Statistical Methods in Medical Research - part 9 pptx

^p 

N
i
p
i
N
,
where p
i
is the estimated prevalence in the ith stratum. The variance of ^p is given by the
equivalent of (19.2), in which we shall drop the terms f
i
as being small:
varp
1
N
2

N
2
i
p
i
1 À p
i

n
i
:
The values of var^p) for the three allocations are as follows:

Allocation var^p)
A0Á000714
B0Á000779
C0Á000739
As would be expected, the lowest variance is for A and the highest for B, the latter being
only a little lower than the variance for a random sample.
Multistage sampling
In this method the sampling frame is divided into a population of `first-stage
sampling units', of which a `first-stage' sample is taken. This will usually be a
simple random sample, but may be a systematic or stratified sample; it may also,
as we shall see, be a random sample in which some first-stage units are allowed to
have a higher probability of selection than others. Each sampled first-stage unit
is subdivided into `second-stage sampling units', which are sampled. The process
can continue through as many stages as are appropriate.
There are two main advantages of multistage sampling. First, it enables the
resources to be concentrated in a limited number of portions of the whole
sampling frame with a consequent reduction in cost. Secondly, it is convenient
for situations in which a complete sampling frame is not available before the
investigation starts. A list of first-stage units is required, but the second-stage
units need be listed only within the first-stage units selected in the sample.
Consider as an example a health survey of men working in a certain industry.
There would probably not exist a complete index of all men in the industry, but it
might be easy to obtain a list of factories, which could be first-stage units. From
each factory selected in the first-stage sample, a list of men could be obtained and
a second-stage sample selected from this list. Apart from the advantage of having
to make lists of men only within the factories selected at the first stage, this
procedure would result in an appreciable saving in cost by enabling the investi-
gation to be concentrated at selected factories instead of necessitating the exam-
ination of a sample of men all in different parts of the country.
The economy in cost and resources is unfortunately accompanied by a loss

of precision as compared with simple random sampling. Suppose that in the
654 Statistical methods in epidemiology
example discussed above we take a sample of 20 factories and second-stage
samples of 50 men in each of the 20 factories. If there is systematic variation
between the factories, due perhaps to variation in health conditions in different
parts of the country or to differing occupational hazards, this variation will be
represented by a sample of only 20 first-stage units. A random sample of 1000
men, on the other hand, would represent 1000 random choices of first-stage units
(some of which may, of course, be chosen more than once) and would con-
sequently provide a better estimate of the national mean.
A useful device in two-stage sampling is called self-weighting. Each first-stage
unit is given a probability of selection which is proportional to the number of
second-stage units it contains. Second-stage samples are then chosen to have
equal size. It follows that each second-stage unit in the whole population has an
equal chance of being selected and the formulae needed for estimation are
somewhat simplified.
Cluster sampling
Sometimes, in the final stage of multistage sampling, complete enumeration of
the available units is undertaken. In the industrial example, once a survey team
has installed itself in a factory, it may cost little extra to examine all the men in
the factory; it may indeed be useful to avoid the embarrassment that might be
caused by inviting some men but not others to participate. When there is no
sampling at the final stage, the method is referred to as cluster sampling. The
investigator has no control over the number of sampling units in the clusters and
this means that the loss of precision, compared with simple random sampling, is
even greater than that in multistage sampling.
Design effect
The ratio of the variance of an estimator from a sampling scheme to the variance
of the estimator from simple random sampling with the same total number of
sampling units is known as the design effect, often abbreviated to Deff.In

Example 19.1 the Deff for allocation C is 0Á000739=0Á000803  0Á92. Another
way of looking at the Deff is in terms of sample size. The same precision could
have been achieved with a stratified sample of 92 people with allocation C as for
a simple random sample of 100 people. The stratified sample is more efficient
(Deff < 1) than simple random sampling and this will occur generally provided
that there is a component of variation between strata. The efficiency of stratified
sampling increases with the increasing heterogeneity between strata and the
consequent greater homogeneity within strata.
In contrast, multistage and cluster sampling will usually have a Deff > 1.
That is, a larger sample size will be required than with simple random sampling.
19.2 The planning of surveys 655
For cluster sampling with m members per cluster and a correlation within
clusters of r for the variable under study, the Deff is given by
Deff  1 m À1r,
which will always exceed 1 (except in the unlikely scenario of negative correla-
tions within clusters). A similar expression was given in §18.9 for sample size
calculations in a cluster randomized trial. If m differs between clusters, then, in
the above formula, m is replaced by

m
2
=

m, which is approximately

m,
provided that the coefficient of variation of cluster size is small.
The above discussion of the efficiency of different sampling schemes relative
to simple random sampling is in terms of sample size. As we noted when
discussing multistage sampling, one of the advantages of this method is a reduc-

tion in cost and the overall efficiency of a sampling scheme should be assessed in
terms of the cost of carrying out the sampling, not just in terms of total sample
size. If the cost of a sampling scheme is c per sample member, relative to the cost
per member of a simple random sample, then the overall efficiency of the
sampling scheme is
100%
c  Deff
:
Thus, a sampling scheme is more, or less, efficient than simple random sampling
according as c  Deff is less, or greater, than unity, respectively. Thus, a cluster
sampling scheme with six members per cluster and a correlation within clusters
of 0Á2(Deff  2Á0) will be more efficient than simple random sampling, provided
that the average cost of conducting the survey per sample member is less than a
half of the cost per member of a simple random sample. In this case the increase
in sample size required to achieve a specified precision has been more than offset
by a reduction in costs.
Mark±recapture sampling
The name of this technique is derived from its application to the estimation of
the number of animals or birds in an area. Traps are set and the captured animals
form a sample of the population. They are marked and released. A second set of
trappings yields a second sample consisting of unmarked animals and some that
were marked on the first trapping occasion. Again, animals are marked and
released and the process is continued for several sets of trappings.
The numbers of animals captured on each occasion, together with the num-
bers of recaptures of previously marked animals, can be used to estimate the
total population. Assumptions must be made on whether the population is
closed (no gains or losses over the total sampling period) or not, on whether
the probability of capture depends on the previous capture history, and on
656 Statistical methods in epidemiology
heterogeneity between animals in probability of capture. The more information

