Sufficient-component cause model of causation. Rothman KJ, Greenland S, Poole C, Lash TL.
Chapter 2: Causation and Causal Inference. Modern Epidemiology: 2008.
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Sufficient-component cause model of causality.
 Cause = an antecedent event, condition, or characteristic that was necessary for
the occurrence of the disease at the moment it occurred, given that other
conditions are fixed.
 Cause – precedes disease onset; had the event been different, the disease would
not have occurred or would have been delayed.
 Sufficient cause = a complete causal mechanism, a minimum set of conditions
and events that are sufficient for the outcome to occur (e.g.: breaking a hip in
the Winter when attempting to navigate an unclear path with poor footwear and
no handrail).
 U = unknown = may depict a component of a sufficient cause.
 Each component is a necessary and sufficient part of a sufficient cause. But
necessary cause = a component cause that that appears in every sufficient cause
(e.g.: having a hip to fracture).
 Causes are relative states (need a referent). This model is suited for analyzing
events vs non-events.
 Not a mechanistic model – all causes made equal.
 Alerts to causal interactions but not to mediated effects.
 Deterministic model viewing chance as U.
Risk = probability
 Relative frequency, repeated sampling. Individual risk bounded to be = 1 or 0.
 Tendency of an entity to produce an event.
 Subjective degree of certainty.
Sufficient-component cause – strength of effects
 If measured as the difference in incidence proportions, depends on the
prevalence of the factor’s causal complements.
 If measured as a ratio, depends additionally on the prevalence of sufficient
causes in which the causal factor does not play a role (if many people have other
sufficient causes, the baseline incidence proportion will be high and the
proportion getting disease due to E will be comparatively low.)
Sufficient-component cause – interactions
 Two component causes acting in the same sufficient cause may be defined as
interacting causally to produce disease.
Etiologic fraction
 Each case etiologically attributable to a given factor can also be attributed to the
other component causes in the sufficient causes in which the factor acts.
 Mistake etiologic fractions sum to 1 – a single necessary cause alone would be
responsible for 100% of all causes.
 All component causes of a sufficient cause interact. E.g.: Yellow shanks – require
strain of fowl and diet of corn. Folly to think of the condition as either genetic
(farmer with 2 strains, all fed corn) or environmental (farmer with 1 strain, some
fed corn). Every case can be attributed to both genes and environment so that
the etiologic fractions sum to > 100%.
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Induction time = time from causal action to irreversible disease occurrence (once A
occurs, time to completion of a sufficient cause involving A).
Latent time = time from disease occurrence to disease detection.
A history of scientific inference. Rothman KJ, Greenland S, Poole C, Lash TL. Chapter 2: Causation
and Causal Inference. Modern Epidemiology: 2008.
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Inductivism – Bacon, Novum Organum, 1620 (e.g.) – generalizations from observations.
Formation of natural laws. Also JS Mill, 1862.
Hume – inductive arguments carry no logical force. Why should we extend that
experience beyond those particular instances, when our perception is not of causal
connections, but merely of a series of events?
Bertrand Russell – example – 2 accurate clocks perpetually chiming hourly, one slightly
ahead of the other.
Post hoc ergo propter hoc and, more generally, the fallacy of affirming the consequent: If
H is true, B is true; B is true, therefore H is true.
Refutationism – logical positivists – nonidentification or underdetermination of theories
by observations – available observations are always consistent with several hypotheses
that are mutually inconsistent – we can never prove a hypothesis.
Popper – science advances by a process of elimination – conjecture and refutation.
Repeated observations do not induce a natural law, but only the belief that one has been
found. But induction plays a legitimate role in hypothesis formation. Good science =
multiplicity of ideas, cycle of induction and falsification.
However – observations are laden with theory – can never provide definitive refutation
(Duhem-Quine thesis).
Consensus and naturalism – Kuhn – role of the scientific community.Paradigm – normal
science – accumulation of anomalies – paradigm shift.
Bayesianism – other inferential activities besides hypothesis evaluation (e.g.: prediction,
control) – deductive argument can provide no information about truth or falsity of a
hypothesis unless you can be certain of the premises – even deduction has limited utility!
But if you can assign a degree of certainty oto the premises of the argument, you may
use any and all the rules of probability theory to derive a certainty for the conlcuions, and
this certainty will be a logically valid consequence of your original certainties.
Causal criteria. Rothman KJ, Greenland S, Poole C, Lash TL. Chapter 2: Causation and Causal
Inference. Modern Epidemiology: 2008.
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Hill’s postulates (Sir Austin Bradford Hill, 1965). ACCESS-PTB
Analogy – E.g.: reasoning by analogy from thalidomide may make it appear more likely
that other drugs may produce inadvertent harms.
