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.

Introduction

In principle, significant reductions in crime can be achieved through focusing on repeat victimisation for high volume crimes such as burglary (Tseloni et al., 2018). For residential burglary in particular, studies showing large reductions in both repeat victimisation and overall crime volumes through providing victims with increased home security, appear to have raised expectations internationally as to the potential effectiveness of such interventions (Laycock & Tilley, 2018; Siale, 2016). But there may be limits to their effectiveness in different contexts. In this paper, we present the results of the first 12 months of a randomised controlled trial (RCT) testing the effectiveness of providing Crime Prevention by Environmental Design (CPTED) measures to residential burglary victims for reducing their risk of revictimisation, in a novel context (New Zealand). We used a novel case-level randomised design to compare repeat victimisation between control, intention-to-treat, and treated groups. The results provide new insights into the circumstances in which providing security improvements may not be an optimal response to burglary. We first review the previous research on burglary revictimisation and CPTED that informed the initiative, and the hypothesised outcomes from the RCT.¹

Repeat victimisation

As with many crimes, being burgled increases the likelihood of being burgled again, so focusing on burglary victims to reduce the risk of repeat victimisations can be an important strategy for reducing burglary overall (Ellingworth et al., 1997; Tseloni et al., 2018). Repeat victimisation can occur because of an existing vulnerability (e.g. poor home security) that remains following the initial burglary, or because the initial burglary itself increases the risk: for example via the burglar returning or telling other offenders about the opportunity (Farrell et al., 1995; Pease, 1998). This risk is highest immediately following the offence, then sharply declines (Johnson et al., 2007; Polvi et al., 1991; Robinson, 1998); a pattern also confirmed in New Zealand (Chainey et al., 2018). Interventions aimed at reducing revictimisation—such as by addressing vulnerabilities exploited in the initial burglary—thus need to be implemented as soon as possible after the burglary (Farrell, 1995). The present intervention included a range of measures aimed at reducing burgled properties’ existing physical vulnerabilities, which are discussed next.

CPTED measures

Within the paradigms of Situational Crime Prevention (Clarke, 1980, 1997) and CPTED (Moffatt, 1983; Newman, 1973), many interventions aim to provide sustained reductions in crime by changing elements of the physical environment to make it harder for offenders to commit crime. Such interventions include ‘hardening’ (securing) crime targets to physically thwart offenders (Clarke, 1997; Thompson et al., 2018). Research into which target hardening measures prevent burglary concludes that the most cost effective combination is ‘WIDE’: window locks, internal lights on a timer, door locks, and external sensor activated lights (Thompson et al., 2018; Tseloni et al., 2017). Using a large dataset from the Crime Survey of England and Wales, these studies found that window and door locks appear in all the most effective combinations associated with reduced risk of burglary victimisation. Locks thus appear foundational, but combinations which also include methods such as sensor lights that deter as well as thwart are the most effective, possibly because harnessing two different prevention mechanisms deters different offender cohorts (Thompson et al., 2018). Alarms and surveillance cameras also appear in effective combinations but are less cost effective (Armitage, 2018a; Thompson et al., 2018). Additionally, measures that enable increased guardianship over a property by third parties can reduce victimisation risk (Reynald et al., 2018). Properties that are visible from the street facilitate guardianship from neighbours and passers-by who might act if an offender was spotted (Armitage, 2013; Moir et al., 2019; Reynald, 2010). Improving visibility to enable this natural surveillance has been shown to deter burglars by increasing the perceived risk involved in the crime (Armitage, 2018b; Clarke, 1997; Robinson, 2000; Thompson et al., 2018). Therefore, in the present intervention, locks and lights were included alongside trimming of foliage to improve lines of sight.