that is availableÐfor example, more trapping occasions and a marking system
that allows identification of the occasions on which each animal was capturedÐ
the more readily can assumptions be checked and modified.
This technique may be applied for the purpose of estimating the size of a
population of individuals with some health-related characteristic. It is particu-
larly useful for rare characteristics, which would require a very large sample
using more traditional methods; for habits which people may be reluctant to
disclose on a questionnaire, such as intravenous drug use; or for groups which
may be differentially omitted from a sampling frame, such as homeless people in
a city. Lists containing members of such a group may be available in agencies
that provide services for the group, and if several lists are available then each
may be considered to correspond to a `trapping' occasion. If there is sufficient
information on identity, then it can be established whether a person is on more
than one list (`recaptures'). A difference from the animal trapping situation is
that there may be no time sequence involved and the lists may be treated
symmetrically in respect of each other.
If there are k lists, then the observations can be set out as a 2
k
table, denoting
presence or absence on each list. The number in the cell corresponding to absence
on all k lists is, of course, unobserved and the aim of the method is to estimate
this number and hence the total number. It will usually be reasonable to antici-
pate that the probability of being on a list is dependent on whether or not a
person is on some of the other lists. That is, there will be list dependency
(corresponding to capture being dependent on previous capture history). A
method of proceeding is to fit a log-linear model to the 2
k
À 1 observed cells of
the 2
k

table and use this model to estimate the number in the unobserved cell.
Dependencies between the lists can be included as interaction terms but the
highest-order interaction between all k lists is set to zero, since it cannot be
estimated from the incomplete table.
A text on the methodology is given by Seber (1982), and Cormack (1989)
describes the use of the log-linear model. A brief review is given by Chao (1998).
The method gives an estimate of the total population size and its standard error.
A problem is that the estimate may be dependent on non-verifiable assumptions,
so that the standard error does not adequately describe the uncertainty. Never-
theless, in situations where more robust methods, based on random sampling,
are infeasible, the method does allow some estimation.
Imputation
Sample surveys usually have missing data through some people failing to answer
some of the questions, either inadvertently or by refusing to answer particular
questions. The analysis of the whole data set is facilitated if the missing data are
19.2 The planning of surveys 657
replaced by imputed values. Imputed values may be obtained using a model
based on the observed values. For example, a multiple regression of x
1
on
x
2
, x
3
, , x
p
might be fitted on the complete data and used to estimate values
of x
1
for those individuals with this variable missing but with observed values of

x
2
, x
3
, , x
p
. This gives the best predicted values but it is unsatisfactory to
substitute these values because to do so excludes variability, and any analysis
of the augmented data would appear more accurate than is justified. Instead, the
random variability has to be built into the imputed values, not only the varia-
bility about the fitted regression line but also the variability due to uncertainty in
estimating the regression coefficients. Thus imputed values contain random
components and there is no unique best set of imputed values. Even for an
imputed set of data with random variation incorporated, a single analysis will
give standard errors of estimated parameters that are too small. This can be
avoided by multiple imputation; that is, the missing data are imputed several
times independently, and each imputed set is analysed in the same way.
Variances of estimated parameters can then be produced by combining the
within-imputation variance with the between-imputation variance. For further
discussion of missing data and the importance of considering whether the fact
that data are missing is informative in some way see §12.6.
Multiple imputation has generally been used with large sample surveys but
may be more widely applied as suitable software becomes available. Readers
wishing to learn more about this technique are referred to Rubin (1987) and
Barnard et al. (1998).
Barnard et al. (1998) also describe applications of multiple imputation to a
wider range of problems than non-response. These include imputation of the true
ages of children when the collected data on ages were insufficiently precise, and
the imputation of dates of acquired immune deficiency syndrome (AIDS) diag-
nosis in people with human immunodeficiency virus (HIV) infection who had not

yet contracted AIDS, using a model based on a set of covariates (Taylor et al.,
1990).
Other considerations
The planning, conduct and analysis of sample surveys give rise to many problems
that cannot be discussed here. The books by Moser and Kalton (1979) and Yates
(1981) contain excellent discussions of the practical aspects of sampling. The
books by Cochran (1977) and Yates (1981) may be consulted for the main
theoretical results.
The statistical theory of sample surveys is concerned largely with the meas-
urement of sampling error. This emphasis may lead the investigator to overlook
the importance of non-sampling errors. In a large survey the sampling errors
may be so small that systematic non-sampling errors may be much the more
658 Statistical methods in epidemiology
important. Indeed, in a complete enumeration, such as a complete population
census, sampling errors disappear altogether, but there may be very serious non-
sampling errors.
Some non-sampling errors are non-systematic, causing no bias in the average.
An example would be random inaccuracy in the reading of a test instrument.
These errors merely contribute to the variability of the observation in question
and therefore diminish the precision of the survey. Other errors are systematic,
causing a bias in a mean value which does not decrease with increasing sample
size; for example, in a health survey certain types of illness may be systematically
under-reported.
One of the most important types of systematic error is that due to inadequate
coverage of the sampling frame, either because of non-cooperation by the
individual or because the investigator finds it difficult to make the correct
observations. For example, in an interview survey some people may refuse to
be interviewed and others may be hard to find, may have moved away from the
supposed address or even have died. Individuals who are missed for any of these
reasons are likely to be atypical of the population in various relevant respects.

Every effort must therefore be made to include as many as possible of the chosen
individuals in the enquiry, by persistent attempts to make the relevant observa-
tions on all the non-responders or by concentrating on a subsample of them so
that the characteristics of the non-responders can at least be estimated. This
allows the possibility of weighting the subsample of initial non-responders to
represent all non-responders (Levy & Lemeshow, 1991, p. 308), or, when back-
ground data are available on all subjects, to use multiple imputation to estimate
other missing variables (Glynn et al., 1993).
Reference must finally be made to another important type of study, the
longitudinal survey. Many investigations are concerned with the changes in
certain measurements over a period of time: for example, the growth and devel-
opment of children over a 10-year period, or the changes in blood pressure
during pregnancy. It is desirable where possible to study each individual over
the relevant period of time rather than to take different samples of individuals at
different points of time. The statistical problems arising in this type of study are
discussed in §12.6.
19.3 Rates and standardization
Since epidemiology is concerned with the distribution of disease in populations,
summary measures are required to describe the amount of disease in a popula-
tion. There are two basic measures, incidence and prevalence.
Incidence is a measure of the rate at which new cases of disease occur in a
population previously without disease. Thus, the incidence, denoted by I,is
defined as
19.3 Rates and standardization 659
I 
number of new cases in period of time
population at risk
:
The period of time is specified in the units in which the rate is expressed. Often
the rate is multiplied by a base such as 1000 or 1 000 000 to avoid small decimal

