Handgun waiting periods reduce gun deaths

Michael Luca, Deepak Malhotra, and Christopher Poliquin
PNAS November 14, 2017 114 (46) 12162-12165; published ahead of print October 16, 2017 https://doi.org/10.1073/pnas.1619896114

  1. Edited by Philip J. Cook, Duke University, Durham, NC, and accepted by Editorial Board Member Kenneth W. Wachter September 21, 2017 (received for review December 3, 2016)

Significance

Waiting period laws that delay the purchase of firearms by a few days reduce gun homicides by roughly 17%. Our results imply that the 17 states (including the District of Columbia) with waiting periods avoid roughly 750 gun homicides per year as a result of this policy. Expanding the waiting period policy to all other US states would prevent an additional 910 gun homicides per year without imposing any restrictions on who can own a gun.

Abstract

Handgun waiting periods are laws that impose a delay between the initiation of a purchase and final acquisition of a firearm. We show that waiting periods, which create a “cooling off” period among buyers, significantly reduce the incidence of gun violence. We estimate the impact of waiting periods on gun deaths, exploiting all changes to state-level policies in the Unites States since 1970. We find that waiting periods reduce gun homicides by roughly 17%. We provide further support for the causal impact of waiting periods on homicides by exploiting a natural experiment resulting from a federal law in 1994 that imposed a temporary waiting period on a subset of states.

More than 33,000 people die in gun-related incidents each year in the United States, accounting for as many deaths as motor vehicle accidents (1). This is concerning both in absolute terms and in comparison to other developed countries, all of which have lower rates of gun violence (2). For example, if the United States could lower its firearm death rate to that of Finland (the high-income country with the second highest rate), roughly 20,000 fewer people would die from guns every year. However, there has been no meaningful reduction in the US firearm-related death rate for more than a decade. Moreover, evidence about which policies would be effective at reducing violence remains limited (3), and the types of bills that are enacted depend on the political party in power (4).

One avenue for reducing gun deaths is to draw on insights from behavioral economics and psychology, which suggest that delaying gun purchases, even for a short time, might be an effective policy tool. Visceral factors, such as anger or suicidal impulses, can spur people to inflict harm on others or themselves, but tend to be transitory states (5, 6). For example, Card and Dahl (7) find that there is a 10% increase in domestic violence following an upset loss of the local National Football League team. Moreover, behaviors triggered by such visceral states can be contrary to longer term self-interest (5, 6).

Delaying a gun purchase could create a “cooling off” period that reduces violence by postponing firearm acquisitions until after a visceral state has passed. Increasing the time it takes to acquire a gun might also close the window of opportunity for would-be perpetrators of violence to use their weapons. Finally, a mandatory delay has the potential to deter purchases among people who have malevolent, but temporary, motivations for owning a firearm.

This article explores the impact of “waiting period” laws on firearm-related homicides and suicides using 45 y of data on law changes and mortality at the state level in the United States. A waiting period is a mandatory delay between the purchase and delivery of a gun; it requires purchasers to wait, typically between 2 and 7 d, before receiving their weapons. We exploit plausibly exogenous temporal and geographic variation in waiting period laws to implement a difference-in-differences approach that identifies the causal impact of waiting periods on homicides and suicides.

We find that waiting periods cause large and statistically significant reductions in homicides. Point estimates using our full 45-y sample and all waiting period changes imply a 17% reduction in gun homicides. We provide further evidence of a causal relationship between waiting periods and lower homicide rates based on a natural experiment in which federal law imposed waiting periods on a subset of states. Estimates from this analysis also suggest that waiting periods reduce gun homicides by 17%. The results of both analyses confirm a large and robust effect of waiting periods on homicides. We also find a negative effect of waiting periods on suicides, but the magnitude and statistical significance of the suicide effect vary across model specification.

