or open window, or through deception or other interaction with the victim. The categories included involved situations where there were the use of keys/lock picking (making lock improvements relevant) and rare, sophisticated methods of forcing entry such as removing windows entirely (making window stays relevant).

• 6. The dwelling had its own entrance. This ruled out apartments with communal entry systems, for which the approved list of security measures were not a feasible option.

Process for delivering security measures

Following a burglary, eligible properties randomly assigned to the intention-to-treat group were assessed by Scene of Crime Officers (SOCOs) or responding police officers¹² to determine which, if any, of the approved security measures¹³ were lacking. The occupiers (and owners, if different) were then offered participation in the trial unless:

• 1) the assessment showed they did not need any of the approved security measures offered,

• 2) a risk assessment showed that the offer or installation of measures would incur a health or safety risk to police staff or contractors hired to install the measures, or

• 3) trial staff were unable to contact the victim after several attempts for an extended period of time.¹⁴

The offer of participation followed an informed consent process and required the consent of both the occupier and owner.¹⁵ Following consent, the District Coordinators sent a work order to approved contractors who then completed the installation work (sometimes over several visits). Last, the District Coordinators followed up with victims to check that the installation was completed satisfactorily.

Maintenance of standard service for the control group

During the trial, all burglary victims were to receive the standard service provided by police, so that the only difference between the trial groups was the intervention described above. Information collected by an independent research company as part of a process evaluation indicates that this occurred. Interviewed attending officers and SOCOs reported that all burglary victims received the same speed of service, investigative responses such as forensic evidence gathering, and burglary prevention advice. Administrative data confirmed no difference between groups in the average time between the offence being reported and the date of SOCO or attending officer’s attendance (median 1 day). When surveyed, intervention group victims were more likely than control group victims to recall police staff discussing ways to improve security with them (95.2%, 298 vs 62%, 198 respectively) [X² (1, N = 632) = 100.8, p <.001, Cramér’s V = 0.4, 95% CI -39.3–-27.0%]. However, victims may simply be more likely to recall security advice when it is followed by the provision of security. If the control group were less likely to receive the standard burglary prevention advice, one would expect them to be less likely to act on it by installing their own security measures. But to the contrary, both groups were equally likely to report installing at least one security measure, and the control group was more likely than the intervention group to report installing new door locks, window stays and lights.¹⁶

Coordination and quality assurance

The District Coordinators played a pivotal role in ensuring full implementation of the intervention and ensuring the quality of data required for its evaluation. They:

• ensured all burglaries were assessed for eligibility,

• ensured all intention-to-treat group burglaries were assessed for security needs and offered participation accordingly,

• checked the assessments and records in NIA to ensure these were accurate and complete,

• liaised with frontline staff, victims, and contractors, to coordinate the assessments and installations,

• recorded all stages of the process for each burglary, from eligibility criteria through to the details of what was installed, when and the costs in a spreadsheet,

• identified any health or safety risks, and

• liaised with District staff to raise awareness of the trial and identify and mitigate any threats to its implementation, including any other planned burglary related initiatives that might interfere with the trial. No other large-scale burglary initiatives were undertaken in the study Districts during the first year of the trial, and any risk posed by short-term local initiatives (e.g. hotspot patrols) was also mitigated by our case-level randomisation, which ensured that control, ITT and intervention properties remained comparable in all respects other than the LLL intervention.

Daily¹⁷ and weekly data reports from NIA acted as audit checks to identify any burglaries that may have been missed or updated since the initial report. Using this data, Weekly Performance Dashboards provided process measures for each stage of the process, to track eligibility, attrition, and timeliness.

Appendix B Technical details of the security measures

Table 4 provides details of the security measures installed.

Table 4 Number and proportion of properties where each security measure was installed

Appendix C Power and sample size calculations

Minimum sample sizes for the primary outcome measure (revictimisation), for several scenarios ranging from optimistic to conservative, were determined by power calculations at the outset of the trial, and updated after a 2-week feasibility study that enabled more accurate estimates of the number of eligible properties and consent rates. Table 5 sets out calculations of the required sample size based on an optimistic effect size that the police considered would be operationally meaningful in terms of overall reductions in burglary considering targets set by the government at the time (New Zealand Police, 2019). This calculation thus reflected an effect size of practical, rather than theoretical, interest (Lakens, 2021). First, expected effectiveness was estimated as the 12-month revictimisation rate (proportion of victims revictimised) in the trial Districts, minus the proportion revictimised within a week of the original burglary (in case security was not installed in that period). From there, the expected effectiveness was further adjusted to reflect that fewer than 100% of future burglaries would be prevented by the security measures. The optimistic estimate meant a 5.0 percentage point difference when comparing the intervention and control group (i.e. 3.9% versus 8.9% revictimised), requiring 75% prevented, which was viewed as plausible considering the targeting of the security measures to the circumstances of the initial burglary. The minimum sample sizes in each group necessary to detect an effect of that size at 80% power was then calculated for optimistic and conservative consent rate scenarios, being the consent rate during the feasibility period of 95% (37 of 39 properties) and 90%, respectively.

