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THE EFFECT OF THE 18-YEAR OLD DRINKING AGE
ON AUTO ACCIDENTS*
by
Stephen Cucchiaro
Joseph Ferreira, Jr.
Alan Sicherman
OR 034-74
May, 1974
Massachusetts Institute of Technology
Operations Research Center
and
Laboratory of Architecture and Planning
Cambridge, Mass.
* This research was supported in part by NSF Grant GI 38004,
by the MIT Undergraduate Research Opportunities Program, and
by the U. S. Army Research Office (Durham) under Contract
No. DA HC04-73-C-0032.
The Effect of the 18-Year Old
Drinking Age on Auto Accidents
by
S. Cucchiaro, J. Ferreira, and A. Sicherman
M.I.T., Cambridge, Mass.
Abstract
The effect of Massachusetts' reduced drinking age on auto accidents is examined by employing an interrupted time series analysis
of monthly accident data covering the period January, 1969, through
September 1973. The data were stratified by driver age, accident type
and (to a limited extent) operating-after-drinking.
These raw data
were adjusted using monthly mileage and seasonal indices and, where possible, a control group not affected by the drinking law. Correlograms
of the adjusted series were computed to check for remaining systematic
bias.
Finally, the average accident rates for the adjusted, well-be-
haved series before and after the March 1973 change were compared using
standard t-tests.
Accident rates among 18-20 year olds did increase significantly-about 40% for involvement in fatalities.
Nevertheless, the results
are consistent with the hypothesis that, as a result of the reduced
drinking age, 18-20 year old driving-after-drinking behavior has become
comparable to that of older drivers.
-ii-
The Effect of the 18-Year Old Drinking Age on Auto Accidents
Table of Contents
PAGE
List of Tables
iii
List of Figures
iv
ACKNOWLEDGEMENT
v
1. BACKGROUND
1
2. HYPOTHESES AND AVAILABLE DATA
3
3. THE'ANALYSIS
10
4. THE RESULTS
17
5. SUMMARY AND CONCLUSIONS
26
6. FUTURE RESEARCH
31
Bibliography
32
Appendix I -- THE TIME SERIES
Part A:
Part B:
Part C:
The Interrupted Time Series Design
Miscellaneous Factors That May Influence
the Accident Data
Corrections for Mileage, Seasonality and No-Fault
A-1
A-1
A-2
A-4
Appendix II -- INTERPRETING THE TIME SERIES
Part A: Correlation and Interruptions
Part B: The Adjusted Well-behaved Time Series
A-9
A-9
A-10
Appendix III -- DATA DIFFICULTIES AND FUTURE RESEARCH
A-18
-iii-
List of Tables
PAGE
1. The Time Series Used in the Analysis
2. The Results -- Before and After Averages
A-1
Estimated Monthly Gasoline Consumption
A-2 Operators and Accident Involvements by Age Groups
6
18
A-5
A-8
-iv-
List of Figures
PAGE
1. Raw Data for Selected Time Series (Part 1)
7
2. Raw Data for Selected Time Series (Part 2)
8
3. Raw Data for Selected Time Series (Part 3)
9
4. Series D-Tl Before and After Adjustments
12
5. Series A2-T1 Before and After Adjustments
13
6. Series A4-T1 Before and After Adjustments
14
7. Average Monthly Rates Before and After Change (Part 1)
19
8. Average Monthly Rates Before and After Change (Part 2)
20
9. Average Monthly Rates Before and After Change (Part 3)
21
A-1
Example of Time Series
A-2
Sample Correlograms for Simulated Data
A-1
A-14
A-3 Sample Correlograms for Selected Series (Part 1)
A-15
A-4 Sample Correlograms for Selected Series (Part 2)
A-16
A-5
A-17
s
Sample Correlograms for Selected Series (Part 3)
-V-
ACKNOWLEDGEMENT
Support for this research has come from several sources. The work
began during the summer of 1973 as an undergraduate research opportunities
project (UROP) for Stephen Cucchiaro (then a senior inmathematics) under
the supervision of Prof. Joseph Ferreira of the M.I.1. Department of Urban
Studies and Planning. The initial work was supported by the UROP office
and NSF Grant G138004 for "Innovative Resource Planning inUrban Public
Safety Systems" at the M.I.T. Operations Research Center and the Laboratory of Architecture and Planning. Alan Sicherman, a graduate student
inOperations Research, joined the group in the fall of 1973 and was
supported by Army Research Office under Contract No. DA HC04-73-C-0032.
We would also like to thank a number of individuals at the Massachusetts Registry of Motor Vehicles for interesting us in the question and
providing us with the raw data and related statistical information.
In
particular, we appreciate the cooperation of James Velis, Assistant to
the Registrar, Fred Cody, Administrative Assistant to the Registrar,
and Evelyn Trefrey of the Registry's Statistical Bureau.
THE EFFECT OF THE 18-YEAR OLD DRINKING AGE ON AUTO ACCIDENTS
1. BACKGROUND
On March 1, 1973, Massachusetts put into effect a law which lowers the
drinking age limit from 21 to 18 years of age.
There has been considerable
concern and discussion in the state legislature, in the Registry of Motor
Vehicles, and in the press over the extent to which io",-ring the drinking
age has caused an increase in motor vehicle accidents.
Preliminary com-
parison of raw data for the few months before and after the March 1 change
have produced much-quoted statistics such as a "131% rise in road deaths
linked to teenagers and liquor."*
Though the increase is dramatic, these data are not adjusted for road
use condition or for other factors that might have changed during the months
involved. Also, the actual number of drinking related fatalities involving
young operators are subject to large statistical fluctuations since they
are small compared with the total number of highway fatalities and the total
number of teenager-involved accidents during those months.**
A more thorough
analysis of the data is needed to determine the extent to which the continuation
past trends, fluctuations due to chance factors and other such considerations
account for portions of the changes observed in the raw data.
This paper studies in more detail several kinds of accident data
and attempts to develop a broader and more reliable picture of how and to
what extent reducing the drinking age has affected teenage driving and
highway accidents.
*
The analysis uses monthly property, injury and fatal
See, for example, Boston Herald American,i2/26/73, p. 3.
** A Boston Herald American article on February 1, 1974, indicated that
persons fatally injured as a result of accidents involving drinking drivers
between 18 and 20 years of age totaled 79 between March 1, 1973 and January
24, 1974, and 35 during the corresponding period of 1972-73.
-2-
accident data for Massachusetts for the period January, 1969, through
September, 1973. Several standard statistical techniques for examining
times series data are used to test various hypotheses.
Lack of access to finer breakdowns of the data and to data
beyond September 1973 limited the scope of the study. However, the
advent of the energy crisis inthe fall of 1973 would reduce the usefulness of the data beyond October, 1973. The data were sufficient
to provide estimates of the law's effect on several accident rates.
Fatal accident rates showed the largest increase -- up approximately
40% for the 18-20-year-old group. The findings support the general
conclusion that, as a result of the law, the 18-20-year-old drivingafter-drinking frequency is now comparable to that of older drivers.
-3-
2. HYPOTHESES AND AVAILABLE DATA
A variey of hypotheses concerning the effects of the new Massachusetts
drinking law are possible.
One is that there has indeed been a sharp increase
in the accident rate for 18 to 20 year olds as a result of the lower drinking age limit.. Another is that motorists under 18 havc experienced an increase in accidents since they can now obtain liquor more easily by themselves through their 18 to 20 year old friends.