CPTED and revictimisation

The effectiveness of CPTED interventions in reducing burglary revictimisation depends on the context in which they are deployed (Farrell & Pease, 2017; Tseloni et al., 2018). Early success stories where large reductions in revictimisation were achieved proved difficult to replicate in other contexts (Tilley, 2000), prompting calls for attention to be paid to the mechanisms by which the intervention is expected to achieve its outcomes in a given study location (Farrell, 1995; Pawson & Tilley, 1997; Tilley, 2000). For example, CPTED interventions are more effective when tailored to the modus operandi (MO) of the burglaries they aim to prevent (Grove et al., 2012). WIDE measures will not prevent burglary via unlocked doors, open windows or deceiving a victim to gain entry (Farrell & Pease, 2017). But improving physical security and lines of sight can reduce both initial and repeat burglaries to properties that previously lacked these (Armitage, 2000; Armitage & Monchuk, 2011). The present intervention was therefore only implemented for properties where the triggering burglary’s MO indicated an underlying vulnerability that could be addressed with WIDE measures, with the aim of implementing these as soon as possible after the burglary when revictimisation risk is highest.

Another contextual factor is how the intervention is delivered. Providing interventions (such as security measures) to potential victims is more effective than simply advising them to implement such risk-reducing measures (Farrell & Pease, 2017; Groff & Taniguchi, 2019a; Grove et al., 2012; Johnson et al., 2017; Stokes & Clare, 2019), though exceptions exist (Budz et al., 2001; Elffers & Morgan, 2019). In New Zealand, previous research found that only small proportions of burglary victims make physical security improvements following a burglary (Siale, 2016). When surveyed, victims report a variety of barriers to implementing security measures, including financial cost and scepticism as to the level of risk (Groff & Taniguchi, 2019a; Stickle, 2015; Stokes & Clare, 2019), which the present initiative sought to overcome through providing these measures free of charge to victims through funding from the New Zealand Treasury.

Lastly, interventions aimed at preventing repeat offences can only prevent (at most) as many offences as would otherwise occur, and are thus more likely to achieve greater prevention effects in contexts with high rates of repeat victimisation (Farrell & Pease, 2017; Groff & Taniguchi, 2019b). Suburban New Zealand typically experiences lower levels of repeat burglary offending than observed in other jurisdictions (Chainey et al., 2018; Chainey & da Silva, 2016). It was therefore important to test this otherwise promising intervention in this context, as robustly as possible, accounting for expectations that the effects may be more modest than observed elsewhere.

Aims and hypotheses

The RCT aimed to determine whether providing eligible burglary victims with security measures consisting of locks, lights and improved lines of sight reduced revictimisation. Hypothesised outcomes were (1) a smaller proportion of intention-to-treat (ITT) and intervention group properties revictimised, compared to control group properties, during the trial period; and (2) higher perceptions of safety, and more positive perceptions of police, from those who have received the intervention, compared to control group victims. We also hypothesised that there would be no displacement effects, based on previous studies (e.g. Budz et al., 2001; Johnson et al., 2017) and the broader literature on displacement (Guerette, 2009; Guerette & Bowers, 2009; Johnson et al., 2014).

Method

In summary, the Locks, Lights and Lines of Sight (LLL) Initiative involved providing security measures (door locks, window stays, security lights and trimming of foliage) to eligible burglary victims, with the aim of preventing further victimisations. The first year of the RCT ran between the 8^th June 2018 and the 7^th June 2019. The following two sections describe the methods used to deliver and evaluate the LLL intervention respectively.

The intervention

Here we summarise the intervention process and describe the trial locations. Further procedural detail is provided in Appendix A.

Intervention process

Following a burglary, properties were first assessed for eligibility. Properties were ineligible if entry was gained through an unlocked door or open window, or through deception or other interaction with the victim, leaving burglaries with entry via force or with no sign of force (e.g. picking a lock) as eligible. Eligible properties assigned to an intention-to-treat group were then assessed by responding police staff to determine which, if any, of a list of approved security measures were lacking. Properties needing security measures were offered participation in the trial following an informed consent process. Relevant District Coordinators then put contractors in touch with consenting victims (including both the property owner and occupier, if different) to arrange installation of the security measures.