Data and Research Design

We construct a panel of every change to waiting period laws in the United States between 1970 and 2014, which we obtained from state statutes and session laws. We combine these changes with annual data on firearm-related deaths from the Centers for Disease Control and Prevention. Fig. 1 shows the number of states with waiting periods over time. Overall, 44 states (including the District of Columbia) have had a waiting period for at least some time between 1970 and 2014. Exploiting the significant geographic and temporal variation in the adoption of waiting periods, we implement a difference-in-differences framework to estimate the causal impact of waiting periods on gun deaths. Essentially, we compare changes in firearm-related deaths within states that adopted waiting periods with changes in firearm-related deaths in other states. We control for changing economic and demographic factors that may be correlated with higher levels of gun violence or with the decision of lawmakers to adopt policies that delay gun purchases.

Fig. 1.
Fig. 1.

States with handgun waiting periods and background checks on dealer sales from 1970 to 2015. Many states were required to implement these policies during the Brady interim period between February 1994 and November 1998 (shaded gray). Following prior research (8), Alabama and Ohio are coded as not requiring background checks after the Supreme Court’s decision in Printz v. United States. Not all states had waiting periods during the Brady interim period because they implemented or already had an instant background check system that obviated the need for a waiting period to investigate gun buyers.

To support our causal interpretation, we then restrict the analysis to the period from 1990 to 1998, during which federal policy forced many states to implement waiting periods. The Brady Handgun Violence Prevention Act (hereinafter “Brady Act”), which went into effect in February 1994, required background checks on handgun purchases from licensed firearm dealers and created a 5-d waiting period to allow sufficient time for the check. Although it was a federal policy, the Brady Act only created new waiting periods for 19 states, since some states already required a background check and waiting period, and some implemented an “instant check” system that allowed for nearly immediate background checks (thereby obviating the need for a waiting period). We provide further details regarding the Brady Act and affected states in Identifying Policy Changes and Materials and Methods.

Results

We begin by examining the effect of waiting periods across the full sample period from 1970 to 2014. The results of Table 1 show that waiting periods are associated with a 17% reduction in gun homicides. This effect is equivalent to ∼36 fewer gun homicides per year for a state with an average number of gun deaths. Waiting periods also lead to a 7–11% reduction in gun suicides (depending on the control variables used in the specification), which is equivalent to 22–35 fewer gun suicides per year for the average state. The results in Table 1 use a log-linear specification; we present models with state-specific trends, models linear in the rate of violence, and Poisson models as part of Tables S3 and S5. The conclusion that waiting periods reduce gun homicides is robust across all specifications. The conclusion regarding suicides is robust to all specifications except those that include state-specific, linear trends (Table S3). Both conclusions are robust across models with and without controls for state-level economic and demographic changes. We also investigate the robustness of the results to the exclusion of individual states in Fig. S1.

View this table:
Table 1.

Effects of handgun waiting periods and background checks on violence, 1970–2014

View this table:
Table S3.

States that implemented background checks and waiting periods during the Brady Act’s interim period from February 1994 through November 1998, according to Ludwig and Cook (8) and this study

View this table:
Table S5.

Effect of handgun waiting periods relative to adoption year, 1977–2013

Fig. S1.
Fig. S1.

Estimates of the effect of waiting periods on gun homicides and suicides, dropping each state individually from the analysis and reestimating model 3 of Table 1. Bars are 1.96 ± SE of the waiting period coefficient. Solid lines mark the full sample estimates, and dashed lines are 1.96 ± full sample SE.

To further support the hypothesis that waiting periods lead to a reduction in gun homicides, we then focus on a natural experiment created by the Brady Act, a federal law that forced some states to adopt new waiting period and background check policies between 1994 and 1998. Ludwig and Cook (8) also use the Brady Act to study whether background checks and waiting periods affect violence. They compare “Brady states” that were subject to the Brady Act with “Brady-exempt states” that were not. However, some states that were classified as Brady states already had waiting periods and background checks before the Brady Act, and other states chose to implement an “instant” background check system instead of requiring a waiting period. As a result, the coding of Brady states in the study by Ludwig and Cook (8) fails to capture all states that had preexisting waiting periods. In contrast, we precisely code which states had waiting periods (before 1994) and which implemented waiting periods only because of the Brady Act. In total, our coding differs from theirs for 16 states. This additional accuracy allows us to assess the causal impact of waiting periods resulting from the Brady Act. The full list of differences between our coding and prior research, along with supporting citations, can be found in Table S4.