fractions. For example, there were 280 new cases of cancer of the pancreas in
men in New South Wales in 1997 out of a population of 3Á115 million males. The
incidence was 280= 3Á115  90 per million per year.
Prevalence, denoted by P, is a measure of the frequency of existing disease at
a given time, and is defined as
P 
total number of cases at given time
total population at that time
:
Both incidence and prevalence usually depend on age, and possibly sex, and sex-
and age-specific figures would be calculated.
The prevalence and incidence rates are related, since an incident case is,
immediately on occurrence, a prevalent case and remains as such until recovery
or death (disregarding emigration and immigration). Provided the situation is
stable, the link between the two measures is given by
P  It, 19:4
where t is the average duration of disease. For a chronic disease from which
there is no recovery, t would be the average survival after occurrence of the
disease.
Standardization
Problems due to confounding (Example 15.6) arise frequently in vital statistics
and have given rise to a group of methods called standardization. We shall
describe briefly one or two of the most well-known methods, and discuss their
relationship to the methods described in §15.6.
Mortality in a population is usually measured by an annual death rateÐfor
example, the number of individuals dying during a certain calendar year divided
by the estimated population size midway through the year. Frequently this ratio
is multiplied by a convenient base, such as 1000, to avoid small decimal fractions;
it is then called the annual death rate per 1000 population. If the death rate is
calculated for a population covering a wide age range, it is called a crude death

rate.
In a comparison of the mortality of two populations, say, those of two
different countries, the crude rates may be misleading. Mortality depends
strongly on age. If the two countries have different age structures, this contrast
660 Statistical methods in epidemiology
alone may explain a difference in crude rates (just as, in Table 15.6, the contrast
between the `crude' proportions with factor A was strongly affected by the
different sex distributions in the disease and control groups). An example is
given in Table 19.1 (on p. 664), which shows the numbers of individuals and
numbers of deaths separately in different age groups, for two countries: A,
typical of highly industrialized countries, with a rather high proportion of
individuals at the older ages; and B, a developing country with a small propor-
tion of old people. The death rates at each age (which are called age-specific
death rates) are substantially higher for B than for A, and yet the crude death
rate is higher for A than for B.
The situation here is precisely the same as that discussed at the beginning of
§15.6, in connection with Example 15.6. Sometimes, however, mortality has to be
compared for a large number of different populations, and some form of adjust-
ment for age differences is required. For example, the mortality in one country
may have to be compared over several different years; different regions of the
same country may be under study; or one may wish to compare the mortality for
a large number of different occupations. Two obvious generalizations are: (i) in
standardizing for factors other than, or in addition to, ageÐfor example, sex, as
in Table 15.6; and (ii) in morbidity studies where the criterion studied is the
occurrence of a certain illness rather than of death. We shall discuss the usual
situationÐthe standardization of mortality rates for age.
The basic idea in standardization is that we introduce a standard population
with a fixed age structure. The mortality for any special population is then
adjusted to allow for discrepancies in age structure between the standard and
special populations. There are two main approaches: direct and indirect methods

of standardization. The following brief account may be supplemented by refer-
ence to Liddell (1960), Kalton (1968) or Hill and Hill (1991).
The following notation will be used.
Standard Special
(1) (2) (3) (4) (5) (6)
Age
group Population Deaths
Death rate
(2)=(1) Population Deaths
Death rate
(5)=(4)
1 N
1
R
1
P
1
n
1
r
1
p
1
.
.
.
iN
i
R
i

P
i
n
i
r
i
p
i
.
.
.
kN
k
R
k
P
k
n
k
r
k
p
k
19.3 Rates and standardization 661
Direct method
In the direct method the death rate is standardized to the age structure of the
standard population. The directly standardized death rate for the special popu-
lation is, therefore,
p
H



N
i
p
i

N
i
: 19:5
It is obtained by applying the special death rates, p
i
, to the standard popula-
tion sizes, N
i
. Alternatively, p
H
can be regarded as a weighted mean of the p
i
,
using the N
i
as weights. The variance of p
H
may be estimated as
varp
H


N

2
i
p
i
q
i
=n
i



N
i

2
, 19:6
where q
i
 1 À p
i
; if, as is often the case, the p
i
are all small, the binomial
variance of p
i
, p
i
q
i
=n

i
, may be replaced by the Poisson term p
i
=n
i
 r
i
=n
2
i
, giving
varp
H
9

N
2
i
p
i
=n
i



N
i

2
: 19:7

To compare two special populations, A and B, we could calculate a standard-
ized rate for each (p
H
A
and p
H
B
), and consider

d  p
H
A
À p
H
B
:
From (19.5),

d 

N
i
p
Ai
À p
Bi


N
i

,
which has exactly the same form as (15.15), with w
i
 N
i
, and d
i
 p
Ai
À p
Bi
as in
(15.14). The method differs from that of Cochran's test only in using a different
system of weights. The variance is given by
var

d

N
2
i
vard
i



N
i

2

, 19:8
with vard
i
 given by (15.17). Again, when the p
0i
are small, q
0i
can be put
approximately equal to 1 in (15.17).
If it is required to compare two special populations using the ratio of the
standardized rates, p
H
A
=p
H
B
, then the variance of the ratio may be obtained using
(19.6) and (5.12).
The variance given by (19.7) may be unsatisfactory for the construction of
confidence limits if the numbers of deaths in the separate age groups are small,
since the normal approximation is then unsatisfactory and the Poisson limits are
662 Statistical methods in epidemiology
asymmetric (§5.2). The standardized rate (19.5) is a weighted sum of the Poisson
counts, r
i
. Dobson et al. (1991) gave a method of calculating an approximate
confidence interval based on the confidence interval of the total number of
deaths.
Example 19.2
In Table 19.1 a standardized rate p