To reduce revictimisation risk immediately following the burglary an ambitious target was set for this process—from assessment to installation—to be completed within two days of the offence report. In the event, the process often took much longer. Installation was complete within two days of the offence report for 3.0% (n=24) of 803 cases analysed for the trial’s process evaluation; 12.3% (n=99) within 5 days. A further 14.9% took between 6 and 10 days, 24.5% took 11–20 days and 48.2% took 21 days or longer. The median completion time was 19 days (mean 29 days).

In total, 10,475 door locks or window stays were installed at 91.0% (n=678) of 745 properties for which invoices had been processed by the end of the trial.² Amongst these properties, a mean of 15.5 locks/stays were installed per property (SD 10.7, range 1–69). Lights were installed at 59.3% (n=442) of the properties (mean 1.7, SD 0.7, range 1–4). Trimming of foliage to improve lines of sight was undertaken at 3.0% (n=22) of the properties. Both locks and lights were installed in half of properties (49.7%/ n=370), only locks in 38.5% (n=287), and only lights in 7.0% (n=52). Appendix B provides additional details of the security measures available to burglary victims as part of the trial, and the numbers installed.

Study locations and trial coordination

Three of New Zealand’s 12 police districts were selected to run the trial based on sample size and practical considerations. Dwelling burglary volumes and repeat victimisation rates were initially identified at District, Area, Station and Census Area Unit levels. Selecting a large number of small locations with high repeat rates would have meant a higher potential effect size (larger reduction in repeats). However, selecting a small number of large areas (Districts) meant higher odds of successful implementation, as it would be easier to coordinate the process centrally at District level. The selected districts had burglary volumes and repeat rates that collectively met sample size requirements (see Appendix C) and were comparable to the national average. Selecting Districts that included both rural and urban areas and were thus representative in terms of operational policing contexts was also prioritised given that the trial took place in the context of decision-making about a possible national rollout of the initiative. Consideration was also given to where other burglary reduction initiatives were planned or already underway. The three trial Districts cover a large proportion of the North Island of New Zealand. They have a combined area of approximately 57,000 square kilometres and estimated population of about 950,000. This includes two cities with populations of about 165,000 and 130,000 and many smaller towns and rural settlements.

In each District, a District Coordinator, reporting to the National Coordinator, was responsible for coordinating the delivery of the intervention and collecting data necessary for its monitoring and evaluation. During the trial no substantial changes were made to the intervention. Minor process tweaks were made to speed up installs, including providing additional information and templates to police staff and contractors, and some contractors stockpiling security measures to reduce delays in installs due to stock running low.

RCT design and analysis approach

Randomisation method

The outcome evaluation employed a non-blind randomised controlled trial (RCT) design to establish a causal relationship between the intervention and repeat burglary. Consistent with previous studies (e.g. Johnson et al., 2017) we included both intention-to-treat (ITT) vs control group and intervention (treated) vs control group comparisons.

Randomisation occurred at the offence level, with eligible burglaries divided randomly into intention-to-treat and control groups. Offence level rather than geographically grouped randomisation was chosen to reduce the logistical burden of identifying whether a property was in or out of a geographic boundary and communicating this to the many staff involved. Randomising based on unequivocal information available to all staff working on a given case—the case reference number (CRN)—reduced the risk of allocation to the wrong group. Because the intervention was focused on repeat offences at the same property, cross-contamination due to neighbouring properties potentially being allocated to different groups was not an issue, by comparison with near-repeat studies which target neighbouring properties (Groff & Taniguchi, 2019a; Johnson et al., 2017).

Eligible burglaries with a CRN ending in an odd number were allocated to the intention-to-treat group, even numbers to the control group. The CRN is generated automatically when an offence is recorded in NIA. Given that records are constantly created nationally across all crime types, the last digit is random in any given case. CRNs cannot be manually overridden, thus preventing manipulation of the assignment of cases to either group. Group allocation was automatically filled out in the District Coordinators’ spreadsheet using an if-then formula on the case reference number. There were just nine instances where control group properties were accidentally offered the intervention by over-enthusiastic officers (0.6%). All intention-to-treat properties were actioned and were at some stage along the assessment to installation process at time of analysis.