View this table:
Table S4.

Effects of handgun waiting periods and background checks on violence, including state-specific trends, 1970–2014

We find that waiting periods led to large and statistically significant reductions in gun violence (Table 2) during the Brady interim period. Specifically, the results of column 3 of Table 2 show that waiting periods implemented during the Brady interim years resulted in a 17% reduction in gun homicides. This is equivalent to roughly 39 fewer homicides per year for the average state. There was also a 6% reduction in gun suicides (i.e., 17 fewer suicides per year for the average state). Both results are robust across models with and without controls for state-level economic and demographic changes. Notably, exploiting the Brady Act as a natural experiment produces similar estimates as the longer sample period from 1970 to 2014.

View this table:
Table 2.

Effects of handgun waiting periods and background checks on violence, 1990–1998

Tables 1 and 2 also show that waiting periods have no significant effect on non-gun homicides, suggesting that people subject to waiting period laws do not substitute other means of committing homicide. This is consistent with other research (9) finding no increase in non-gun homicides in response to policies restricting access to firearms. Results for non-gun suicides, however, are less clear; some specifications suggest partial substitution toward non-gun methods of suicide in response to handgun waiting periods.

Discussion

Our results show that waiting periods reduce gun homicides. Waiting periods for gun purchases are supported not only by the American Medical Association but also by a majority of Americans and a majority of gun owners (10, 11). Our point estimates, based on 45 y of data, suggest that the 17 states (including the District of Columbia) with waiting periods as of 2014 avoid ∼750 gun homicides. Expanding the waiting period policy to states that do not currently have it would prevent an additional 910 gun homicides per year. Waiting periods would therefore reduce gun violence without imposing any restrictions on who can own a gun.

Materials and Methods

Our main specifications are of the form:rit=αi+λt+βWit+γBit+δ'Xit+ϵit,

where rit is the natural logarithm of the rate of violence (homicides or suicides) per 100,000 adult residents, Wit is an indicator for handgun waiting periods and Bit is an indicator for whether background checks are required for dealer handgun sales. We include an indicator variable for background checks on handgun purchases from licensed firearm dealers because a major source of policy variation in our dataset (the Brady Act) also affected background check policies. As seen in Tables 1 and 2, the estimated impact of background checks depends on model specification. We also incorporate time-varying state-level control variables that may influence rates of gun violence (8), Xit, including alcohol consumption, poverty, income, urbanization, black population, and seven age groups. Summary statistics for these variables are included in Tables S1 and S2. The αi and λt parameters represent state and year fixed effects. These fixed effects control for stable, state-specific factors affecting violence and time-varying factors that affect all states identically. It is impossible to control for all time-varying, state-specific factors that affect gun violence. For example, policing tactics, drug use, and environmental factors such as lead exposure might not have changed uniformly across states over time and may also affect violence. However, the consistency between our estimates during the short (Brady interim) period and the longer period (including all waiting period changes since 1970) supports our interpretation of the results. The model parameters are estimated via least squares weighted by state population. We then calculate the percentage effect of waiting periods on violence using the estimator described by Kennedy (12).

View this table:
Table S1.

State-level summary statistics: 1970–2014 (Table 1)

View this table:
Table S2.