H
could be calculated for each population. What should
be taken as the standard population? There is no unique answer to this question. The
choice may not greatly affect the comparison of two populations, although it will certainly
affect the absolute values of the standardized rates. If the contrast between the age-specific
rates is very different at different age groups, we may have to consider whether we wish
the standardized rates to reflect particularly the position at certain parts of the age scale;
for example, it might be desirable to give less weight to the higher age groups because
the purpose of the study is mainly to compare mortality at younger ages, because the
information at higher ages is less reliable, or because the death rates at high ages are more
affected by sampling error.
At the foot of Table 19.1 we give standardized rates with three choices of standard
population: (a) population A, (b) population B, and (c) a hypothetical population, C,
whose proportionate distribution is midway between A and B, i.e.
N
Ci
G
1
2
n
Ai

n
Ai

n
Bi

n
Bi


:
Note that for method (a) the standardized rate for A is the same as the crude rate;
similarly for (b) the standardized rate for B is the same as the crude rate. Although the
absolute values of the standardized rates are different for the three choices of standard
population, the contrast is broadly the same in each case.
Indirect method
This method is more conveniently thought of as a comparison of observed and
expected deaths than in terms of standardized rates. In the special population the
total number of deaths observed is

r
i
. The number of deaths expected if the
age-specific death rates were the same as in the standard population is

n
i
P
i
.
The overall mortality experience of the special population may be expressed in
terms of that of the standard population by the ratio of observed to expected
deaths:
M 

r
i

n

i
P
i
: 19:9
When multiplied by 100 and expressed as a percentage, (19.9) is known as the
standardized mortality ratio (SMR).
To obtain the variance of M we can use the result varr
i
n
i
p
i
q
i
,and
regard the P
i
as constants without any sampling fluctuation (since we shall often
19.3 Rates and standardization 663
Table 19.1 Death rate for two populations, A and B, with direct standardization using A, B and a midway population C.
Age (years)
ABC
Population
Deaths
Age-specific
DR per 1000
Population
Deaths Age-specific
DR per 1000
Population

1000s % 1000s % 1000s %
0± 2100 8Á97 10 000 4Á76 185 14Á51 4100 22Á16 1 174 11Á74
5± 1900 8Á12 800 0Á42 170 13Á33 100 0Á59 1 072 10Á72
10± 1700 7Á26 700 0Á41 160 12Á55 100 0Á62 990 9Á90
15± 1900 8Á12 2 000 1Á05 120 9Á41 180 1Á50 876 8Á76
20± 1700 7Á26 1 700 1Á00 100 7Á84 190 1Á90 755 7Á55
25± 1500 6Á41 1 400 0Á93 80 6Á27 160 2Á00 634 6Á34
30± 1500 6Á41 1 700 1Á13 70 5Á49 170 2Á43 595 5Á95
35± 1500 6Á41 2 700 1Á80 65 5Á10 200 3Á08 576 5Á76
40± 1600 6Á84 4 800 3Á00 65 5Á10 270 4Á15 597 5Á97
45± 1500 6Á41 7 800 5Á20 60 4Á71 370 6Á17 556 5Á56
50± 1500 6Á41 14 200 9Á47 55 4Á31 530 9Á64 536 5Á36
55± 1500 6Á41 23 800 15Á87 40 3Á14 690 17Á25 478 4Á78
60± 1300 5Á56 34 900 26Á85 30 2Á35 880 29Á33 396 3Á96
65± 900 3Á85 40 700 45Á22 30 2Á35 1500 50Á00 310 3Á10
70± 600 2Á56 42 000 70Á00 20 1Á57 1520 76Á00 207 2Á07
75±
700 2Á99 98 100
140Á14
25 1Á96 4100
164Á00
248 2Á48
Total 23 400 99Á99 287 300 1275 99Á99 15 060 10000 100Á00
Crude rate 12Á28 11Á81
(a) Standardization by population A
Expected deaths 287 300 365 815
Standardized rate 12Á28 15Á63
(b) Standardization by population B
Expected deaths 10 242 15 060
Standardized rate 8Á03 11Á81

(c) Standardization by population C
Expected deaths 101 657 137 338
Standardized rate 10Á17 13Á73
664 Statistical methods in epidemiology
want to compare one SMR with another using the same standard population; in
any case the standard population will often be much larger than the special
population, and var(P
i
) will be much smaller than var(p
i
)). This gives
varM

n
i
p
i
q
i


n
i
P
i

2
: 19:10
As usual, if the p
i

are small, q
i
9 1 and
varM9

r
i


n
i
P
i

2
: 19:11
Confidence limits for M constructed using (19.11) are equivalent to method 3
of §5.2 (p. 154). Where the total number of deaths,

r
i
, is small, this is
unsatisfactory and either the better approximations of methods 1 or 2 or exact
limits should be used (see Example 5.3).
If the purpose of calculating var(M) is to see whether M differs significantly
from unity, var(r
i
) could be taken as n
i
P

i
Q
i
, on the assumption that p
i
differs
from a population value P
i
by sampling fluctuations. If again the P
i
are small,
Q
i
9 1, we have
varM9

n
i
P
i


n
i
P
i

2

1


n
i
P
i
, 19:12
the reciprocal of the total expected deaths. Denoting the numerator and
denominator of (19.9) by O and E (for `observed' and `expected'), an approx-
imate significance test would be to regard O as following a Poisson distribution
with mean E.IfE is not too small, the normal approximation to the Poisson
leads to the use of O ÀE= E
p
as a standardized normal deviate, or, equiva-
lently, O À E
2
=E as a x
2
1
variate. This is, of course, the familiar formula for a
x
2
1
variate.
Example 19.3
Table 19.2 shows some occupational mortality data, a field in which the SMR is trad-
itionally used. The special population is that of farmers in 1951, aged 20 to 65 years. The
standard population is that of all males in these age groups, whether occupied or retired.
Deaths of farmers over a 5-year period are used to help reduce the sampling errors, and
the observed and expected numbers are expressed on a 5-year basis.
The SMR is

100 M 
1007678
11 005
 69Á8%
and
19.3 Rates and standardization 665
Table 19.2 Mortality of farmers in England and Wales, 1949±53, in comparison with that of the male
population. Source: Registrar General of England and Wales (1958).
(1) (2) (3) (4)
Age
i
Annual death rate
per 100 000, all
males (1949±53)
1
5
P
i
 10
5
Farmers, 1951
census population
n
i
Deaths of farmers
1949±53
r
i
Deaths expected
in 5 years

5 Â1Â2Â10
À5
n
i
P
i
20± 129Á8 8 481 87 55
25± 152Á5 39 729 289 303
35± 280Á4 65 700 733 921
45± 816Á2 73 376 1998 2 994
55±64 2312Á4 58 226 4571 6 732
7678 11 005
varSMR10
4
varM