Motorists between 21 and
23 might also experience an increase since younger 18 to 20 year old friends
with whom they associate will want to spend more time drinking.
A more complicated type of hypothesis might be that there was a transient increase in the accident rate immediately after the March 1 change
but, after a few months, the rate dropped to a lower, long-term level.
Yet
another theory is that an increased accident rate after March 1, 1973 reflects a continuation of a trend that had been in progress prior to the
inactment of the new drinking law. Still another suggests that the number
of citations issued to 18 to 20 year olds for alcohol-related violations has
increased due to a more stringent police attitude in response to the enactment of the relaxed Massachusetts drinking law.
Further complications arise if differential "types" of 18 to 20 year
olds (e.g., females, just received licenses, etc.) have experienced different
changes in accident rates. Also, different geographic areas (e.g., urban,
near state border, etc.) may have experienced different effects.
The rates
for different types of accidents (e.g., fatal, property damage only, single
car accidents, etc.) might change in different ways.
In order to test these hypotheses, much more data is needed besides
before and after figures for accidents involving drinking operators aged 18
to 20.
Certain data are needed to control for mileage driven, seasonality,
-4-
past trends and the like.
Then quarterly or monthly accident data broken
down by age of operator, related citations, and accident severity are needed
to test the basic hypotheses.
The Massachusetts Registry of Motor Vehicles provided us with certain
monthly data for the January 1969 through September
973 period.* The fol-
lowing types of information were available on a monthly basis:
(1) The number of citations** issued for "operating under the
influence," and "operating atter drinking" violations.
(2) The number of reported accidents classified as fatal, nonfatal, or property damage types.
(3) Driver age breakdowns for the above data.
(4) Breakdowns of (2) indicating whether "operating under the
influence" or "operating after drinking" citations were
issued.
(5) Estimates of the number of miles driven in Massachusetts.
Data beyond September were not available and, unfortunately, we could not
obtain the accident data broken down both by age and drinking citations.
The fatal, non-fatal, and property damage only breakdowns enable
differential changes in accident rates related to accident severity to be
identified.
The age breakdowns permit focusing on specific age groups.
They are also helpful in controlling for other factors that might influence
the number of alcohol related accidents since changes in the monthly number
of accidents involving operators over 25 are not likely to be related to
changes in the drinking law.
* These data were provided by the Accident Records Section of the Mass.
Registry of Motor Vehicles.
** Operating after drinking and operating under the influence "violations"
appearing in these Registry statistics refer to information on reports for
investigated accidents. The investigator cites an involved operator for
"driving under the influence" if he determines that the operator's blood
alcohol content was at least 0.1%. Driving after drinking is indicated if the
operator admits drinking or has a blood alcohol content less than 0.1%.
-5-
The drinking citation data provide the only available Registry indicators of
the number of accidents related to liquor consumption.
However, such citation
data may be misleading to the extent that the March 1 change altered the circumstances under which police issued drinking citations to youths.
Eighteen time series could be developed using te cour age groups or
the two citation categories together with the three accident types.
Table 1
identifies these 18 time series plus an additional series (A4-T1) for all
monthly fatalities involving operators of all ages.
The numbers and abbre-
viations for these time series given in Table 1 will be used throughout the
report.
Figures 1, 2 and 3 graph the unadjusted monthly data for several of
these series.
-6-
Table 1. The Time Series Used in the Analysis
Driver and Accident Categories
OPERATOR INVOLVED**
ACCIDENT TYPE
*Dl:
Received an "Operating after
Drinking" Citation
*D2:
Received an "Operating under
the Influence" Citation
Al:
Under 18 years of age
A2:
18 to 20 years of age
A3:
21 to 23 years of age
A4:
over 23 years of age
AA:
All ages combined
T1:
Involved a Fatality
T2:
Involved only nonfatal personal injury
T3:
Involved property
damage only
Time Series Labels
1)
2)
3)
4)
5)
6)
DI-TI
D2-T1
D1-T2
D2-T2
D1-T3
D2-T3
19) AA-Tl:
7)
8)
9)
10)
11)
12)
Al-Tl
A2-T1
A3-T1
A4-T1
A1-T2
A2-T2
13)
14)
15)
16)
17)
18)
Total number of deaths resulting from auto accidents.
* Includes drivers of all ages
** Multiple car accidents will appear in more than one category
A3-T2
A4-T2
A1-T3
A2-T3
A3-T3
A4-T3
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The behavior of the eighteen sets of monthly accident and citation data
will be interpreted as interrupted times series.* After adjusting the series
to remove suspected, systematic biases, we will identify those series which
appear to have significantly different average accident rates before and
after March, 1973.
Finally, various hypotheses about the law's effects will
be checked for consistency with the data and a theory of what has happened
will be developed.
Several standard statistical techniques** are used to adjust the data
for miscellaneous factors to correct for trends, and to identify those adjusted time series for which the policy change appears to be associated with
significantly different behavior,
Two methods were used to attempt to factor
out the influence on the accident rate of changes in miscellaneous factors
unrelated to the new drinking law such as the amount of driving, and
seasonal trends.
Both methods are described in detail in Appendix II.
Onemethod scaled the monthly data using estimates of monthly mileage,
seasonal trends and other such factors.
The second method regarded the over
23 year old drivers as a control group whose accident data could be used to
standardize the 16 to 23 year old experience.
Assuming that miscellaneous
factors affected all age groups similarly, any significant difference in the
ratio of the monthly accident experience for the over 23 group and each of the
other groups could be attributed to the changed drinking law.
* Appendix I briefly reviews the use of an interrupted time series design,
** The techniques are similar to those used elsewhere in studying highway
accident data, See for example the work of Glass and Campbell on the effect
of Connecticut's speed limit enforcement [1,4].
-11-
All eighteen series were adjusted using method one. Method two was used
only for series 7, #8and #9. (See discussion inAppendix II.)
Figures 4,
5 and 6 compare three series before and after adjustments. The adjusted
figures are scaled to represent the equivalent accident rate for each standardized month per 2.3 billion motor vehicle miles (the 1969-1973 average
mileage per month).
Thus, the 9 reported fatal accidents involving "after
drinking" citations during April of 1969 correspond to a seasonally adjusted
rate of 10.7 per 2.3 billion motor vehicle miles, Similarly, the 9 such accidents during August of 1970 correspond to 8 after the method I adjustments.
The adjustments account for some but certainly not all of the monthly
fluctuations in the accident rates.*
Nevertheless, the remaining "noise" is
easily handled if it represents random fluctuations around average before and
after accident rates.
Ideally, the mileage and seasonality adjustments or
the use of the over 23 control group account for all systematic biases inthe
series except for the March 1973 change.
For series such as D-T1, the only
sharp or systematic change in the adjusted series appears to have occured in
March 1973.
For others, such as A3-T1, no trends are obvious and itis not
clear whether there isa March 1973 interruption.
For the A4-T2 series,
interruptions at other times appear more important,
To help identify those "well behaved," adjusted series which appear to
exhibit trends or interruptions inMarch 1973 (or not all all), we examined
the correlograms of the adjusted time series. As explained inAppendix II,
the correlogram of a particular series measures the extent to which accident
rates Kmonths apart are correlated, Correlograms of a few series (for the
period before the March 1973 change) are shown in the Appendix for K values
* For example, the mean number of monthly citations for the D1-T1 series
was 802, The standard deviations before and after mileage and seasonality
corrections were 3,08 and 2,53,
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-15-
between 1 and 50.