State-level summary statistics: 1990–1998 (Table 2)

We code a state as having a waiting period if it imposes any mandatory delay on the purchase of a handgun or has a permitting system for dealer and private sales. (In Table S5, we estimate models with a separate control variable for handgun permit systems and show that the effect of waiting periods is not limited to states with permitting systems.) Currently, 10 states and the District of Columbia impose an explicit waiting period on handgun sales, and an additional five states have permitting systems for private and dealer sales that result in a delay of firearm purchases. Forty-four states have had a handgun waiting period at some point since 1970, although 19 implemented the policy only due to the Brady Act’s interim provisions, in effect from February 1994 to November 1998. These provisions required local law enforcement agencies to conduct background checks on handgun purchases from licensed firearm dealers and required a 5-d waiting period to conduct the check. Some states already required background checks and/or waiting periods before the Brady Act, and were therefore not affected by the new law, but other states were forced to adopt a new waiting period due to the federal policy change. When the permanent provisions of the Brady Act took effect on November 30, 1998, the federal waiting period requirement was replaced with an instant background check system [the National Instant Criminal Background Check System (NICS)]. As a result, many states discarded their waiting periods after 1998 because the NICS eliminated the need for a waiting period to investigate purchasers’ backgrounds. We use the subset of waiting period changes that resulted from the Brady Act as a natural experiment to provide further support for our analysis of the full sample period from 1970 to 2014.

Although nine states have also had a waiting period on long-guns (i.e., rifles and shotguns) sometime since 1970, we focus on handgun waiting periods because handguns account for 70–80% of firearm homicides (13) and because a major source of variation in our data, the Brady Act’s interim period, only affected handgun sales.

Summary Statistics

Tables S1 and S2 provide summary statistics for variables used in the main analyses. Table S1 shows summary statistics for variables used for analyses presented in Table 1, covering the full 1970–2014 sample period. Table S2 shows summary statistics for variables used for the analysis of the Brady interim period in Table 2, covering 1990–1998.

Identifying Policy Changes

In our first set of analyses, covering 1970–2014, we extend prior coding of policy changes by including an additional 36 y of data with 25 changes in waiting period policies. Our approach to identifying changes in waiting period policies also improves on Ludwig and Cook’s (8) classification of states affected by the Brady Handgun Violence Prevention Act. Prior research coded all states subject to the Brady Act’s interim provisions as treatment states, but some of these states already had background checks and/or waiting periods before the interim period. Table S4 details the differences between our coding and that of Ludwig and Cook (8). In total, our coding differs for 16 states; the table footnotes provide supporting citations for each difference. We find that these improvements more accurately measure the effects of waiting periods on homicides, which we now find to be robust and statistically significant at conventional levels, even when we restrict the sample to the same years examined in prior research.

Robustness: State-Specific Trends

If states that do and do not adopt waiting periods have different trends in violence before the implementation of the waiting period, then one might be concerned that our results reflect these different trends rather than the impact of the waiting period policy. To allow for the possibility of differential secular trends, Table S3 estimates a log-linear model with linear trends that vary by state for the 1970–2014 time period [We do not estimate models with state-specific trends for the analysis of the Brady interim period (1990–1998) because there is too little pretreatment data to identify preexisting, state-specific trends in gun violence (14)]. This model produces similar estimates for the effect of waiting periods on homicides, suggesting that differential trends are not the main driver of the results and providing further support for our interpretation. The results for suicides, however, differ across specification and are not robust to the inclusion of control variables and state-specific trends in suicide. The model without trends in column 3 of Table 1 suggests that waiting periods reduce gun suicides by 7%, while the model in column 3 of Table S3 suggests no reduction. The results of Table S3 also suggest that any decrease in gun suicides due to waiting periods is offset by an increase in non-gun suicides.

Robustness: Falsification Exercise and Dynamic Effects

To shed further light on the dynamics of the effects shown in Table 1, Table S6 reestimates the model in column 3 of Table 1, but includes leads and lags of the policy change, specifically including indicator variables for the years before and after implementation of a waiting period. We find that the impact of waiting periods does not appear until the waiting period has been adopted, providing further support for our causal interpretation. Violence appears to fall soon after implementation, although the single-year estimates are imprecise.

View this table:
Table S6.

