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Resisting Broken Windows

The Effect of Neighborhood Disorder on Political Behavior

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Abstract

Concurrent housing and opioid crises have increased exposure to street-crime, homelessness and addiction in American cities. What are the political consequences of this increased neighborhood disorder? We examine a change in social context following the relocation of homelessness and drug treatment services in Boston. In 2014, an unexpected bridge closing forced nearly 1000 people receiving emergency shelter or addiction treatment to relocate from an island in the Boston Harbor to mainland Boston, causing sustained increases in drug-use, loitering, and other features of neighborhood disorder. Residents near the relocation facilities mobilized to maintain order in their community. In the subsequent Mayoral election, their turnout grew 9% points while participation in state and national elections was unchanged. However, increased turnout favored the incumbent Mayor, consistent with voter learning about candidate quality following local shocks. Voters responded to neighborhood changes at the relevant electoral scale and rewarded responsive politicians.

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Notes

  1. But see van Noord et al. (2018).

  2. The city had previously announced plans to begin repairing the 63-year old bridge in September. An engineer involved with the reconstruction project told local media that reconstruction would only require partial lane closures, and “under no circumstance will the whole bridge be closed” (Burrell 2014).

  3. The 2017 images are from July, while the 2013 images are from September. Google did not offer images in 2017 and 2013 from the same month.

  4. The South End Fitness Center was used as a shelter until the Southampton Street Shelter opened in June 2015. We include it as a treatment indicator for the 2014 election only.

  5. Our turnout analyses are restricted to voters who lived in the same residence and were registered to vote across both election cycles.

  6. Because of the equivalence between “fixed-effects” and first differences with two time periods, an equivalent model can be expressed in terms of changes in turnout for each voter: \(\text {Turnout}_{i1} - \text {Turnout}_{i1} = \beta [I(d_{i} < d^*)] + \epsilon _{i} \)

  7. We do not analyze changes in voting between city council local elections in non-mayoral election years due to variation across city council districts in challenges to incumbent city councillors. We also do not estimate changes in vote share between the 2010 and 2014 midterm elections because Boston’s electoral precincts were changed in 2011 following the decennial census.

  8. Our pre-analysis plan specified bootstrap standard errors. Results are not substantially or substantively different using either method, but the clustered standard errors tend to be larger than the bootstrapped ones, so we chose to report the more conservative clustered standard errors. We include bootstrapped standard errors in the Appendix Table A8.

  9. Including fixed effects for all city council districts, instead of a single dummy for Tito Jackson’s district, deviates from our pre-registration. After receiving feedback about differential levels of competitiveness in ward city council races concurrent with the mayoral race, we were persuaded to use council district fixed effects. Results are substantively similar in sign, magnitude, and significance.

  10. Homelessness-related 311 calls were identified by string searching the open-ended CLOSURE_REASON field in the data for the string “homeless” and using only calls in the set of call types (“Requests for Street Cleaning”, “Ground Maintenance”, “Poor Conditions of Property”, “CE Collection”, “Illegal Dumping”, “General Comments For a Program or Policy”, “Housing Discrimination Intake Form”, and “Highway Maintenance”) corresponding to these explicitly designated homelessness calls.

  11. The 2017 coefficient is positive, but this is conditional on the distance being at zero (and the covariates being at base categories, where applicable). Generally, mayoral turnout was lower in 2017 than 2013.

  12. The 2014 midterms occurred shortly after the Long Island Bridge closing, and voters may have not had time to process and react to the neighborhood changes. The national election turnout results do show positive turnout coefficients at the largest definitions of treatment, but these coefficients shrink towards zero and all but two lose significance in the specifications with matched covariates (Table A11 in the Appendix).

  13. The main specifications for vote choice differ from those in our pre-registration. A detailed explanation is provided in Appendix Section 7.

  14. Precinct boundaries changed before the 2012 election, precluding a similar analysis of 2014 and 2010 vote share.

  15. In Section 8 of the Appendix, we estimate heterogeneous treatment effects by race (Figs. A6 and A7) and placebo tests (Figs. A8, A9, A10) which explore racial threat as a channel through which these effects took place. We find some evidence consistent with a larger treatment effect among whites, though treatment effects were present among all racial groups. Placebo tests of racially similar neighborhoods as those around the relocation sites do not exhibit the turnout increase we have shown. In Appendix Section 9, we present results from a robustness check (Figs. A17 and A18) using randomization inference (comparing the observed result with thousands of hypothetical alternative relocation sites).

  16. In Appendix Section 8, we interact treatment with homeownership status and do not find larger impacts on homeownership (Fig. A18).

  17. It is also possible that the pro-incumbent effect was caused by increased Walsh campaign activity in 2017. We have found no clear evidence that the Walsh campaign devoted greater resources to voter contact or campaign events in the treatment areas, but it is difficult to rule out that this could have contributed to the effects.

  18. It is possible that other newly-salient issues in this area (e.g. crime) also favored Walsh.

  19. The political effects of other kinds of shocks (such as natural disasters) similarly depend on the government’s response (Healy and Malhotra 2009, 2010; Chen 2013).

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Acknowledgements

We thank Ryan Enos and Stephen Pettigrew for sharing voterfile data and Jenna Savage of the Boston Police Department for consultation and providing 911 call data. We are also grateful for generous support from the Harvard University Inter-faculty Initiative on Medications and Society. This project has benefited from conversations with Ryan Enos, Jennifer Hochschild, Steve Ansolabehere, Jon Rogowski, Riley Carney, Melissa Sands, Justin de Benedictis-Kessner, Shom Mazumder, Michael Hankinson, Alex Mierke-Zatwarnicki, Hanno Hilbig, Shiro Kuriwaki, and Justin Pottle. We further thank audiences and discussants at the annual meetings of the 2019 Midwestern Political Science Association, the 2019 International Society of Political Psychology, the 2019 NYU CESS Experimental Political Science Conference, the 2019 Harvard Experimental Political Science Conference, and the 2019 Toronto Political Behaviour Workshop.

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  1. Department of Government, Harvard University, 1737 Cambridge Street, Cambridge, MA, 02138, USA

    Jacob R. Brown & Michael Zoorob

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  1. Jacob R. Brown
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Correspondence to Jacob R. Brown.

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This project was supported by the Harvard University Inter-faculty Initiative on Medications and Society. The analysis was pre-registered with Evidence in Governance and Politics. The pre-registration materials can be found at https://osf.io/5bwcq. Replication data and code can be found at https://doi.org/10.7910/DVN/EFTYVK.

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Brown, J.R., Zoorob, M. Resisting Broken Windows. Polit Behav 44, 679–703 (2022). https://doi.org/10.1007/s11109-020-09626-1

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