A series exhibiting linear growth with no noise would
A stable series with uncorrelated,
produce a linearly increasing correlogram.
random noise would produce a stable correlogram that fluctuated randomly
around 0.
As expected, series A4-T2 in Figure 6 above produced a poorly behaved
correlogram.
Both series D-Tl (#1) and A2-Tl (#8) were judged well-behaved.
a discussion of the
In all, nine series were acceptable (see Appendix Ii fr
criteria used to make these judgements).
Of those adjusted using method I,
#1, #3, #5, #8, #9, #10 and #19 were accepted.
Of those adjusted using the
over 23 experience, #8 and #9 were accepted,
In summary, these nine series--after adjustments and controls to remove
certain systematic biases--appear to fluctuate randomly about a stable level
for the months prior to March 1973.
To the extent that this is the case,
the hypotheses suggested in section 2 can be tested by comparing the average
accident rates before March 1973 with the experience after that date.*
Table 2 and figures 7, 8 and 9 present the results.
For each of the
eight series, averages for the adjusted numbers of accidents per month were
computed for four time periods:
Period
Period
Period
Period
A:
B:
C:
D:
January
August
March
April
1969
1972
1973
1973
through
through
through
through
February
February
September
September
1973
1973
1973
1973
* Conceivably more complicated adjustments and statistical techniques
could be used to interpret some of the remaining 10 series. However, we
felt that the short time period following the change, the uncertainty about
alternative adjustments and the level of unexplained noise in the data limited
the practicality of more detailed analysis.
I_
__
1--1·1111- .··1·^11·111^11-·-----Y-l--__-----1
-16-
Considering Periods B and D separately permits possible time varying effects
to be identified.
If the average accident rate for Period B were signifi-
cantly different from the average during Period A, then a trend which began
before passage of the law might account for any Period A to C change.
Periods C and D are distinguished to enable identification of any transient
effect of the law during March 1973.
(With only seven months of data
following the change itwas not possible to investigate longer transient
effects.)
Since all nine adjusted series vary substantially from month to month
throughout the 5 years, small changes in the before and after average accident rates do not necessarily suggest a March 1973 interruption inthe
series.
To establish a criterion for determining the smallest change that
should be considered significant, we employed standard t-tests for the
difference between two means. The usual assumptions about the normality,
independence and stationarity of the "noise" inthe series were made and 95%
confidence intervals were used for each of the eight series. Appendix II
explains the assumptions and the technique.
-17-
4. THE RESULTS
The results for all nine time series are summarized in Table 2 and
graphed in Figures 7, 8, and 9. The letter beside each bar indicates the
time period for which the average accident rate was calculated.
The dotted
vertical lines are related to the tests for significant differences before
and after March 1973.
For each series, the dotted line indicates the
lowest possible period C averages that would still be udged significantly higher than the period A average accident rate.
Similar lines might be
drawn to compare means for other combinations (A-D, B-C, B-D, and A-B).
However, B-C and B-D comparisions are based on too little data (6or 7 months
each) to have narrow confidence intervals and are not used. Corresponding
lines for A-D and A-B comparisions are not sufficiently different to warrant
separate lines on the graphs (Appendix IIdiscusses the differences inmore
detail).
The bar graphs in Figures 7,8 and 9 indicate the average number of
operators (or deaths inone instance) involved inparticular types of accidents during each month. The magnitude of the bars are scaled so that they
correspond to the average number of operators (or deaths) for a deseasonalized month per 2.3 billion motor vehicle miles (the January 1969 through
February 1973 average).
For example, the Figure 7 result for fatal accidents
involving operators over 23 years old has a magnitude of 59.8 during period
A. Thus an "average" month between January 1969 and February 1973 had 59.8
such operators involved infatal accidents. Similarly, an average of 13.7
operators aged 18-20 were involved infatal accidents during each month of
period A.
* Period
Period
Period
Period
_^Y
i-I _11
I
A includes
B includes
C includes
D includes
L
January
August
March
April
1969
1969
1973
1973
-- --1YLIIL-II--IC_-
through
through
through
through
February
February
September
September
1973
1973
1973
1973
-18-
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-19Figure 7. Average Monthly Rates Before and After Change (Part I)
Operators involved/standard month
O
80c
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in fatal accidents*
it
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M
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g.
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e
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Operators of all ages involved
in non-fatal injury accidents
and cited for driving-afterdrinking*
5.15
A
D1 - T3
Cd
_
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Operators of all ages involved
in property damage accidents
and cited for driving-afterdrinking*
B
D
t
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*The standard monthly averages are computed from the monthly figures adjusted for
mileage and seasonality and are saled to indicate the rate per 2.3 billion miles
(the monthly average).
**Period
Period
Period
Period
A: January 1969 through February 1973
B: August 1969 thrbugh February 1973
C: March 1973 through September 1973
D: April1 1973 through September 1973
---Period C averages-extending to the right of the dotted line are considered significantly different from.the period A average. (Within the accuracy of the graphs,
the same is approximately true for A-B and A-D comparisons.)
-20Figure 8. Average Monthly Rates Before and After Change (Part 2)
Operators Involved/standard month
I,
i
i
0
,! I A
i
A
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s .
I 10
jT
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D1 - T1
Operators of all ages involved
in fatal accidents and cited
for drinking-after-driving*
B
C
I~~~ -
M
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5.29
A
A2 - TI
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.
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18-20 year olds involved in
fatal accidents*
I
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I
6.09
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c
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A
B
-__~~~~~~~~~~~~
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18-20 year olds involved in
fatal accidents***
(using control group)
I
C
D
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S
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I
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20
*The standard monthly averages are computed from the monthly figures adjusted for
mileage and seasonality and are scaled to indicate the rate per 2.3 billion miles
(the monthly average).
**Perlod A:
Period :
Period C:
Period D:
January 1969 through February 1973
August 1969 through February 1973
March 1973 through September 1973
Aprf1 1973 through September 1973
***The standard monthly average Is computed from the monthly ratios of the 18-20 year
old experience to the over 23 year old experience multiplied by (1/5.75) so that
the period A average matches that obtained in series A2-T1.
---Period C.averagse.extending to the right of the dotted line are considered significantly different from the period A average. (Within the accuracy of the graphs,
the same is approximately true for A-B and A-P comparisons.)
-21-
Figure 9. Average Monthly Rates Before and After Change (Part 3)
Operators involved/standard month
C
Srcl
?u.
A
B _______
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21-23 involved in fatal
accidents*
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21-23 involved in fatal
accidents**
(using control group)
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All fatalities
all ages*
I
*The standard monthly averages are computed from the monthly figures adjusted for
mileage and seasonality and are scaled to indicate the rate per 2.3 billion
miles (the monthly average).
**The standard monthly average is computed from the monthly ratios of the 18-20 year
old experience to the over 23 year old experience multiplied by (1/5.75) so that
the period A average matches that obtained in series A3-T1.
---Period C averages extending to the right of the dotted line are considered significantly different from the period A average. (Within the accuracy of the graphs,
the same Is approximately true for A-B and A-D comparisons.)
-22-
For the bar graphs corresponding to series adjusted using the control
group, the interpretation is slightly different.
The number of over 23 year
old operators involved infatal accidents in each month isused as the standard of comparision.