Outcome measures

The primary outcome measure was whether a further burglary was reported to police at a property within the year of the trial.³ Best practice for measurement of repeat victimisation is to use a minimum of 12 months, and while a rolling-window (12 months following each offence) is preferable (Farrell et al., 2002), a fixed-window was used for the present analysis which was conducted at the end of the first year of the trial in order to inform decisions about its second year. Offences later in the period therefore have a shorter time-period within which repeats can occur. We also conducted survival analyses comparing the groups’ probability of surviving without a revictimisation accounting for each property’s time at risk of a further burglary, following previous studies (Elffers & Morgan, 2019; Johnson et al., 2017).⁴

Revictimisation was defined as there being reported to police any subsequent burglary at the property within the trial period. Revictimisations were identified using a combination of the address and its coordinates, such that different addresses (e.g. Flat 1, Flat 2) with overlapping coordinates, were not counted as repeats. Since revictimisations could themselves initiate the trial process, only the first repeat victimisation was counted. For example, if a control group property was revictimised and the second burglary was eligible, they would be offered security measures, but subsequent offences would be excluded from analysis. Their inclusion would have meant blending treatment and control groups, violating assumptions of statistical tests which require independence between groups.

Two secondary outcome measures examined severity of revictimisation. First, the New Zealand Crime Harm Index (CHI) was used to quantify the harm caused by repeat burglaries. The CHI provides a weighting for each offence based on an estimation of the minimum number of days in prison a first time offender would serve for the offence (Curtis-Ham & Walton, 2018). The CHI weights apply to specific offence codes which distinguish between burglaries occurring overnight vs daytime, and involving different values of theft (under $500, $500-$5000 or over $5000 in NZ Dollars). These value categories were also included as a separate measure. These severity measures also served to test whether the intervention group increased their tendency to report lower levels of burglary due to increased vigilance or trust in police following the intervention.

Additional secondary measures included self-reported revictimisation and perceptions of safety and the police elicited via a survey conducted by an independent research company. Survey invitations were sent at monthly intervals. Intervention group victims were invited a month after security installation; control group victims two months after the burglary. Participants were invited via email (if available) to fill the survey out via the company’s secure online survey platform. Alternatively, participants were invited, and/or the survey was undertaken, by phone (using Computer Assisted Telephone Interviewing) or by mail, depending on the contact information available or participants’ preferred method.⁵ By the end of the evaluation period, 655 victims had completed the survey: 318 from the intervention group and 337 from the control group (response rates of 54.2% and 43.2% respectively).⁶

Regarding revictimisation, respondents were asked to specify whether there had been any subsequent burglary, property damage or attempted break-in/suspicious behaviour at the property (either the dwelling or outbuildings). They were also asked whether these incidents were reported to police.

In terms of safety, respondents were asked: “thinking about your overall sense of freedom from crime, how safe or unsafe did you or do you feel in the following situations?” The five-point response scale ranged from very unsafe to very safe and there were 12 situations, one for each combination of 4 contexts and 3 timings in relation to the burglary. The contexts were: in your home during the day, in your home after dark, in your local neighbourhood during the day, and in your local neighbourhood after dark. The timings were: Before the burglary, straight after the burglary, and now (at the time of the interview).

Perceptions of police were assessed with the same questions used in the annual Citizens’ Satisfaction Survey (https://www.police.govt.nz/about-us/publication/citizens-satisfaction-survey-reports).⁷ Respondents were asked to describe their level of trust and confidence in police, in absolute terms (on a five-point scale from no trust and confidence to full trust and confidence), and in terms of the extent to which it had changed as a result of their recent contact with police (on a five-point scale from decreased a lot to increased a lot). Respondents were also asked to rate their satisfaction with the police staff who came to investigate the burglary (on a five-point scale from very dissatisfied to very satisfied).

We also measured various types of displacement as categorised in the relevant literature (e.g. Guerette, 2009; Johnson et al., 2014). The displacement analyses are detailed in Appendix D given the lack of a main effect.