Consistency – Repeated observations in different populations under different
circumstances. Criticism: Circumstances and populations have different characteristics
which may affect the association.
Coherence – Causal interpretation does not conflict with what is known about the natural
history and biology of disease. Body of evidence is coherent between domains
(triangulation). Criticism: Lack of coherence may not falsify the hypothesis.
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Experimental evidence – Evidence obtained from reducing or eliminating an exposure
and seeking a change in disease. Criticism: secular effects. Also, exposure may merely be
a surrogate.
Strength – Stronger > weaker associations. Criticisms: Counter examples.
Specificity – one cause leads to a single effect, one effect has a single cause. Counter
example: Smoking and cancer.
Plausibility. Criticism: May vary with times.
Temporality – inarguable requirement, sine qua non, but lack of temporality does not
refute causation, merely refutes causation in the specific instance observed.
Biologic gradient = Does response curve. Strong = linear, weaker = monotonic. Counterexample: J-shaped relationship, glycemia and death.
Ultimately, causal inference is a subjective matter of degree of personal belief.
Greenland S, Rothman KJ. Chapter 3: Measures of Occurrence. Modern Epidemiology: 2008.
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Epidemiology = the study of the distribution and determinants of disease frequency in
human populations. Focus on population distributions. Must obtain valid and precise
estimates of the effect of a potential cause on the occurrence of disease – must be able
to measure disease occurrence.
Types of population
 Closed population – adds no new members, loses members only to death.
 Open population – may gain new members who did not initially qualify for it over
time (immigration or birth), or lose living members through emigration.
 Closed versus open depends on the time axis. E.g.: all persons who ever used a
particular drug is an open population on calendar time, but closed on time from
drug use.
 Any study with LTFU = open. Sometimes called “closed on the left”.
 Population
 Cohort = a group of persons for whom membership is defined in a permanent
fashion, or a population in which membership is determined entirely by a single
defining event.
 Steady state – number of people entering is balanced by the number of people
exiting. AKA stationary.
 Stronger form of steady state – no immigration or emigration, deaths balanced
by births.
Incidence times
 E.g.: Death – 100% for everyone?
 Time is measured relative to a reference event – the zero time.
 Incidence time = time span from zero time to the time of event.
 Time is undefined if person never experiences the event – convention –
censoring – assumed that the incidence time is unspecified but greater than the
time of censoring. Censoring complicates incidence time analyses – go to rates.
 Average age at death not equal to life expectancy.
Incidence rates
 Person time = length of time each individual was in the population at risk – event
was a possibility and would have been counted as an event, if it had occurred.
 I = A / T, where T = total person time.
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Nbar = average size of the population = T/ tdelta, where tdelta = length of the risk
period.
 Incidence rate ignores distinction between individuals who do not contribute
because they were in the population only briefly, and those who do not
contribute because they were in the population for a long time but never got
disease.
 Unit = reciprocal time. Time unit chosen to ensure that the minimum rate has at
least one digit left of the decimal.
 Closed population – outcome = death – reciprocal of death rate is the average
death time.
 Stationary population with no migration – reciprocal of crude incidence rate of
inevevitable outcome (e.g.: death) = average time spent in the population until
outcome = waiting time = incidence time from population entry.
 Competing risk – requires modification of these relations.
 With migration – average age at death does not equal life expectancy due to
addition of younger individuals. Waiting time to death will be overestimated as
well.
Incidence proportions
 Defined for a closed population.
 R = A/N, where N is the population at the beginning of observation.
 S = 1-R = (N-A)/N.
 R/S = incidence odds.
 When R is small, S = 1 (approx.) and R/S = R.
 When R is small, Naverage = N (approx.) and I = A/(N*tdelta) (Usually denominator
requires sum of T for each individual).
 R = A/N = (A/(N*tdelta) * tdelta ~ I * tdelta when R < 0.10.
 R ~ R/S when R <0.10.
 These relations can be made valid by making t(delta) so short that no more than
one person leaves the population over the interval. The analysis of death rate for
a closed population within successive small age or time intervals is life-table
methodology.
Prevalence
 The proportion of a poulation in a state at a given time.
 Prevalence pool = subset of the population in the given state.
 Prevalence reflects both incidence and duration of disease, an is misleading in
etiologic research.
 E.g.: better survival from a chronic disease leads to higher prevalence –
misconstrue therapy as causative.
 Required for congenital malformations – most malformed embryos are not
carried to term and are undetectable.
 Assume stationary population – inflow to prevalence pool = outflow.