The bars represent the average over each period of the
ratio of the 18-20 year-old experience to the over 22 y:ar-old experience.
The length of the bars are scaled so that the value during period A matches
the period A mean obtained using method I adjustments
series #8 or #9).
The sizable monthly fluctuations that remain in the adjusted time series
limit our ability to determine whether changes in the A to C or A to D averages
are due to the March 1973 change or to random fluctuations inmonthly figures.
Thus, for the 18-20 fatalities of series #8,changes of less than 3 involvements in fatalities per month between periods A and C would not be judged significant (using the t-test described inAppendix IIat the 95% confidence level) even
though a change of 3 would amount to 22% of the period A monthly average.
Similarly, for the over-23 fatality figures, changes of less than 9 operator
involvements per month (inthe period A to period C averages) would not be
judged significant.
Despite these large noise levels a number of significant
differences were found.
Depending upon which averages are compared, the estimated magnitude of
the changes can differ. For series #1 the estimates vary between 37%
(comparing period B to period D) and 75% (comparing period A to period C).
We shall use changes in the period A to period C averages as our (point)
estimate of the changes inthose series judged to be "interrupted."
These
changes are thought to be the best (point) estimates of the effects of law.
The period B averages were based on the 7 months just preceeding the enactment of the law and are subject to large standard errors.
However, the
period A averages are based on several years data after corrections for
seasonality and trends and are not substantially different from the period B
-23-
averages. Period C figures are used for post March 1973 estimates since
so few months data were available after the change and period C and D estimates were not significantly different. Series #1 estimates are most sensitive to the choice--a fact that may be due to changed enforcement levels for
issuing driving after drinking violations. Such possib 4lities will be discussed later.
Results for each series are discussed separately in .he remainder of this
section. General conclusions and interpretations are developed in section 5.
Series #1:
Operating after drinking fatalities
Period C and D averages were significantly different from those
during period A. The estimated 75% increase from 8.03 to 14.03 cases per
month corresponds to 6 more operators per (standardized) month involved in
fatal accidents when cited for driving after drinking.
Inmore graphic
terms, the relationship between the number of operators involved in fatal
accidents and the number of deaths during the years 1967-1972 has been close
to 6/5.t1
5]
For the series #1estimates this amounts to 5 more deaths per
month associated with "driving-after-drinking" accidents.
Series #3:
Operating after drinking injuries
No significant increase was noted. Some studies have shown that alcohol is less of a factor inproperty damage and non-fatal injury accidents[ll ]
and this may account for the different results for series #1and #2. Other
possibilities are changes in the enforcement of driving after drinking restrictions and the fact that period A to period C changes would have to exceed
13 (about 20%) before being judged significant.
-24-
Series #5:
Operating after drinking involvements--property damage only
Here a significant increase of 24.5% is found. The change is much less
than for fatal accidents involving drinking--consistent with the theory
mentioned above.
It corresponds to an increase of about 8 in the number of
operators involved in property-damage-only accidents an,' cited for driving
after drinking.
Series #8:
Fatal accidents involving 18-20 year olds
A significant increase of about 38.8% is noted. This amounts to 5.3
more operator involvements per month and is very close to the difference
observed in series #1. Such a match suggests that 18-20 year old operators
account for the increase in drinking-related fatalities.
Series #9:
Fatal accidents involving 21-23 year olds
No significant increase is observed suggesting that this age group was
not affected by the law.
The 1% increase was far from the 25% increase
needed in order for the change to be judged significantly above the noise
level.
Series #10:
Fatal accidents involving operators over 23
As expected, no significant change is observed.
The 6% drop is well
within the normal range of fluctuations.
Series #20:
18-20 year old fatalities--using the control group
A significant increase is noted.
tional operator involvements per month.
The 44.8% change amounts to 6 addiThese figures closely match the
series #8 figures for 18-20 year old operators involved in fatalities when
adjustments were based on seasonality and miles driven.
-25-
Series #21:
21-23 year old fatalities--using the control group
No significant increase is observed reconfirming the results for the
21-23 year olds using mileage and seasonality considerations.
It should be
noted that the figures using the control group are numerically close to
their counterparts using mileage and seasonality.
The
oncurrence strengthens
the argument that changes are due to the law and not to extraneous factors
not considered in the analysis.
Series #19:
All auto accident-related fatalities
No significant change is observed.
However, increases less than 10%
per month could not be distinguishable from noise in the data.
The impact
on the total number of deaths of the increase in the number of 18-20 year
olds involved in fatalities is not great enough to be distinguished from the
impact that random or unknown factors have upon the total number of deaths.
This is to be expected since the 18-20 year old group account for only about
15% of the total number of operators involved in fatalities.
Even a fairly
large change in this group may not substantially affect the total mean.
-26-
5. Summary and Conclusions
Of the eighteen sets of 57-month time series, only the seven series
involving fatalities or driving-after-drinking violations were sufficiently
well behaved to be used in the analysis.
The non-fatal and property-damage
data were distorted -- apparently due to changes ir arcident reporting
under the no-fault insurance law.
The driving-under-the-influence and
under-18-year-old-fatality data were subject to large monthly fluctuations
because of the small monthly totals involved and their correlograms were
unacceptable.
The correlograms for the driving under the influence citations
were rejected because they exhibited marked 12 month periodicity even after
the standard seasonality connections.*
The results for the seven usable series support the hypothesis that
reducing the drinking age resulted in an increase in drinking related
accidents among 18-20 year old drivers.
Among these usable series, the two
which did not Include the experience of 18-20 year old operators did not
appear to experience interruptions in March of 1973.
Fatal accidents in-
volvlng 21-23 year olds (series A3-T1) and operators over 23 (series A4-T1)
were apparently unaffected by the law, but those for 18-20 year olds
(series A2-T1) jumped 40%.
Two of the three series concerning accidents involving operating after
drinking citations increased significantly -- 75% and 24% respectively for
driving-after-drinking fatalities and property-damage-only accidents.
These results indicate a substantial March 1973 change in the frequency of
drinking related accidents (and, possibly, in the circumstances whereby
*Evidently seasonality adjustments for accident occurrence do not correspond
to those for accidents involving driving-under-the influence citations. We
did not have enough data to permit meaningful adjustments to correct for
this periodicity.
-27-
drinking citations are Issued).
Since the increase in reported operating-
after-drinking fatalities (75% corresponds to 6 more per month) matched the
numerical increase in 18-20 year old involvement in fatal accidents (40
corres>o2nds to 5.3 more per month), and since no older age groups experienced an increased rate of involvement in fatalities,
ne concludes that
there was a significant increase in the frequency of drinking-related
accidents among 18-20 year olds.
Judging from the results for the operating-after-drinking series, the
increase in accident rates among 18-20 year olds more most pronounced for
fatal accidents.
Precise figures for non-fatal and property damage acci-
dents could not be developed, but the effect for non-fatal accidents appears
smaller by a factor of about three.
It is quite possible that the changed
law produced a transient effect as well as a (smaller) long term increase
in accident rates.
However, the data did not include enough months after
the change to enable detailed investigation of these transient effects.
Despite the dramatic increase in fatalities among 18-20 year olds and
in the number of drinking-related citations, some care must be exercised
in using the results to draw conclusions about the drinking behavior of
youths.
From a public policy point of view, one would like to know how
the accident and drinking behavior of 18-20 year olds before and after
March 1973 compares with that of older motorists.