Estimates of the waiting period effect, controlling for other gun policies

Robustness: Other Changes in Gun Policy

While the results overall point to the causal effect of waiting periods, one might still be concerned that other gun policy changes are correlated with the timing of waiting period changes. To address this concern, we provide evidence that the effects reported in Table 1 are robust to the inclusion of controls for other gun policies in a state. Specifically, in Table S5, we reestimate the models of columns 2 and 3 in Table 1, but include additional variables for handgun permit and concealed carry policies to account for potential correlation between the implementation of these policies and waiting periods. The results in Table S5 show that the inclusion of other gun policies in the model does not change our conclusion that waiting periods reduce gun homicides and suicides. Our study uses a natural experiment embedded in the Brady Act to identify the impact of waiting periods; estimating the causal impact of exogenous changes to other gun policies is beyond the scope of this study. Other research focuses on the impact of handgun permits (15, 16) and concealed carry laws (17⇓⇓–20).

Alternative Model Specifications

Alternative specifications for the effect of waiting periods on homicides and suicides produce similar point estimates (Tables S7 and S8). The estimates in Table S7 are based on models linear in the rate of violence. The results in columns 2 and 3 imply that waiting periods reduce gun homicides by roughly 18% and gun suicides by 5–9% for a state with an average rate of violence. Results for the Poisson model (Table S8) imply reductions of 18–20% and 7–11.6% for gun homicides and suicides, respectively, while estimates based on the log-linear model presented in the main text and Table 1 imply 17% and 7–11% reductions.

View this table:
Table S7.

Alternative specifications for the effect of handgun waiting periods and background checks on violence from 1970 to 2014: Linear rate

View this table:
Table S8.

Alternative specifications for the effect of handgun waiting periods and background checks on violence from 1970 to 2014: Poisson

Additionally, we examine unweighted, least-squares estimates (Tables S9 and S10). The coefficient estimates on the waiting period dummy from the unweighted regressions are attenuated relative to the weighted results. This suggests that the effect of waiting period policies is heterogeneous, with larger states experiencing greater reductions in violence than smaller states (21). To ensure our results are not driven by outlier states, we reestimate the model of gun homicide and suicide rates (column 3 of Table 1), but exclude one state at a time. Fig. S1 shows the 51 resulting coefficients (one from excluding each state and the District of Columbia) for homicides and suicides. The coefficient estimates are consistently negative. As expected from the difference between the weighted and unweighted estimates, large states like Pennsylvania and Florida seem to exert downward pressure on the coefficient.

View this table:
Table S9.

Unweighted estimates of the effects of handgun waiting periods and background checks on violence: Full sample period

View this table:
Table S10.

Unweighted estimates of the effects of handgun waiting periods and background checks on violence: Brady period

Complete Coefficient Estimates

Table S11 presents coefficient estimates for all variables included in model 3 of Table 1. This model uses the same control variables as prior research by Ludwig and Cook (8).

View this table:
Table S11.

Effects of handgun waiting periods on violence, 1970–2014

Footnotes

  • ↵1To whom correspondence should be addressed. Email: mluca{at}hbs.edu.

  • Author contributions: M.L., D.M., and C.P. designed research, performed research, analyzed data, and wrote the paper.

  • The authors declare no conflict of interest.

  • This article is a PNAS Direct Submission. P.J.C. is a guest editor invited by the Editorial Board.

  • See Commentary on page 12097.

  • This article contains supporting information online at www.pnas.org/lookup/suppl/doi:10.1073/pnas.1619896114/-/DCSupplemental.

This is an open access article distributed under the PNAS license.