 Assume no migration – Inflow over tdelta = incidence proportion time the number
of susceptible patients = I * (N – P) * tdelta
 Outflow = I’ * P * tdelta.
 I’ defined as the incidence rate of outflow. In a stationary population without
migration, the reciprocal of I’ is waiting time with disease (disease duration).
 Then P / (N-P) = prevalence odds = I * D.
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Relationships between incidence times, rates, and proportions in a closed population
with an inevitable outcome and a small number of events relative to the number at risk.
 Product limit formula
 S = product [(Nk – Ak) / Nk]
 Relates overall incidence proportion from sub-interval proportions.
 Incidence proportions defined only for closed populations. However,
incidence proportion of a left-closed population may be calculated as the
product of incidence proportions of sub-intervals in which the population
may be considered closed. Allows proportions to be calculated for open
populations.
 Exponential formula
 Ik = Ak / (Nk * tdelta) (Using the rare outcomes assumption, otherwise
denominator is the sum of T for each individual).
 Then sk = 1 – R = 1 – Ik*tdelta (k).
 Substitute into product limit formula.
 Note that 1-x = exp(-x) when x is small.
 Then the exponential formula is:
 S = exp (- sum[Ik*tdelta (k)).
 R = 1-S = 1 – exp (- sum[Ik*tdelta (k)).
 Relates overall incidence proportion to incidence rates.
 Often used to translate incidence rates from an open population into
incidence proportions for a closed populations (proportion only defined
for a closed population).
Competing risks
 Complicate proportions as measures of effect – an exposure may affect time at
risk for competing events, thus leading to an increase in the risk of competing
events that is an actual effect of exposure, but one we would like to remove.
 Usually treated with censoring – this assumes that in the absence of the
competing risk (counter-factual), the risk for disease among those removed
would have been equal to those remaining conditional on other known variables.
I.e.: competing risks occur at random, though not necessarily completely at
random.
 This may not be reasonable. E.g.: Fat intake and colon cancer, fatal CHD is a
competing risk. But risk factors for CHD also related to fat. Removal of CHD may
remove subjects with high fat intake and increased risk of colon cancer.
 Also may not be reasonable because lack of the competing risk is counterfactual
– actually removing it may require improved diet and decreased risk of colon
cancer, so treating the risk as equal may overestimate the true risk if disease had
been removed.
Greenland S, Rothman KJ, Lash TL. Chapter 4: Measure of effect and measure of association.
Modern Epidemiology: 2008.
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Effect = the change in a population characteristic that is caused by the factor being at one
level versus another (counterfactual) – the change is described as either the absolute or
relative difference in potential outcomes for a given cohort.
Potential-outcome or counterfactual theory of causation
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Counterfactually defined effect measures involve two distinct conditions, only
one of which may actually occur.
 We do not observe the measure of effect directly – we only observe its
components, and only one of them, really.
 For the other component, we need to predict what it would have been. We
observe a cohort we believe is similar to estimate it.
 The result is a measure of association that we hope will equal the measure of
effect.
 A measure of effect compares what would happen to one population under two
possible but distinct conditions, of which at most only one can occur. A measure
of association compares what happens in two distinct populations.
 Confounding occurs when the measure of association is not equal to the
measure of effect.
Rate difference = ID = Ai/T1 – A0/T0.
Risk difference = RD = A1/N1 – A0/N1.
Causal difference in average disease-free time = TD = T1/N1 – T0/N0
Rate ratio = IR = I1 / I0.
Risk ratio = RR = R1 / R0.
Causal ratio of disease-free time = TR = T1/T0.
Odds ratio = OR = (R1/(1-R1))/(R0/(1-R0)).
Prevalence odds ratio = POR = IR if average disease duration is same for those exposed
and those unexposed.
Excess risk = Attributable risk = AR = RD or ID.
Excess relative risk = AR / I0.
Excess fraction = (AR / I0) * 100%.
Attributable fraction = (AR / I1) * 100% = the percent of incidence in the exposed that
would be eliminated if exposure were eliminated.
Population attributable risk = PAR = Ipop – I0 or Rpop – R0 .
Population attributable fraction = (PAR / Ipop) * 100% = the percent of incidence in the
population that would be eliminated if exposure were eliminated.
Etiologic fractions – number or proportion of cases actually caused by an exposure.
Excess fractions probably underestimate the etiologic fraction, since many more cases in
I1 than I1 – I0 may be due to exposure (causal complement of exposure may be completed
before another sufficient cause, but another sufficient cause may be completed anyways,
but later.).
Intervention effect – probably over estimated by excess fractions, because interventions
are rarely effective, or may change the person-time characteristics and invalidate the
estimation.