Arguments for repealing
the law would be strengthened if the post March 1973 accident rate for the
youths reflected a much higher drinking, driving and accident involvement
rate than existed among older age groups.
It is quite tempting to draw such an inference from the above results.
The logic is as follows:
(1) The increase of 5 per month in the number
of fatalities involving 18-20 year olds was caused by the relaxed drinking
-28-
law and reflects an increase in driving-after-drinking accidents.
(2) Since
this increase matches the Increase in operating-after-drinking citations,
the latter are a good indication of drinking-related accidents.
(3) Even
If we assume that no operating-after-drinking related fatalities prior to
March 1973 involved 18-20 year olds,* the 5 or 6 new monthly 18-20 year old
drinking-related fatalities amount to more than 35% of all post-March 1973
operating-after-drinking citations.
(4) Since 18-20 year olds comprise
only 8% of all drivers, the group accounts for more than 4 times its share of
drinking-related fatalities.
The problem with this reasoning is that all operators in all age groups
are assumed to receive drinking-related citations whenever involved in
fatal accidents after drinking.
Before March 1973, only 15% of all operators
involved In fatalities received drinking citations.
But numerous studies
have indicated that upwards of 50% of all auto fatalities are alcohol
related. 11
Raw data from the Massachusetts State Police Laboratory suggest
similar numbers (55%-60%
after March 1973).**
for both over and under 21 year old age groups
Another indication of changed reporting is that, even
though such a small percentage of fatalities produced drinking violations,
the number of monthly operating-after-drinking violations after March 1973
increased by more than the increase in 18-20 year old fatalities --
and that
doesn't count any additional operating-under-the-influence violations.
In light of this possibility that drinking related citations may be an
incomplete and biased indication of alcohol-related fatalities among all
*Preliminary data from the Department of Public Safety (reported, for example,
in the February 1, 1974, issue of the Boston Herald American) associate 17%
(30 out of 174) of the drinking-related citations issued between March 1,
1972 and January 24, 1973 with 18-20 year old operators.
**More extensive discussion of the State Police Laboratory data may be found
in Appendix III.
_
_
e
~
_^
~
1
1_~
_
__I-IIIIIIIII-DYIY
--II- -^·
I·I--1--_
--__.II_
-29-
age groups, let us reexamine our results.
developed In this paper
The most reliable estimate
s the 40; increase in 18-20 year fatalities.
Fatality data are generally considered to be the most complete accident
data and, unlike the drinking violation data, are not affected by citation
practices.
Since an increase in fatalities was observed after March 1973
only for the 18-20 year-old group, the additional 5.3 involvements per
month is our best indication of the increase in dr:nk;ng-related fatalities
due to the law.
These additional 5.3/month amount to 28%
1973 18-20 year old fatalities.
(5.3/19) of the post March
But 18-20 year-olds had been regularly
involved in alcohol related fatalities prior to the change in law.
Suppose
the 18-20 year olds now drove after drinking as often as other age groups and
in accordance with the studies mentioned above were involved in drinkingrelated fatalities that accounted for about half the fatal accidents associated with their age group.
Then about 10 (53%) of the roughly 19 monthly
(post March 1973) fatal accidents involving 18-20 year olds would be alcohol
related.
Of these 10, about 5 would result from the change in the law
implying 5/month prior to March 1973.
Thus we expect that 5/i3.7 or 36%
of the 18-20 year old fatalities before March 1973 involved alcohol.
2 and 3 drinking-related citations were issued
in fatalities before March 1973.*
Between
monthly to 18-20 year olds involved
Allowing for a certain amount of under-
reporting, the 5/month estimate for pre-1973 months is reasonable.
This picture of 18-20 year old behavior can be consistent with the
drinking-related violations data as well.
Suppose alcohol-related fatalities
and citations for other age groups remained unchanged before and after
*From the Department of Public Safety figures cited earlier.
---- `-~1^11-
--"'----
-30-
March 1973 and that 18-20 year olds involved in drinking-related fatalities
were Issued operating-after-drinking citations half the time before March 1973
and three-fourths of the time afterwards.
13.7 · 0.36 · 0.50
=
Then they would account for
2.5 citations per month before March 1973 and
19 x 0.53 x 0.75 - 7.6 citations after.*
The difference of 5.1 citations per month
Is based on several individual estimates, each of which is subject to substantial
fluctuations.
Nevertheless, It is close to the obser'ved increase of 6 operat-
Ing-after-drinking citations per month.
The above argument shows how the observed data could result if alcohol
were related to the same fraction of fatal accidents for 18-20 year olds as
for older drivers.
However, 18-20 year olds typically have more than their
share of fatal accidents.
Though they include 8% of all drivers, they account
for about 15% of all involvements in fatal accidents between 1969 and 1972.15
Whether this is due to more driving or driving exposure, to less driving experience and skill,-or to some other reason is not clear, but relatively frequent
driving-after drinking Is not likely to be the cause.
In conclusion, our interpretation of the consequences of the reduced
drinking age supports a re-evaluation of the arguments for repealing the law.
While the 18-20 year olds do have a higher fatal accident involvement rate than
older drivers, the same fraction appears to be drinking-related -- implying that
18-20 year olds now drink and drive about as often as older drivers.
Hence,
arguing for a prohibition on 18-20 year old drinking solely in order to avoid
the 5/month increase in fatal accidents involving 18-20 year olds appears
unduly discriminatory against this age group -- why not prevent 30-40 year olds
*The second term n the calcullations is the previously estimated fraction of
fatal accidents that involve alcohol.
-
- -
- ___1_
I---
---
.-
·------
--
·-
------
A_~I
-
-
-
-31-
from drinking and protect their families as well as themselves?*
6. Future Research
Finally, some comments about unanswered questions and future research.
Appendix III discusses some of these issues in more detdil.
No-fault insur-
ance appeared to limit the usefulness of non-fatal inJury and property damage
data, thereby eliminating the possibility of estimating the law's effect on
less serious accidents.
The best one could do was get a crude indication
from drinking violation data that the effect is much smaller than for fatalities.
Transient effects may be involved (see in particular the DI-Tl data
in Figure 4 for operating-after-drinking fatalities) but cannot be adequately
studied without more data following March 1973.
Unfortunately, data after
October 1973 must be adjusted to include "energy crisis" effects -- a particularly difficult correction if various age groups are affected differently.
The most logical next step would be to break down the drinking-related
citations by age and repeat the above analysis.
Accurate estimates of the
fraction of 18-20 year old fatalities that involve liquor are central to
policy recommendations regarding the drinking age law.
However, the State
Police Lab and drinking-related citation data are not unbiased, consistent
measures of drinking-related driving.
More detailed information is needed about the
circumstances whereby drinking-related citations are issued and about the
relationship between operator blood specimens tested and the number and type
of fatal accidents involved.
*Since 18-20 year olds have more than their share of fatalities, increasing the
driving age might be justifiable (unless the difference is due to experience),
but such an option is not at issue here.
I
-
-
-~~~~~~~~~~~~~~~~~~~~~~~
..
,1
_---1·
1
1
I
I---
-32-
Bibliography
1. Campbell, Donald T., "Measuring the Effects of Social Innovations by
Means of Time-Series," Statistics: A Guide to the Unknown, J. Tanur,
et al. editors, Holden-Day, Inc., San Francisco, 1972, pp. 120-129.