References

  1. ↵
    1. National Center for Health Statistics, Centers for Disease Control and Prevention
    (2015) About Compressed Mortality, 1999-2014. CDC WONDER Online Database. Available at wonder.cdc.gov/cmf-icd10.html. Accessed August 5, 2016.
    .
  2. ↵
    1. Grinshteyn E,
    2. Hemenway D
    (2016) Violent death rates: The US compared with other high-income OECD countries, 2010. Am J Med 129:266–273.
    .
    OpenUrlCrossRefPubMed
  3. ↵
    1. Sacks CA
    (2015) In memory of Daniel–Reviving research to prevent gun violence. N Engl J Med 372:800–801.
    .
    OpenUrl
  4. ↵
    1. Luca M,
    2. Malhotra D,
    3. Poliquin C
    (2017) The impact of mass shootings on gun policy. Harvard Business School NOM Unit Working Paper No. 16-126. Available at dx.doi.org/10.2139/ssrn.2776657. Accessed October 1, 2016.
    .
  5. ↵
    1. Loewenstein G
    (1996) Out of control: Visceral influences on behavior. Organ Behav Hum Decis Process 65:272–292.
    .
    OpenUrlCrossRef
  6. ↵
    1. Loewenstein G,
    2. Lerner JS
    (2002) The role of affect in decision making. Handbook of Affective Sciences, eds Davidson RJ, Scherer KR, Goldsmith HH (Oxford Univ Press, Oxford), pp 619–642.
    .
  7. ↵
    1. Card D,
    2. Dahl GB
    (2011) Family violence and football: The effect of unexpected emotional cues on violent behavior. Q J Econ 126:103–143.
    .
    OpenUrlCrossRefPubMed
  8. ↵
    1. Ludwig J,
    2. Cook PJ
    (2000) Homicide and suicide rates associated with implementation of the Brady Handgun Violence Prevention Act. JAMA 284:585–591.
    .
    OpenUrlCrossRefPubMed
  9. ↵
    1. Raissian KM
    (2016) Hold your fire: Did the 1996 Federal Gun Control Act expansion reduce domestic homicides? J Policy Anal Manage 35:67–93.
    .
    OpenUrl
  10. ↵
    1. American Medical Association
    (2016) AMA Expands Policy on Background Checks, Waiting Periods for Gun Buyers. Available at https://perma.cc/CNE4-FEQ9. Accessed October 28, 2016.
    .
  11. ↵
    1. Sides J
    (December 23, 2012) Gun owners vs. the NRA: What the polling shows. Washington Post, Wonkblog. Available at https://perma.cc/HCC9-4DY5. Accessed October 28, 2016.
    .
  12. ↵
    1. Kennedy P
    (1981) Estimation with correctly interpreted dummy variables in semilogarithmic equations. Am Econ Rev 71:801.
    .
    OpenUrl
  13. ↵
    1. Planty M,
    2. Truman J
    (2013) Firearm Violence, 1993-2011 (US Department of Justice, Washington, DC), NCJ 241730. Available at https://www.bjs.gov/index.cfm?iid=4616&ty=pbdetail. Accessed October 18, 2016.
    .
  14. ↵
    1. Wolfers J
    (2006) Did unilateral divorce laws raise divorce rates? A reconciliation and new results. Am Econ Rev 96:1802–1820.
    .
    OpenUrl
  15. ↵
    1. Webster D,
    2. Crifasi CK,
    3. Vernick JS
    (2014) Effects of the repeal of Missouri’s handgun purchaser licensing law on homicides. J Urban Health 91:293–302.
    .
    OpenUrlCrossRefPubMed
  16. ↵
    1. Rudolph KE,
    2. Stuart EA,
    3. Vernick JS,
    4. Webster DW
    (2015) Association between Connecticut’s permit-to-purchase handgun law and homicides. Am J Public Health 105:e49–e54.
    .
    OpenUrl
  17. ↵
    1. Lott JR Jr,
    2. Mustard DB
    (1997) Crime, deterrence, and right-to-carry concealed handguns. J Legal Stud 26:1–68.
    .
    OpenUrlCrossRef
  18. ↵
    1. Ludwig J
    (1998) Concealed-gun-carrying laws and violent crime: Evidence from state panel data. Int Rev Law Econ 18:239–254.
    .
    OpenUrlCrossRef
  19. ↵
    1. Ayres I,
    2. Donohue JJ III
    (2002) Shooting down the ‘more guns, less crime’ hypothesis. Stanford Law Rev 55:1193–1312.
    .
    OpenUrl
  20. ↵
    1. Manski CF,
    2. Pepper JV
    (2017) How do right-to-carry laws affect crime rates? Coping with ambiguity using bounded-variation assumptions. Rev Econ Stat doi:10.1162/REST_a_00689.
    .
    OpenUrlCrossRef
  21. ↵
    1. Solon G,
    2. Haider SJ,
    3. Wooldridge JM
    (2015) What are we weighting for? J Hum Resour 50:301–316.
    .
    OpenUrlCrossRef
  22. Federal Register 59 (1994). Available at https://www.gpo.gov/fdsys/pkg/FR-1994-07-22/html/94-17819.htm. Accessed June 29, 2016.
    .
    1. Manson DA,
    2. Gilliard DK,
    3. Lauver G
    (1999) Presale Handgun Checks, the Brady Interim Period, 1994-98 (US Department of Justice Bureau of Justice Statistics Bulletin, Washington, DC), NCJ 175034. Available at https://www.bjs.gov/content/pub/pdf/phc98.pdf. Accessed June 29, 2016.
    .
    1. Vernick J,
    2. Hepburn L
    (2003) State and federal gun laws. Evaluating Gun Policy: Effects on Crime and Violence, eds Ludwig J, Cook PJ (The Brookings Institution, Washington, DC), pp 345–402.
    .
    1. U.S. Department of Justice Bureau of Justice Statistics
    (1996) Survey of State Procedures Related to Firearm Sales (US Department of Justice Bureau of Justice Statistics Bulletin, Washington, DC), NCJ 160763. Available at https://www.bjs.gov/index.cfm?ty=pbdetail&iid=1067. Accessed August 2, 2014.
    .
    1. Carroll CA Jr
    (January 27, 1994) South Carolina Executive order no. 94-03. Available at hdl.handle.net/10827/1350. Accessed June 14, 2017.
    .
View Abstract
Back to top
Article Alerts
Email Article
Citation Tools
Request Permissions
Handgun waiting periods reduce gun deaths
Michael Luca, Deepak Malhotra, Christopher Poliquin
Proceedings of the National Academy of Sciences Nov 2017, 114 (46) 12162-12165; DOI: 10.1073/pnas.1619896114
del.icio.us logo Digg logo Reddit logo Twitter logo CiteULike logo Facebook logo Google logo Mendeley logo