10
4
7678
11 005
2
from 19:11,
 0Á634,
and
SESMR0Á80%:
The smallness of the standard error (SE) of the SMR in Example 19.3 is
typical of much vital statistical data, and is the reason why sampling errors are
often ignored in this type of work. Indeed, there are problems in the interpreta-
tion of occupational mortality statistics which often overshadow sampling
errors. For example, occupations may be less reliably stated in censuses than in

the registration of deaths, and this may lead to biases in the estimated death rates
for certain occupations. Even if the data are wholly reliable, it is not clear
whether a particularly high or low SMR for a certain occupation reflects a health
risk in that occupation or a tendency for selective groups of people to enter it. In
Example 19.3, for example, the SMR for farmers may be low because farming is
healthy, or because unhealthy people are unlikely to enter farming or are more
likely to leave it. Note also that in the lowest age group there is an excess of
deaths among farmers (87 observed, 55 expected). Any method of standardiza-
tion carries the risk of oversimplification, and the investigator should always
compare age-specific rates to see whether the contrasts between populations vary
greatly with age.
The method of indirect standardization is very similar to that described as the
comparison of observed and expected frequencies on p. 520. Indeed if, in the
666 Statistical methods in epidemiology
comparison of two groups, A and B, the standard population were defined as the
pooled population A B, the method would be precisely the same as that used in
the Cochran±Mantel±Haenszel method (p. 520). We have seen (p. 662) that
Cochran's test is equivalent to a comparison of two direct standardized rates.
There is thus a very close relationship between the direct and indirect methods
when the standard population is chosen to be the sum of the two special
populations.
The SMR is a weighted mean, over the separate age groups, of the ratios of
the observed death rates in the special population to those in the standard
population, with weights (n
i
P
i
) that depend on the age distribution of the
special population. This means that SMRs calculated for several special popula-
tions are not strictly comparable (Yule, 1934), since they have been calculated

with different weights. The SMRs will be comparable under the hypothesis that
the ratio of the death rates in the special and standard populations is indepen-
dent of ageÐthat is, in a proportional-hazards situation (§17.8).
The relationship between standardization and generalized linear models is
discussed by Breslow and Day (1975), Little and Pullum (1979) and Freeman and
Holford (1980).
19.4 Surveys to investigate associations
A question commonly asked in epidemiological investigations into the aetiology
of disease is whether some manifestation of ill health is associated with certain
personal characteristics or habits, with particular aspects of the environment in
which a person has lived or worked, or with certain experiences which a person
has undergone. Examples of such questions are the following.
1 Is the risk of death from lung cancer related to the degree of cigarette
smoking, whether current or in previous years?
2 Is the risk that a child dies from acute leukaemia related to whether or not the
mother experienced irradiation during pregnancy?
3 Is the risk of incurring a certain illness increased for individuals who were
treated with a particular drug during a previous illness?
Sometimes questions like these can be answered by controlled experiment-
ation in which the presumptive personal factor can be administered or withheld
at the investigator's discretion; in example 3, for instance, it might be
possible for the investigator to give the drug in question to some patients and
not to others and to compare the outcomes. In such cases the questions are
concerned with causative effects: `Is this drug a partial cause of this illness?' Most
often, however, the experimental approach is out of the question. The investi-
gator must then be satisfied to observe whether there is an association between
factor and disease, and to take the risk which was emphasized in §7.1 if he or she
wishes to infer a causative link.
19.4 Surveys to investigate associations 667
These questions, then, will usually be studied by surveys rather than by

experiments. The precise population to be surveyed is not usually of primary
interest here. One reason is that in epidemiological surveys it is usually admin-
istratively impossible to study a national or regional population, even on a
sample basis. The investigator may, however, have facilities to study a particular
occupational group or a population geographically related to a particular med-
ical centre. Secondly, although the mean values or relative frequencies of the
different variables may vary somewhat from one population to another, the
magnitude and direction of the associations between variables are unlikely to
vary greatly between, say, different occupational groups or different geograph-
ical populations.
There are two main designs for aetiological surveysÐthe case±control study,
sometimes known as a case±referent study, and the cohort study. In a case±
control study a group of individuals affected by the disease in question is
compared with a control group of unaffected individuals. Information is
obtained, usually in a retrospective way, about the frequency in each group of
the various environmental or personal factors which might be associated with the
disease. This type of survey is convenient in the study of rare conditions which
would appear too seldom in a random population sample. By starting with a
group of affected individuals one is effectively taking a much higher sampling
fraction of the cases than of the controls. The method is appropriate also when
the classification by disease is simple (particularly for a dichotomous classifica-
tion into the presence or absence of a specific condition), but in which many
possible aetiological factors have to be studied. A further advantage of the
method is that, by means of the retrospective enquiry, the relevant information
can be obtained comparatively quickly.
In a cohort study a population of individuals, selected usually by geograph-
ical or occupational criteria rather than on medical grounds, is studied either by
complete enumeration or by a representative sample. The population is classified
by the factor or factors of interest and followed prospectively in time so that the
rates of occurrence of various manifestations of disease can be observed and

related to the classifications by aetiological factors. The prospective nature of the
cohort study means that it will normally extend longer in time than the case±
control study and is likely to be administratively more complex. The correspond-
ing advantages are that many medical conditions can be studied simultaneously
and that direct information is obtained about the health of each subject through
an interval of time.
Case±control and cohort studies are often called, respectively, retrospective
and prospective studies. These latter terms are usually appropriate, but the
nomenclature may occasionally be misleading since a cohort study may be
based entirely on retrospective records. For example, if medical records are
available of workers in a certain factory for the past 30 years, a cohort study
668 Statistical methods in epidemiology
may relate to workers employed 30 years ago and be based on records of their
health in the succeeding 30 years. Such a study is sometimes called a historical
prospective study.
A central problem in a case±control study is the method by which the
controls are chosen. Ideally, they should be on average similar to the cases in
all respects except in the medical condition under study and in associated
aetiological factors. Cases will often be selected from one or more hospitals
and will then share the characteristics of the population using those hospitals,
such as social and environmental conditions or ethnic features. It will usually be
desirable to select the control group from the same area or areas, perhaps even
from the same hospitals, but suffering from quite different illnesses unlikely to
share the same aetiological factors. Further, the frequencies with which various
factors are found will usually vary with age and sex. Comparisons between the
case and control groups must, therefore, take account of any differences there
may be in the age and sex distributions of the two groups. Such adjustments are
commonly avoided by arranging that each affected individual is paired with a
control individual who is deliberately chosen to be of the same age and sex and to
share any other demographic features which may be thought to be similarly