Based on burglaries reported between 1 June 2017 and 31 May 2018 and the eligibility rate observed in the feasibility period, we estimated that 2,998 properties would be eligible in the year of the trial, exceeding the requisite sample size (n=828) for the optimistic scenario by approximately three times. If the effect size was halved (h=.1, or a 2.5 percentage point difference), this sample would be 93% and 90% of the requisite number at 95% and 90% consent rates respectively. Additional power calculations for an intention-to-treat comparison applying more conservative effect sizes and consent rates indicated that the trial would need to be extended beyond the first year to achieve a sufficient sample.

In the event, 2,614 properties were eligible in the first year, meaning that the present analysis risked Type II error (falsely accepting the null hypothesis of no difference) for the intention-to-treat comparison if the true effect was very small. This risk was acceptable for the purpose of the present analysis, conducted to inform decisions about the initiative, because there would be little practical difference between concluding the intervention was not effective or was so marginally effective as to not warrant its cost.

Table 5 Power and sample size calculations for the trial districts combined

Appendix D Displacement analyses

Displacement measures

Table 6 shows the measures of displacement employed.

Table 6 Displacement measures

Analysis methods

To test for target and offence displacement, we compared pre-intervention and post-intervention monthly offence counts in the trial districts and a group of control districts, using controlled interrupted time series analysis (Lopez Bernal et al., 2018). This analysis was conducted using the R package MarketMatching (Larsen, 2016) which provides a user-friendly workflow drawing on the functions of CausalImpact (Brodersen et al., 2015) and dtw (Dynamic Time Warping, Tormene et al., 2009) packages. CausalImpact has previously been used to identify the effects of a crime focused intervention in a quasi-experimental study (Ratcliffe et al., 2017). The dynamic time warping analysis first identifies a set of control areas which best match the intervention area’s pre-intervention time series. The control time series are then fed to CausalImpact to construct a Bayesian structural time series model which produces a counterfactual prediction for the post-intervention period, i.e. the pattern predicted to have occurred had the intervention not been implemented. The observed (trial districts’) post-intervention time series is then compared to the counterfactual prediction. In our context, a divergence of the observed from predicted time series would indicate displacement (observed > predicted) or diffusion (observed < predicted). A 36 month pre-intervention time period was used, to enable seasonal patterns to be accounted for, consistent with previous research into seasonality in crime time series (Hipp et al., 2004; Linning et al., 2017).¹⁸

Results

Consistent with there being no difference in revictimisation overall, we found little evidence of displacement. The only indication of displacement was that intervention group properties were significantly more likely to have near repeat burglary occur within 200m, though this effect was very small (Table 7, X² (1, N = 2,306) = 5.6, p = .018). In light of the lack of a main effect and no 70m effect (Table 7), we treat this as a spurious result rather than evidence of displacement, in line with Groff and Taniguchi’s (2019a) approach to a similar result. There were no significant differences between groups indicative of MO displacement: 3-4% suffered a burglary outside or to an outbuilding; 1–2% suffered a burglary with an ineligible method of entry (Table 7). Analysis of the timing of repeat victimisations revealed no differences between groups in the number of days between the initial and subsequent burglary, suggesting no temporal displacement (Table 7).

Table 7 Measures of MO, spatial and temporal displacement by RCT group

The CausalImpact analysis showed no evidence of displacement to other types of crime. The time series for other burglary and other dishonesty offences per month during the trial period did not diverge outside the range predicted from the matched group of control districts. Table 8 presents the results of the matching process to identify control districts and CausalImpact analysis for each potential displacement crime type. As described in the table notes, several parameters were set to optimise the fit between the pre-intervention trial and matched controls’ time series. Fit was measured by the Durbin-Watson statistic (DW, a measure of autocorrelation in the residuals with an optimal value of 2) and Mean Absolute Percentage Error (MAPE, with lower values better). The moderate levels of fit indicate that the matched districts were not perfect controls for the trial districts, requiring caution in their use as a counterfactual. Even assuming their appropriateness as controls, the analysis shows that the observed crime volumes did not deviate sufficiently from the counter-factual expected values to conclude that any target or crime type displacement occurred.

Table 8 Matching and ‘CausalImpact’ analysis results for crime displacement types

Figure 3 shows the expected and observed volumes of crime per month for each crime type. The steep drop in the top graph reflects a change in recording practice in April 2017. At no point during the trial period does the observed crime volume in the trial districts deviate outside the 95% confidence intervals of the expected values.

Fig. 3

Expected time series (orange line) with 95% confidence intervals and observed trend in the trial districts (green line) for (a) non-residential burglary and (b) theft, prior to and during the trial period (dotted vertical line).