2. Department of Scientific Research and Road Research Laboratory, Research
on Road Safety, London: Her Majesty's Stationary (f ice, 1963.
3. Gibra, Issac N., Probability and Statistical Inference for Scientists
and Engineers, Englewood Cliffs, N.J., Prentice Hall, Inc., 1973.
4. Glass, Gene V., Analysis of Data on the Connecticut Speeding Crackdown
as a Time Series Quasi-Experiment, Law and Society Review 311, (19681969), pp. 55-76.
5. Glass, Gene V., A Program for the Analysis of Certain Time-Series
Quasi-Experiments, Educational and Psychological Measurement 27
(1967),
pp. 743-750.
6. Haight, Frank A., "Do Speed Limits Reduce Traffic Accidents?,"
Statistics: A Guide to the Unknown, Holden-Day, Inc., San Francisco,
1972, pp. 130-136.
7. Haddon, W., Accident Research--Methods
and Row, publishers, 1964.
and Approaches, New York:
Harper
8. Holtzman, Wayne H., "Statistical Models for the Study of Change in a
Single Case," in Problems in Measuring Change, C. W. Harris, editor.
The University of Wisconsin Press, Milwaukee, 1963.
9. Kendall, M. G., Time Series, New York: Hafner Press, 1973.
10.
Liquor Handbook, New York: Gavin-Jobson Associates, Inc., 1968.
11.
Little, A. D., The State of the Art of Traffic Safety, New York: Praeger
Publishers, Inc., 1970.
12.
National Safety Council, Accident Facts, Chicago, Illinois (1967 and
1969 editions).
13.
National Safety Council, Traffic Safety, Chicago, Illinois, March and
September issues of 1969-1973.
14.
Rebello, Robert E., editor, Econometric Software Package Users Manual
(ESP), Cambridge, Mass., M.I.T., November, 1972.
15. Registry of Motor Vehicles, the Commonwealth of Massachusetts, Publication
of Statistical Facts, Boston: Registry of Motor Vehicles Statisticians
Office, 1969-1972.
16.
Spiegel, Murray P., Theory and Problems of Statistics
Outline Series, New York: McGraw-Hill Book Company, 1961.
A-1
Appendix I -- THE TIME SERIES
Part A:
The Interrupted Time Series Design
The interrupted time series design is one useful method which allows us
to draw inferences from statistical data. Graphically, the statistic being
tested is plotted for a significant amount of time before and after a policy
change is introduced.
(See Figure A-1 below.)
Assuning everything except
the policy under study remains unchanged, we can then deduce whether a change
in the statistic occurring after the policy change is associated with significantly different behavior (LINE A), is a continuation of a trend that had
been in progress prior to the policy change (LINE B), or is just part of an
unstable "zig-zag" (LINE C).
_T_
-
I
I
I
NIUM bEt
OF
I
I
A :C
LiNr_.
)ENTS
A
II
I
it
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I
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MB
ER
OF
A CC
DN
T5
LINE
B
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t
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,i
t
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N
Jm, BE R
o F
A Cc DCNT S
I
1
I-
LINE
C
tiut e
FIGURE A-1
P
POLI C Af
ci4A A- &
4e
A-2
Notice that ifwe had observed the time period just before and just
after the policy change there would be no way of telling which of the three
cases mentioned above would be a valid representation of the change being
studied.
Attempting to identify the causal relationship between a change in
policy and a specific measure of effectiveness iscomplicated by the fact
that many other factors besides the change in policy under study may influence the specific measure of effectiveness being tested.
Since itmay not
be feasible to isolate the change in policy under study and its specific
measure of effectiveness from other factors which may influence the observed
results, several hypotheses may have to be examined using a variety of statistics and controlling for various third-variable effects.
Part B:
Miscellaneous Factors That May Influence the Accident Data
Several factors might influence the accident statistics in addition to
the policy change concerning the eighteen year old drinking law. Before
associating a change in the accident statistics with the change inpolicy,
the effect of these other factors must be considered.
Any change in the driving environment or inthe pattern of road use
between 1969 and 1973 might affect the number of Massachusetts reported
accidents and complicate the analysis of the drinking law's effects.
If
changed driving patterns were only caused by new 18-20 year old drinking
habits, adjustments might not be required. However, other circumstances
might introduce systematic bias inthe monthly accidents figures. While
most aspects of Massachusetts' driving environment are unlikely to have
changed substantially and systematically during 1969-73, factors such as
increased vehicle safety and seat belt use o a steady increase inmiles driven
are possible exceptions.
A-3
As is commonly done, we shall adjust for the number of miles driven per
month.
National Safety Council figures indicate a 5% per year increase in
mileage but a steady fatality rate per (hundred million) vehicle miles through
the sixties [12,13].
During four years, the effect of increased mileage
on the number of accidents is substantial.
We shall also adjust for seasonality.
Included under this heading are such
monthly changes as weather, holidays and liquor consumption habits.
Some of
the seasonality effects manifest themselves in changes in the number of miles
driven in certain months relative to others.
holidays.
Examples are months having
However, National Safety Council figures show that the number of
fatalities per hundred million miles driven is not the same for each month.
Apparently other factors produce monthly changes in accident risk.
Since we
have only seven months data following the change in the drinking law, corrections for seasonally different months are important.
Another way accident statistics can change is when the way accidents are
reported change.
Different standards for what is considered an accident may
be in effect during different years.
Also, more or less accidents may be
reported depending on the reporting mechanism.
The advent of No Fault In-
surance in Massachusetts beginning in January 1971 apparently had a significant impact on the number of reported non-fatal accidents.
This fact might
complicate the interpretation of certain accident statistics before and after 1971.
We assume that other factors influencing the monthly accident figures
did not introduce any systematic bias in the data but contributed to random
statistical fluctuations in the data.
A-4
Part C: Corrections for Mileage, Seasonality and No-Fault
As explained in the text, two methods of correcting for mileage, seasonality and no-fault were employed. Method I involved scaling monthly figures
by estimated mileage and seasonality trends. Method IIused the experience
of drivers over 23 years of age as a control group.
Method I
Visual examination of several series suggested that the No-fault law
produced a marked reduction in reported accidents beginning inJanuary 1971.
For non-fatal injury accidents the effect was most pronounced.
graphs of raw data in Section 2 of the text.)
(See the
The impact of no-fault appear-
ed to produce additional changes during 1972 and we felt that 1971-1972 was
too short a time span to gauge what the 1973 impact ought to be. Accordingly,
the non-fatal accident data for the four age groups appeared most affected and
were not further analyzed.*
The monthly figures for the remaining sets of data were normalized to
monthly figures per billion vehicle miles by dividing each monthly figure by
the estimated number of miles driven each month. The estimates [15], based on
gasoline consumption, are given inTable A-1 and reflected an approximately
linear increase inmileage of 0.4% per month.
Next, a seasonal index for each of the twelve months of the year was
developed for particular classes of accident data. These reflected the ratio
of the particular monthly accident rate to one-twelfth of the yearly average.
For example, the seasonality factor for February (for operators involved in
fatal accidents) is 0.75 indicating the number of reported operators involved
infatal accidents during February (with 28 days) is three-quarters of the
rate for a "normal" month with no seasonal effects. By dividing each mileage* Interestingly enough, no-fault appeared to have a different affect on reported accidents involvingyoung and old drivers. Alarger drop inreported non-fatal
accidents apparently took place for older age groups.