relevant.
The remarks made in §19.2 about non-sampling errors, particularly those
about non-response, are also relevant in aetiological surveys. Non-responses are
always a potential danger and every attempt should be made to reduce them to as
low a proportion as possible.
Example 19.4
Doll and Hill (1950) reported the results of a retrospective study of the aetiology of lung
cancer. A group of 709 patients with carcinoma of the lung in 20 hospitals was compared
with a control group of 709 patients without carcinoma of the lung and a third group of
637 patients with carcinoma of the stomach, colon or rectum. For each patient with lung
cancer a control patient was selected from the same hospital, of the same sex and within
the same 5-year age group. Each patient in each group was interviewed by a social worker,
all interviewers using the same questionnaire.
The only substantial differences between the case and control groups were in their
reported smoking habits. Some of the findings are summarized in Table 19.3. The
difference in the proportion of non-smokers in the two groups is clearly significant, at
any rate for males. (If a significance test for data of this form were required, an appro-
priate method would be the test for the difference of two paired proportions, described in
§4.5.) The group of patients with other forms of cancer had similar smoking histories to
those of the control group and differed markedly from the lung cancer group. The
comparisons involving this third group are more complicated because the individual
patients were not paired with members of the lung cancer or control groups and had a
somewhat different age distribution. The possible effect of age had to be allowed for by
methods of age standardization (see §19.3).
19.4 Surveys to investigate associations 669
Table 19.3 Recent tobacco consumption of patients with carcinoma of the lung and control patients
without carcinoma of the lung (Doll and Hill, 1950).
Daily consumption of cigarettes
Non-smoker 1± 5± 15± 25± 50± Total
Male

Lung carcinoma 2 33 250 196 136 32 649
Control 27 55 293 190 71 13 649
Female
Lung carcinoma 19 7 19 9 6 0 60
Control 32 12 10 6 0 0 60
This paper by Doll and Hill is an excellent illustration of the care which should be
taken to avoid bias due to unsuspected differences between case and control groups or to
different standards of data recording. This study, and many others like it, strongly suggest
an association between smoking and the risk of incurring lung cancer. In such retro-
spective studies, however, there is room for argument about the propriety of a particular
choice of control group, little information is obtained about the time relationships
involved, and nothing is known about the association between smoking and diseases
other than those selected for study. Doll and Hill (1954, 1956, 1964) carried out a cohort
study prospectively by sending questionnaires to all the 59 600 doctors in the UK in
October 1951. Adequate replies were received from 68Á2% of the population (34 439
men and 6194 women). The male doctors were followed for 40 years and notifications
of deaths from various causes were obtained, only 148 being untraced (Doll et al., 1994).
Some results are shown in Table 19.4. The groups defined by different smoking categories
have different age distributions, and the death rates shown in the table have again been
standardized for age (§19.3). Cigarette smoking is again shown to be associated with a
sharp increase in the death rate from lung cancer, there is almost as strong an association
for chronic obstructive lung disease, and a relatively weak association with the death rates
from ischaemic heart disease.
This prospective study provides strong evidence that the association between smoking
and lung cancer is causative. In addition to the data in Table 19.4, many doctors who
smoked at the outset of the study stopped smoking during the follow-up period, and by
1971 doctors were smoking less than half as much as people of the same ages in the general
population (Doll & Peto, 1976). This reduction in smoking was matched by a steady
decline in the death rate from lung cancer for the whole group of male doctors (age-
standardized, and expressed as a fraction of the national mortality rate) over the first 20

years of follow-up.
In a cohort study in which the incidence of a specific disease is of particular
interest, the case±control approach may be adopted by analysing the data of all
the cases and a control group of randomly selected non-cases. This approach was
termed a synthetic retrospective study by Mantel (1973). Often the controls are
670 Statistical methods in epidemiology
Table 19.4 Standardized annual death rates among male doctors for three causes of death, 1951±91,
related to smoking habits (Doll et al., 1994).
Standardized death rate per 100 000 men
Number
of deaths
Non-
smokers Ex-smokers
Current
smokers
Cigarette smokers (cigarettes per day)
1±14 15±24 25±
Lung cancer 893 14 58 209 105 208 355
Chronic
obstructive
lung disease 542 10 57 127 86 112 225
Ischaemic heart
disease 6438 572 678 892 802 892 1025
chosen matched for each case by random sampling from the members of the
cohort who are non-cases at the time that the case developed the disease (Liddell
et al., 1977), and this is usually referred to as a nested case±control study. Care
may be needed to avoid the repeated selection of the same individuals as controls
for more than one case (Robins et al., 1989). A related design is the case±cohort
study, which consists of a random sample of the whole cohort; some members of
this sample will become cases and they are supplemented by the cases that occur

in the remainder of the cohort, with the non-cases in the random subcohort
serving as controls for the total set of cases (Kupper et al., 1975; Prentice, 1986).
These designs are useful in situations where it is expensive to extract the whole
data, or when expensive tests are required; if material, such as blood samples, can
be stored and then analysed for only a fraction of the cohort, then there may be a
large saving in resources with very little loss of efficiency.
The measurement of the degree of association between the risk of disease and
the presence of an aetiological factor is discussed in detail in the next section.
19.5 Relative risk
Cohort and case±control methods for studying the aetiology of disease were
discussed in the previous section. In such studies it is usual to make comparisons
between groups with different characteristics, in particular between a group of
individuals exposed to some factor and a group not exposed. A measure of the
increased risk (if any) of contracting a particular disease in the exposed com-
pared with the non-exposed is required. The measure usually used is the ratio of
the incidences in the groups being compared and is referred to as relative risk (f).
Thus,
f  I
E
=I
NE
, 19:13
19.5 Relative risk 671
where I
E
and I
NE
are the incidence rates in the exposed and non-exposed,
respectively. This measure may also be referred to as the risk ratio.
In a cohort study the relative risk can be estimated directly, since estimates

are available of both I
E
and I
NE
. In a case±control study the relative risk cannot
be estimated directly since neither I
E
nor I
NE
can be estimated, and we now
consider how to obtain a useful solution.
Suppose that each subject in a large population has been classified as positive
or negative according to some potential aetiological factor, and positive or
negative according to some disease state. The factor might be based on a current
classification or (more usually in a retrospective study) on the subject's past
history. The disease state may refer to the presence or absence of a certain
category of disease at a particular instant, or to a certain occurrence (such as
diagnosis or death) during a stated periodÐthat is, to prevalence and incidence,
respectively.
For any such categorization the population may be enumerated in a 2 Â 2
table, as follows. The entries in the table are proportions of the total population.
Disease
À
 P
1
P
3
P
1
 P