Lastly, to identify specific mechanisms for any reduction in revictimisation, we tested for any differences in revictimisation between properties in the intervention group receiving different security measures. One measure set out in the Evaluation Plan was unable to be implemented: it was intended to compare the number of attempted (but unsuccessful) repeat burglaries between RCT groups, but this data is not codified or systematically recorded in police systems.

Analysis methods

Differences between groups (Control vs ITT, Control vs Intervention) on categorical outcome measures (e.g. revictimised or not, repeat offence value, survey responses) were tested with Chi Square. Differences between groups in the distribution of continuous outcome measures were tested using a t-test (crime harm index of repeats). Differences between groups in the risk of revictimisation over time since the initial burglary were tested with Cox Proportional Hazards models. Repeat and near repeat offences (a displacement measure) were identified using the Repeat and Near Repeat Classification tool in ArcGIS for Desktop. Statistical analyses were carried out in R (R Core Team, 2013) and SPSS.

Results

This section first describes the numbers and baseline characteristics of victims in each trial group, before presenting results for outcome measures relating to revictimisation and victim perceptions. It concludes with results of supplementary analyses by type of security measure and timing of revictimisation.

Eligibility and participation

Figure 1 displays the ‘participant flow’ for the RCT, including the numbers of participants who were randomly assigned, those lost for various reasons of attrition after randomisation, and the final numbers analysed per group for the primary outcome measure.⁸ In the year of the trial, 885 victims had agreed to participate, forming the intervention group for whom security measures had been (n=765), or were scheduled to be (n=120), installed. The remaining 308 of the ITT group were either excluded for need, risk or uncontactable reasons or were awaiting the victim’s decision whether to participate (‘consent pending’).

Fig. 1

CONSORT 2010 flow diagram of eligibility and attrition

To check for selection bias as a result of the various sources of attrition within the ITT group, the distribution of tenure in the excluded and included properties was compared (Table 1). Excluded properties were more likely to be social housing (Housing NZ) properties than those in the intervention group [X² (2, N = 1144) = 9.4, p = <.01, Cramér’s V = .1]. These properties were usually excluded for reasons of need (i.e. already having the security measures), rather than victims declining. Given the random assignment, most likely the same proportion of social housing properties in the control group also had sufficient existing security measures. Thus, provision of security measures to properties without them would remain the only difference between control and intervention groups.

Table 1 Distribution of tenure in the excluded and intervention groups

Further, there were no significant differences between control and intervention group survey respondents in age, gender or ethnicity. Although these personal characteristics are less relevant to burglary where the dwelling rather than a specific person is usually the target, the lack of difference provides further evidence against selection bias when comparing the control and intervention groups.

Revictimisation outcomes

The revictimisation (RV) rates for the intention-to-treat, intervention and control groups, were not statistically significantly different (see Table 2).⁹ Ten percent of properties in each group were revictimised within the 12-month trial period, with 5% in each group suffering a repeat burglary that was also eligible (for which the security measures were most relevant). There were also no significant differences in revictimisation harm as measured by the Crime Harm Index, or the value of property stolen (see Table 2).

Table 2 Revictimisation (RV) measures by RCT group

Likewise, the survival analyses revealed no differences in the risk of revictimisation over time from the initial burglary (see Figure 2; all comparisons were not statistically significant). The survival curves confirm that for all groups (control, ITT, intervention) revictimisations were most likely within the first few weeks, after which the risk levelled off. Notably, no difference in revictimisation emerged even after most intervention group installations were completed (62.5% were completed within 50 days of the initial burglary but the curves continue to track similarly).

Fig. 2

Survival curves comparing intention-to-treat (ITT) versus control groups (left panels) and intervention versus control groups (right panels) in risk of any burglary revictimisation (top panels) and eligible burglary revictimisation (bottom panels)

Significantly fewer intervention group survey respondents stated that there had been a subsequent break-in, damage or suspicious incident at the property (14% vs 20% of control respondents, X² (1, N = 603) = 4.0, p = <.05, Cramér’s V = .1, 95% CI -12.8–-.18%). But consistent with the data from offences reported to police, there was no difference between groups in relation to subsequent break-ins specifically (or any other specific type of subsequent incident). Nor was there any difference between groups in whether they said they reported subsequent incidents to the police.