You May Also be Interested in

PNAS Profile with NAS member and mathematician Yuval Peres
PNAS Profile
PNAS Profile with NAS member and mathematician Yuval Peres
Researchers report evidence in yeast cells that nucleosomes inhibit binding and cleavage by the genome-editing enzyme CRISPR-Cas9, suggesting nucleosome position maps might help improve genome-editing efficiency. Image courtesy of Janet Iwasa (University of Utah, Salt Lake City).
DNA architecture influences genome editing efficiency
Researchers report evidence in yeast cells that nucleosomes inhibit binding and cleavage by the genome-editing enzyme CRISPR-Cas9, suggesting nucleosome position maps might help improve genome-editing efficiency.
Image courtesy of Janet Iwasa (University of Utah, Salt Lake City).
A study exploring intergenerational social mobility in the United States finds that fewer people born in the 1980s were upwardly mobile than those born in the 1940s and that the slowing of status mobility accentuates inequalities of opportunity. Image courtesy of Pixabay/Ponciano.
Intergenerational trends in status mobility
A study exploring intergenerational social mobility in the United States finds that fewer people born in the 1980s were upwardly mobile than those born in the 1940s and that the slowing of status mobility accentuates inequalities of opportunity.
Image courtesy of Pixabay/Ponciano.
A study suggests that social learning from exposure to opposing political views on social networks can improve accuracy and remove partisan bias, but displaying political symbols during cross-party communication can prevent such learning, according to the authors.
Social networks and interpretation of climate data
A study suggests that social learning from exposure to opposing political views on social networks can improve accuracy and remove partisan bias, but displaying political symbols during cross-party communication can prevent such learning, according to the authors.
Proceedings of the National Academy of Sciences: 115 (38)
Current Issue

Submit

Jump to section