A-5
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adjusted monthly figure by its seasonality factor, all the monthly figures
were deseasonalized.
Seasonality factors were developed for particular sets of data using
several sources and criteria. Because the series only spanned four years
(1969-1972, plus January through September of 1973), ar! because large fluctuations ineach year's monthly figures were present, itwas not possible to
calculate reliable seasonal factors from the data themselves.
Information
from the following sources were also used:
a) Seasonality factors developed by using national data for
fatalities per mile driven between 1966 and 1968 [12].
b) Monthly fatality data for Massachusetts between 1966 and 1970 [15].
c) Monthly hard liquor sales during 1967.
d) Monthly non-fatal injury accident data for Massachusetts
between 1966 and 1970 (the five years immediately before no-fault
insurance).
To calculate seasonality factors using (b)and (d)above, monthly figures
for each year were divided by one-twelfth the yearly total.
For each month,
the median ratio of the five years was chosen as the seasonal factor.
(Using
the median avoided sensitivity to extreme values.) Although these monthly
figures were not based on accidents per miles driven but rather on the absolute number of accidents, itwas felt that the monthly seasonal variation in
miles driven was negligible compared to the seasonal effect. All age groups
were assumed to have the same seasonal effect.
Examining the appropriate raw time series suggested that series involving fatalities and/or alcohol showed the same gross seasonality properties.
For these data, sources (a), (b), and (c)above were used to calculate
seasonality factors. All of the factors in sources (a), (b), and (c)resembled
each other inrelation to which months were high and low as well as inthe
A-7
value of the factors themselves. The median of the factors of (a), (b), and
(c)was chosen for the overall factor for the alcohol related and/or fatality
related statistics being tested. The final figures arrived at inorder of
the calendar months were .84, .75, .87, .95, 1.04, 1.03, 1,00, 1.09, 1.00,
1.11, 1.15, 1.12.
Factors derived from (d)were used for the non-alcohol related, non-fatal
accident figures for all ages. The averages of the month to year ratios for
1971 and 1972 multiplied by twelve for total property damage figures were
used as seasonal factors for all non-alcohol-related property damage accident figures. The values are not listed here because these sets of
data were not used inthe final analysis.
(See the text for a list of those
sets used infinal analysis.)
Summarizing for Method I, series judged not to be grossly affected by
No-Fault were adjusted
(1) By dividing each monthly figure by the estimated number of
miles driven in that month;
(2) By dividing the result of step 1 by the appropriate seasonality
factor.
Method II
The alternative method for adjusting the raw data involved using accident data for operators aged 24 and over as a control. Monthly figures for
each type of accident involving young drivers were divided by the corresponding over-23 year old figures. The idea isthat the over-23 year old group
exhibits the same monthly mileage and seasonal fluctuations (and, perhaps
the same no-fault insurance characteristics) as the younger age group--but
isunaffected by the drinking law. Hence, resulting ratios would exhibit only
random monthly fluctuations or systematic changes due to the new drinking law.
A-8
Examination of the gross properties of the time series for the different
age groups lends credence to this assumption.
mained fairly constant.
Also, the yearly ratios re-
The table below indicates the percentage of all
fatal accidents involving operators in each age group.
Groups
Table A-2: Operators and Accident Involvements h Ag__Ae
% of Fatal Accidents involving
% of All Operators
an Operator in Each Group
in Each Group
Age Group
1972
1971
1970
1969
1969 1970 1971
under 18
18-21
21-23
over 23
Source:
2.6
7.6
8.2
81.6
2.8
7.7
8.3
81.2
2.6
8.0
8.1
81.3
6.6
14.8
14.5
64.1
7.0
15.1
14.2
63.7
7.2
14.4
13.1
65.3
6.8
14.7
14.0
64.5
Massachusetts Registry of Motor Vehicle Annual
Statement Reports
Figures 4, 5 and 6 in the text graph the Dl-T1, A2-T1 and A4-T2 time
series (numbers 1, 8 and 14) before and after adjustments for mileage and
seasonal factors.
Figure 5 compares the raw data for A2-T1 with the ad-
dustments using both Methods I and II. These figures are discussed in the
body of the text.
A-9
Appendix II -- INTERPRETING THE TIME SERIES
Part A:
Correlation and Interruptions
In the time series approach, we have a set of temporally ordered (adJusted) observations divided into two groups; those pertaining to the time
period preceding the policy change and those pertaining to the time period
following the policy change.
The statistical methods appropriate for analyzing the data depend
heavily on the characteristics of the data.
If the figures are uncorrelated
with one another, e.g., independent and randomly fluctuating, then a variety
of standard statistical procedures could be applied.
However, if some
correlation among the data points is present, e.g., some residual seasonality
or some kind of significant upward trend, then much more complicated methods
are required and minor interruptions become harder to identify.
A common
measure of the degree of correlation among points in a time series is
the autocorrelation coefficient of order k, where k is the number of time
units separating the points,
If enough observations of the time series
are available, then the autocorrelation coefficient PK can be estimated by
using the formula [8]
n-K
(Xi - X)(Xi+K - X)/(n - k)
rK
n
(Xi - X)2/n
i=l
where
Xi = th observation,
rK = estimate for autocorrelation coefficient PK
n = number of observations
and
X=
i X
n i=1
Al 0
Theoretically, -1 < PK
<
1 . When IPKI is near 1, a high degree of
correlation is present. When IPKI is near 0, little or no correlation is
present. A plot of rK versus k for a time series is called a correlogram.
The general appearance of a correlogram along with the values of rK tell
a lot about the characteristics of a time series.
An independent sequence of normally distributed observations would have
a correlogram with values rK fluctuating close to 0. A periodic series
would exhibit a periodic correlogram with high values of rK repeating at
various intervals. A series with a trend might exhibit large values for
some of the rK and an appearance of a sloping line as the general shape of
the correlogram.
(See the examples
n Figures A-2 through A-5.)
To test for significant correlation in a correlogram, we use rK as an
estimate of PK and test the hypothesis that
K = 0 . Confidence limits for
rK are available if we assume independent mormally distributed fluctuations
and an rK that behaves in the same way as serial correlation. [ 3 g]
independent, normal assumptions are often used for accident data[Lf
The
since
it seems reasonable that random fluctuations in the number of accidents
during one month would be independent of fluctuations in other months.
For a 50 term series, we would accept the hypothesis that
-0.28
K = 0 if
rK < 0.28 for any particular value of K.
In fact, some additional complications arise. As k increases, the con-
fidence limit gets wider since fewer and fewer terms are available for calculating rK .
Thus, in the case of a series with fifty terms, about the
first thirty values of rK are worth calculating.
Since the confidence limits
apply to a single rK value, all thirty values are not expected to fall within
the 95% linits.
If the values of rK were independent and PK did in fact equal
A-il
0, then the probability that more than three fell outside would be about 0.06.
Accordingly, we shall accept the PK = 0 hypothesis if no more than 3 are outside, if these are not too large (e.g., if IrKI is still < 0.4) and if the
shape of the correlogram is not pronouncedly periodic or suggestive of a trend.
A correlogram can be calculated for each of th
fifty months preceding the policy change.
tie series for the
K = 0 is accep-
If the hypothesis
ted, we assume that the basic characteristics (i.e., independent normally
distributed fluctuations) in the data apply to the points following the
policy change.