3
Factor
À P
2
P
4
P
2
 P
4
P
1
 P
2
P
3
 P
4
1
19:14
If these proportions were known, the association between the factor and the
disease could be measured by the ratio of the risks of being disease-positive for
those with and those without the factor.
Risk ratio 
P
1
P
1
 P
3


Ä
P
2
P
2
 P
4


P
1
P
2
 P
4

P
2
P
1
 P
3

:
19:15
Where the cases are incident cases the risk ratio is the relative risk.
Now, in many (although not all) situations in which aetiological studies are
done, the proportion of subjects classified as disease-positive will be small. That
is, P

1
will be small in comparison with P
3
, and P
2
will be small in comparison
with P
4
. In such a case, (19.15) will be very nearly equal to
672 Statistical methods in epidemiology
P
1
P
3
Ä
P
2
P
4

P
1
P
4
P
2
P
3
 c, say: 19:16
The ratio (19.16) is properly called the odds ratio (because it is the ratio of P

1
=P
3
to P
2
=P
4
, and these two quantities can be thought of as odds in favour of having
the disease), but it is often referred to as approximate relative risk (because of the
approximation referred to above) or simply as relative risk. Another term is
cross-ratio (because the two products P
1
P
4
and P
2
P
3
which appear in (19.16) are
obtained by multiplying diagonally across the table).
The odds ratio (19.16) could be estimated from a random sample of the
population, or from a sample stratified by the two levels of the factor (such as
a prospective cohort study started some time before the disease assessments are
made). It could also be estimated from a sample stratified by the two disease
states (i.e. from a case±control study), and it is this fact which makes it such a
useful measure of relative risk. Suppose a case±control study is carried out by
selecting separate random samples of diseased and non-diseased individuals, and
that the frequencies (not proportions) are as follows, using the notation of §4.5:
Disease
À

casescontrols
Factor
 aca c
À bdb d
a bc dn
19:17
Frequently, of course, the sampling plan will lead to equal numbers of cases and
controls; then a b  c d 
1
2
n. Now, a=b can be regarded as a reasonable
estimate of P
1
=P
2
, and c=d similarly estimates P
3
=P
4
. The observed odds ratio,
^
c 
ad
bc
, 19:18
is the ratio of a=b to c=d, and therefore can be taken as an estimate of
P
1
P
2

Ä
P
3
P
4

P
1
P
4
P
2
P
3
 c , 19:19
the population odds ratio or approximate relative risk defined by (19.16).
The assumption that the case and control groups are random samples from
the same relevant population group is difficult to satisfy in case±control studies.
Nevertheless, the estimates of relative risk derived from case±control
studies often agree quite well with those obtained from corroborative cohort
studies, and the theory seems likely to be useful as a rough guide. In retrospective
19.5 Relative risk 673
studies, cases are often matched with control individuals for various factors; the
effect of this matching is discussed below.
Equation (19.18) is identical to (4.25), and the sampling variation of an odds
ratio is best considered on the logarithmic scale, as in (4.26), so that approximate
limits, known as the logit limits, can be obtained, as in Example 4.11. If any of
the cell frequencies are small, more complex methods, as discussed in §4.5, must
be used. Apart from exact limits (Baptista & Pike, 1977), the limits due to
Cornfield (1956) are the most satisfactory (see (4.27) to (4.29)).

Example 19.5
In a case±control study of women with breast cancer (Ellery et al., 1986), the data on
whether oral contraceptives were used before first full-term pregnancy were:
Cases Controls
OC before FFTP
Yes 4 11 15
No 63 107 170
67 118 185
Proceeding as in Example 4.11, the estimated odds ratio is 0Á62 with 95% logit limits of
0Á19 and 2Á02. Using the notation of (4.27) to (4.29), the upper Cornfield limit is for
A  7Á62. Substituting this value in (4.28) gives c
U
 1Á92, from (4.29) var(a;
c  1Á923Á417, and evaluating (4.27) gives À1Á96. The lower limit was found for
A  1Á66, giving c
L
 0Á20. Therefore the Cornfield limits are 0Á20 and 1Á92.
Frequently an estimate of relative risk is made from each of a number of
subsets of the data, and there is some interest in the comparison and combin-
ation of these different estimates. There may, for example, be several studies of
the same aetiological problem done at different times and places, or, in any one
study, the data may have been subdivided into one or more categories, such as
age groups, which affect the relative proportions in the rows of the 2 Â2 table or
in the columns or in both rows and columns. One approach, illustrated in
Example 19.6 below, is to take the separate estimates of ln
^
c and weight them
by the reciprocal of the sampling variance (4.26). The estimates can then be
combined by taking a weighted mean, and they can be tested for heterogeneity by
a x

2
index like (8.15) (Woolf, 1955). This method breaks down when the subsets
contain few subjects and therefore becomes unsuitable with increasing stratifica-
tion of a data set. Although in these circumstances the method may be improved
by adding
1
2
to each observed frequency, it is preferable to use an alternative
method of combination due to Mantel and Haenszel (1959). For many
situations this method gives similar results to the method of Woolf, but the
674 Statistical methods in epidemiology
Mantel±Haenszel method is more robust when some of the strata contain small
frequencies; in particular, it may still be used without modification when some of
the frequencies are zero. The method was introduced in §15.6 as a significance
test. We now give further details from the viewpoint of estimation. Denote the
frequencies in the 2 Â 2 table for the ith subdivision by the notation of (19.17)
with subscript i. The Mantel±Haenszel pooled estimate of c is then
R
MH


a
i
d
i
=n
i


b

i
c
i
=n
i

: 19:20
Mantel and Haenszel gave a significance test of the hypothesis that c  1. If
there were no association between the factor and the disease, the expected value
and the variance of a
i
would, as in (15.18) and (17.12), be given by
Ea
i

a
i
 b
i
a
i
 c
i

n
i
,
vara
i


a
i
 b
i
c
i
 d
i
a
i
 c
i
b
i
 d
i

n
2
i
n
i
À 1
W
b
b
a
b
b
Y

: 19:21
The test is calculated by adding the differences between the observed and
expected values of a
i
over the subsets. Since these subsets are independent, the
variance of the sum of differences is equal to the sum of the separate variances.
This gives as a test statistic
X
2
MH



a
i
À

Ea
i

2

vara
i

, 19:22
which is approximately a x
2
1
(see (15.20)). If desired, a continuity correction

may be included.
A number of options are now available for estimating the variance of R
MH
,
and hence constructing confidence limits. First, using the method proposed by
Miettinen (1976), test-based confidence limits may be constructed. If the stand-
ard error of ln R
MH
were known, then, under normal theory, a test statistic of the
hypothesis c  1 ln c  0) would be
z  ln R
MH
=SEln R
MH
,
taken as an approximate standardized normal deviate. The test statistic X
2
MH
is
approximately a x
2
1
, and taking the square root gives an approximate standar-
dized normal deviate (§5.1). The test-based method consists of equating these
two test statistics to give an estimate of SE(ln R
MH
). That is,
SEln R
MH
ln R