Victim perceptions of safety and police

The survey results revealed that victims who received security measures now felt safer in their homes at night and had more positive views of police than control group victims. Comparisons of control and intervention group survey respondents’ perceptions of safety across the 12 situations revealed only one statistically significant difference: 45% of those in the control group felt safe or very safe in their home at night at the time of the survey, versus 54% in the intervention group [X² (1, N = 564) = 4.1, p = <.05, Cramér’s V = .1, 95% CI +0.3% - +17.5%].

In terms of attitudes to police, several positive effects emerged. By comparison with the control group, more intervention group respondents reported:

• a) They had full or quite a lot of trust and confidence in the police (63% vs 77%, X² (1, N = 653) = 14.6, p = <.001, Cramér’s V = .15, 95% CI +6.8 - +21.3%).

• b) Their trust and confidence in police had improved as a result of their recent contact with police regarding the burglary (27% vs 52%, X² (1, N = 653) = 39.8, p < .001, Cramér’s V = 0.3, 95% CI +16.8% - +32.0%).

• c) They were (very) satisfied with the staff who came to investigate the burglary (76% vs 90%, X² (1, N = 565) = 19.1, p < .001, Cramér’s V = .2, 95% CI +7.6% - +20.6%).

Security type

Analysis of revictimisation for different subgroups based on the type of security measures and over different time periods showed the same pattern as overall. There were no significant differences in revictimisation when comparing properties where a given type of security measure was installed, to those where that security measure was not installed (Table 3).

Table 3 Revictimisation rate for different security measures (N = 765)

Discussion

This study found that providing burglary victims with locks, lights and lines of sight did not reduce their risk of revictimisation within the 12-month study period. Correspondingly, neither displacement nor diffusion of benefits appear to have occurred. But victims who received security measures nonetheless reported feeling safer in their home at night and more positively towards police. These positive perceptual outcomes are consistent with those found by Johnson et al. (2017). We focus this section on exploring possible explanations for finding no effect on revictimisation.

One common reason for finding no effect in evaluations of policing interventions is implementation failure: the intervention is not fully delivered (Bowers & Johnson, 2006; Neyroud, 2017). However, the LLL initiative achieved high levels of implementation, comparable with other recent repeat or near repeat intervention studies (Groff & Taniguchi, 2019a; Hunter & Tseloni, 2018; Johnson et al., 2017; Pegram et al., 2018). All burglaries were assessed for eligibility, and all eligible properties were assigned to a group, with 25% of the intention-to-treat group then lost to the various sources of attrition. We believe the initiative’s multi-level approach to implementation (Fixsen et al., 2005), including governance and accountability components operating from frontline to Ministerial level facilitated this success. The high uptake rate is also unsurprising since victims offered the intervention were informed the estimated value of the security and its installation was $400 (in the event the average cost per property was $1,021.33). The issue appears to be less a matter of whether the intervention was delivered, but when.

We believe installation timing to have been an important contributing factor to the lack of effect of security measures in this study. Consistent with previous local (Chainey et al., 2018) and international research (Johnson et al., 2007; Polvi et al., 1991; Robinson, 1998), revictimisation risk was highest during the first week and dropped off over the following weeks. But by comparison with other studies where prevention advice or basic security equipment was able to be delivered rapidly following a triggering offence (Groff & Taniguchi, 2019a; Johnson et al., 2017), the current intervention was more intensive, requiring additional steps to arrange and complete installation. The delays experienced in security installation therefore reduced the intervention’s ability to prevent repeat offences during the highest risk period for repeats to occur, immediately following the initial burglary. However, timing cannot be the only explanation. We might still expect a difference to emerge over a longer time period for repeats to occur following security installation, but the survival curves show no difference out to over 300 days, and a separate evaluation following the second year of the trial recently reported no difference in revictimisation over that time period (Ashcroft et al., 2021).