These points were not included in the original correlogram
since we expect something might shift due to the policy change and the points
by themselves, did not contain enough observations to compute rK
The pre-policy change and post-policy change are then compared to
determine whether they are significantly different.
The null hypothesis is
that they have the same mean and standard deviation (i.e., the policy change
had no effect).
Once again a 5% confidence level is used.
The criterion
was defined by a one-tailed t-test for the difference between two means since
we suspect that the most likely alternative to equal means should be for the
mean of the post-group to be larger'than the mean of the pre-group.
In
mathematical terms, the hypothesis that the period A mean is the same as
the period C mean* for any well-behaved series is rejected if
- Y > t95,55 Vp50 + 7
50
where X = (1/50)
=1l
X i and
=
57
(1/7) 1 X i and X i is the observed
i=51
* Period A covers January 1969 through February 1973; Period C covers
March through September 1973.
A-12
(adjusted) rate during month i for the particular series. Here we let t95,5 5
represent the cutoff value for a one-sided t-test at the 95% significance
level with 55 degrees of freedom -- t95,55 m 1.7. The pooled estimate of the
standard deviation of the observations is used so that
Vp
449sx2
v
+ 6sy2)/55, where s x = (1/49)
2 (1/6)
(X
s,~,=(l~Sy
1
(Xi
and
-
X
Y)2
Y)
i=51
For those series whose correlograms show signigicant autocorrelation,
the analysis becomes very difficult and less discriminating since correlated
but unexplained fluctuations can give rise to large shifts ina time series
inthe absence of any other changes.[lI 9] Removing further trends is hard
since the effort may create further autocorrelation in the adjusted series.[ 9]
Earlier studies of Massachusetts fatalities have indicated little correlation
and we hoped that enough series would appear well behaved to enable the
above t-test to be used. As t turned out this was the case.
Inaddition to the correlograms, a further check was employed to test
ifa rise inthe accident rate may have started in the months just previous
to the policy change, but somehow did not affect the correlogram. The mean
of months 44 through 50 was checked against the mean for months 1 through
50 to see if that period had a significant difference as well.
If itdid,
itwould indicate that the change in level may have occured before the policy
change.
A-13
Part B:
The Adjusted Well-behaved Time Series
Inbrief review, two methods were used to adjust the data for increased
mileage and seasonal considerations. A correlogram was used to check which
adjusted data were amenable to the t-statistic hypothesis test for a significant difference between two means. This test was then performed and
results obtained for that available accident data. As indicated in the
main body of the this report, series 1,3, 5, 8, 10, 19, 20 and 21 were
adquately behaved and amenable to the t-statistic hypothesis test.
Inthis
appendix, some of the details of applying the procedures are discussed.
Correlograms were computed using the computer at the M.I.T. Information
Processing Center. As a check, a psuedo-random normally distributed series
of fifty terms and several series of linear and periodic data were correlogrammed
and produced the expected results. Figures A-2 through A-5 graph the correlograms
of the normal samples and several well-behaved and correlated series of accident data.
Note the apparent periodicity of the driving under the influence violations.
For the available accident data, the mileage and seasonality corrections
accounted for only a small part of the variations from month to month.
This
result isto be expected since the numbers of accidents occurring per month
are small for many categories we considered.
The seasonal adjustment did
reduce the total variance of the series as was expected, and the mileage
adjustment did remove an increasing trend of about 5% per year. The random
fluctuations were so large, however, that correlograms of some of the acceptably-behaved series before mileage and seasonal adjustments, were slightly
correlated but otherwise not much different from the correlogram for the adjusted data.
Our interpretation of this result is that it shouldn't affect
the analysis substantially if the seasonal or mileage adjustments are generally
reasonable though perhaps not very precise.
A-14
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A-18
Appendix III -- DATA DIFFICULTIES AND FUTURE RESEARCH
In addition to the introduction of no-fault insurance (which affected
the consistency with which accidents are reported), other data difficulties
are possible.
In trying to develop inferences from the data concerning the
effect of the policy change, other historical events ocuring near the time
of the policy change could effect the accident statistics.
shortage beginning in October of 1973 is just such an event.
used data only through September 1973.
The gasoline
This study
Use of data beyond October 1973
would have to take into account possible effects of reduced speed and driving
on the general accident rate.
Another source of difficulty may be in the differences in reporting
for different age groups and the completeness of reporting for certain
types of accidents.
as consistent.
violations.
For fatal accidents, reporting is generally regarded
However, this may not be the case for drinking-related
If most violations for one age group were reported while other
groups were less frequently cited, then a rise in that one group's rate
could produce a sharp rise in the total.
This might explain why the impact
of the increase in 18-21 year old fatalities did not register on the total
number of accident fatalities (all of which are assumed to be reported) but
did register on the total number of the after drinking violations in fatal
accidents.
Few of Massachusetts' fatal accidents involve drinking violations
(around 20%) compared with the 50% figures developed by controlled studies.
of alcohol's role on fatalities.
Hence, the above reasoning is a likely
explanation.
Massachusetts State Police lab test results are subject to other biases
but are closer to the 50% figures and are consistent with the section 4 results.
_
__
_I___I
_IIXIUII__UI·1I_·_l--·-L·I_^···LLIL
A-19
Medical Examiners are required by law to send the lab blood specimens of
all individuals killed inauto accidents.*
alcohol content of the specimens.
The lab then determines the
However, the results can provide only a
crude indication of the percentage of accidents that are alcohol related
since operators involved infatalities are tested only f they themselves
die within hours of the accidents. Thus, the percentage of specimens from
operators that have significant alcohol content may be biased estimates
and are subject to large fluctuations since the total number of operators
of all ages tested each year is around 140.
During 1972, 57% of the 21-and-
over operators and 47% of the under 21 operators tested had blood alcohol
contents above 0.05%. In1973 the corresponding percents were 59% and 55%.
The 47% and 55% figures for 18-20 year olds during 1972 and 1973 roughly
consistent with the (more reliable) findings for the 18-20 year old fatality
data.
To see this assume that 47% (or 6.4 per month) of all 1972 fatalities
involving 18-20 year olds were alcohol related. Assume also that 56.6%
(or 10.8 per month) of all post March 1973 fatalities involving 18-20 year
olds were alcohol related. The difference--i.e., 10.8-6.4 = 4.4 fatalities
per month--is not too far from 5.3 per month increase inalcohol-related
fatalities among 18-20 year olds.
Future studies may make use of more sophisticated techniques to analyze
data such as the property damage and non-fatal accident figures that were
too poorly behaved to be studied here.
The Box-Tiao method of correcting
for autocorrelation isone possibly--a computer program isavailable for
using this model on a time series [5:].
Other methods to analyze data with
increasing trends could include regression analysis with or without provision
-
- -
* Here, killed isdefined as dead within 4 hours of the accident.
_
1_
CI
113______U___lll__l_
A-20
for correlated error.
However, most such analyses are complicated since few
data points following the policy change are available.
More data would be helpful in analyzing the series to check for transient effects after March 1973.
Using such data is complicated by the gaso-
line shortage effect. Using more data before 1969 my ot help significantly
since the real accuracy of the tests depend on the availability of the post
policy change data.
Further breakdowns of the alcohol-related violations by age might help
illuminate the effect of reporting biases.
These further breakdowns, how-
ever, would involve very small numbers and exhibit large fluctuations
relative to the mean.
In addition, they would be subject to the same biases
and underreporting discussed earlier for the fatal number of operating-afterdrinking violations.
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