MH
=X
MH
: 19:23
This method is strictly only valid if c  1, but in practice gives reasonable
results provided R
MH
is not extreme (see Breslow & Day (1980, §4.3), who
19.5 Relative risk 675
recommend using X
MH
calculated without the continuity correction for this
purpose). Unfortunately, the method breaks down if R
MH
 1. The calculations
are illustrated in Example 19.6.
The most satisfactory method was proposed by Robins et al. (1986). This
method is suitable when a large data set is subdivided into many strata, some
containing small frequencies, as well as when there are only a few strata, none
containing small frequencies. Using their notation,
P
i
a
i
 d
i
=n
i
, Q
i

b
i
 c
i
=n
i
,
R
i
 a
i
d
i
=n
i
, S
i
 b
i
c
i
=n
i
, R



R
i
and

S



S
i
so that R
MH
 R

=S

;
then
varln R
MH


P
i
R
i
2R
2



P
i
S

i
 Q
i
R
i

2R

S



Q
i
S
i
2S
2

: 19:24
Breslow and Day (1980, §4.4) set out a method for testing the homogeneity of
the odds ratio over the strata. However, like the method of Woolf discussed
above, the method breaks down with increasing stratification.
A special case of subdivision occurs in case±control studies, in which each
case is matched with a control subject for certain important factors, such as age,
sex, residence, etc. Strictly, each pair of matched subjects should form a subdi-
vision for the calculation of relative risk, although, of course, the individual
estimates from such pairs would be valueless. The Mantel±Haenszel pooled
estimate (19.20) can, however, be calculated, and takes a particularly simple
form. Suppose there are altogether

1
2
n matched pairs. These can be entered into
a2Â2 table according to whether the two individuals are factor-positive or
factor-negative, with frequencies as follows:
Control
Factor  Factor À
Case
Factor  tra
Factor À sub
cd
1
2
n
19:25
The marginal totals in (19.25) are the cell frequencies in the earlier table (19.17).
The Mantel±Haenszel estimate is then
676 Statistical methods in epidemiology
R 
r
s
: 19:26
This can be shown to be a particularly satisfactory estimate if the true relative risk,
as measured by the cross-ratio of the probabilities (19.16), is the same for every
pair. The Mantel±Haenszel test statistic is identical to that of McNemar's test
(4.17).
Inferences are made by treating r as a binomial variable with sample size
r  s. The methods of §4.4 may then be applied and the confidence limits of the
relative risk, c
L

and c
U
, obtained from those of the binomial parameter p, using
the relation
c 
p
1 Àp
:
Liddell (1983) showed that the limits given by (4.16) simplify after the above
transformation to give
c
L

r
s 1F
0Á025, 2s 1, 2r
c
U

r 1F
0Á025, 2r 1, 2s
s
W
b
b
a
b
b
Y
, 19:27

and that an exact test of c  1 is given by
F 
r
s  1
, 19:28
tested against the F distribution with 2(s  1) and 2r degrees of freedom (in this
formulation, if r < s, r and s should be interchanged). This exact test may be used
instead of the approximate McNemar test (§4.5).
A general point is that the logarithm of c is, from (19.16),
lnP
1
=P
3
ÀlnP
2
=P
4
logit probability of disease when factor 
À logit probability of disease when factor À:
The methods of analysis suggested in this section can thus be seen to be par-
ticularly appropriate if the effect of changing from factor  to factor À is to
change the probability of being in the diseased state by a constant amount on the
logit scale. It has been indicated in §14.2 that this is a reasonable general
approach to a wide range of problems, but in any particular instance it may be
far from true. The investigator should therefore guard against too ready an
assumption that a relative risk calculated in one study is necessarily applicable
under somewhat different circumstances.
Example 19.6 uses the above methods to combine a number of studies into a
summary analysis. It may be regarded as a simple example of meta-analysis
(§18.10).

19.5 Relative risk 677
Example 19.6
Table 19.5 summarizes results from 10 retrospective surveys in which patients with lung
cancer and control subjects were classified as smokers or non-smokers. In most or all of
these surveys, cases and controls would have been matched, but the original data are
usually not presented in sufficient detail to enable relative risks to be estimated from
(19.26) and matching is ignored in the present analysis. (The effect of ignoring matching
when it is present is, if anything, to underestimate the departure of the relative risk from
unity.) The data were compiled by Cornfield (1956) and have been referred to also by Gart
(1962).
Defining w
i
as the reciprocal of var(ln
^
c
i
) from (4.26), the weighted mean is

w
i
ln
^
c
i

w
i

161Á36
105Á4

 1Á531,
and the pooled estimate of c is exp(1Á531)  4Á62.
For the heterogeneity test (8.15), the x
2
9
statistic is

w
i
ln
^
c
i

2
À


w
i
ln
^
c
i

2

w
i
 253Á678 À247Á061  6Á62 P  0Á68:

There is no strong evidence of heterogeneity between separate estimates. It is, of course,
likely that the relative risk varies to some extent from study to study, particularly as the
factor `smoking' covers such a wide range of activity. However, the sampling variation of
the separate estimates is evidently too large to enable such real variation to emerge. If we
assume that all the variation is due to sampling error, the variance of the weighted mean
of ln
^
c
i
can be obtained as
1

w
i
 0Á00949:
Approximate 95% confidence limits for ln c are
1Á531 Æ1Á96 0Á00949
p
 1Á340 and 1Á722:
The corresponding limits for c are obtained by exponentials as 3Á82 and 5Á60.
The Mantel±Haenszel estimator of c is
R
MH

302Á840
64Á687
 4Á68:
The statistic for testing that this estimate differs from unity is
X
2

MH
3793 À 3554Á85
2
=193Á17
 293Á60 P < 0Á001:
The test-based method of calculating confidence limits from (19.23) gives
SEln R
MH
ln4Á68= 293Á60
p
 1Á543=17Á13
 0Á0901,
and approximate 95% confidence limits for ln c are
678 Statistical methods in epidemiology