An additional explanation is that there was less of a gap between control and intervention group victims’ level of security than expected—at least during the highest risk period for revictimisation. Significantly more control group victims reported they had installed new locks, window stays and security lights than intervention group victims (see Appendix A: Maintenance of standard service for the control group). This finding indicates that by the time they were surveyed—over a month after the burglary, many control group victims had installed WIDE measures; but at that point some intervention group victims would still have been waiting for their free measures to be installed.¹⁰ It also contrasts with previous New Zealand research informing our initial belief that providing prevention advice would be less effective than providing prevention measures directly (Siale, 2016). Thus, to the extent that the intervention provided measures that victims would otherwise have taken themselves, the groups’ revictimisation risks would have converged. Future research could focus on identifying burglary victims, or potential victims, who are less likely to implement their own security upgrades and exploring less costly means of encouraging or aiding them to do so.

Any effect of the intervention would also have depended on the extent to which the control and intervention groups used the security measures. The effectiveness of these measures relies on people using them (e.g. locking doors, turning on sensor lights). If those in the control group who installed their own measures were more vigilant in using them, this too could reduce the difference between the groups. However, the fact there was no difference in repeat victimisation of any kind—including through unlocked doors or open windows—suggests that both control and intervention group victims were just as likely to be more vigilant about security following the initial burglary.

A further factor that possibly reduced the difference between control and intervention groups is dosage. Not all victims in the intervention group received the full ‘dosage’ of security measures recommended to bring them up to the same standard. Interviews with those implementing the trial identified that there were occasions where some recommended measures were not installed, due to either not being on the approved list of security measures or owners/occupiers selectively consenting to some measures and not others. However, data on recommended versus installed measures were unfortunately not collected systematically to enable the extent of partial dosage to be quantified.

The fact that revictimisations occurred despite the security upgrades is suggestive of the upper limits of such prevention efforts, and the need to revise our original estimates of potential prevention effect downwards. Our results suggest that some offenders are not thwarted or deterred by improved security, having sufficient determination or sophistication to overcome it, especially in light of the myriad other factors that would continue to ‘flag’ the property as a good target (Armitage, 2018b; Cromwell et al., 1990; Nee, 2015; Pease, 1998). That such a cohort exists is consistent with studies of burglars in other jurisdictions (Clare, 2011; Nee & Meenaghan, 2006; Sanders et al., 2016). Further, the MO categories used to determine eligibility may not have been sufficiently narrow. Eligible burglaries included those where entry was gained via breaking windows, which door locks and window stays would not thwart, and daylight burglaries, for which lighting would not be relevant. Our results thus lend further support to the need to target interventions to very specific problems for prevention effects to be optimal (Clarke, 1997; Grove et al., 2012).

The above considerations highlight several limitations which appear to have contributed to the lack of effect of this intervention on 12-month revictimisation. Two more limitations warrant mention here. First, the case level RCT design limited the ability to analyse whether the intervention affected not simply whether properties were revictimised but how frequently. The security measures, while not affecting whether a subsequent burglary occurred, may have prevented additional burglaries that would otherwise have occurred. As Groff and Taniguchi (2019a) point out, such trade-offs between implementation and evaluation are often necessary in this kind of research. Future studies might draw the line in favour of enabling measurement of revictimisation frequency.

Second, the district level displacement analyses used a quasi-experimental case control design, outside of the RCT proper. Despite the CausalImpact label, a causal inference cannot be made as the design does not rule out differences between the trial and control districts in addition to the trial. This limits the ability to make causal inferences, as it is not known whether the trial was the only difference between the trial and control districts. Although important to acknowledge, this point is moot in light of the null results.

Conclusion

The findings of this study do not warrant as simplistic a conclusion as ‘security measures do not prevent burglary’. The results instead make an important contribution to our understanding of the contexts in which the effectiveness of providing burglary victims with these specific security improvements may be limited, with obvious implications for policing practice. Our results are likely to generalise to similar contexts where revictimisation rates are low, victims are proactive in implementing security improvements and prompt installation cannot be achieved. Targeting locations with the highest revictimisation rates whilst ensuring speedy security assessments and installation is a challenge worthy of future research innovation.

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).