Relationships among measure of effect
 If R < 0.10, then the size of the population at risk varies little across time and is
equal in exposed and unexposed population, so that it cancels out of the rate
ratio.
 Then RR = IR = OR. RR ~ OR because 1-R is ~ 1 when R < 0.10.
 Relations denote absolute value of the logarithms: Null < RR < OR. This is because
S1 / S0 > 1 (log scale, i.e.: | S1 – S0 | > 0).
 Relations denote absolute value of the logarithms: Null < RR < IR. Analogous
reasoning, where if R1 > R0, then T1 < T0.
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If there is effect-measure heterogeneity, at most, no more than one of the
measure of effect will be homogeneous.
Non-collapsibility
 The overall OR may be more extreme that stratum-specific ORs, because the
overall OR is not a weighted average of stratum-specific ORs.
 Likewise, the IR may also exhibit non-collapsibility. However, the RR is always
collapsible.
Katzmarzyk PT, Ardern CI. Overweight and obesity mortality trends in Canada, 1985-2000.
Canadian Journal of Public Health, 95(1): 2004.
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An alternative way to calculate the population attributable risk is to calculate a weighted
sum of the attributable risk fraction in exposed and unexposed subjects (for the latter it
will be equal to zero), weighted by their respective prevalences in the population.
This formulation is particular useful for multiple exposure levels compared to a common
reference level. Instead of (I1 – Ipop) / Ipop, one is able to substitute (I1 – I0) / I1, and thus
use RRs in the calculation of PAR. However, RRs must be age and sex-adjusted.
Greenland S, Lash TL, Rothman KJ. Chapter 5: Concepts of Interaction. Modern Epidemiology:
2008.
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Statistical interaction = “departure from additivity of effects on the chosen outcome
scale”.
X, Z, Y. Suppose that X and Z have effects on Y, and the RD for one remains constant
across levels of the other. Then there is no statistical interaction on the risk-difference
scale, because the combined effect of X and Z on risk can be computed simply by adding
together the separate risk differences for X and Z. This is lack of statistical effect
modification.
Effect modification is scale-dependent. Homogeneity on the log-risk scale requires effect
modification on the risk difference scale, and vice versa.
Biologic interaction (effect modification, not “effect measure modification”, which is
statistical interaction)
 Possible types defined in table 5-2. E.g.: causal synergism – X and Z together
required for Y = 1. E.g.: causal antagonism – X and Z together cause Y = 0 when
either alone causes Y = 1, and the absence of both causes Y = 0.
 Departures from additivity imply interaction, but additivity does not imply
absence of interaction.
 Super additivity (e.g.: causal synergism) and sub-additivity (e.g.: causal
antagonism).
 Biologic interaction is not identifiable from epidemiologic data.
Oleckno, WA. Chapter 11: Case-control studies. Essential Epidemiology: 2002
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Effect modification occurs when the direction or magnitude of an association varies at
different levels of a third factor.
Effect modification refers to a real effect in the population, while interaction is a
characteristic of the sample data.
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Effect modification vs confounding
 Confounding needs to be controlled – nuisance. Confounding also assumes that
the exposure-outcome effect is constant among levels of the confounder.
 Effect modification is a real effect that needs to be described. The exposureoutcome effect varies among levels of the effect modifier.
 Positive confounding is present when OR(c) > OR(stratum), & OR(stratum) are
equal.
 Negative confounding is present when OR(c) < OR(Stratum), & OR(stratum) are
equal.
 Effect modification is present when OR(stratum) are unequal. Usually the OR(c) is
in between; this will usually need to be, at least initially, a qualitative assessment
because tests may be underpowered. Magnitude matters; qualitative reversal of
association is even better.
 Confounding and effect modification are both present when OR(c) is not equal to
OR(stratum) (either less than or more than, off to one side), and OR(stratum) are
not equal.
 Exceptions: Residual confounding may look like effect modification.
 Exceptions: Non-collapsibility of the OR may look like confounding.
 Reference to Kleinbaum, Kupper, and Morgenstern. Epidemiologic Research:
Principles and Quantitative Methods. Belmont, CA: Lifetime Learning
Publications, 1982.
Protocol: Observe stratum-specific odds ratios. Consider whether effect modification
makes sense. Perform a test of heterogeneity. Report pooled summary values if
appropriate. Effect modification takes priority over confounding in the sequence of
analysis.
Rothman KJ, Greenland S, Lash TL. Chapter 6: Types of epidemiologic studies. Modern
Epidemiology: 2008.
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In laboratory studies, an experiment is a set of observations, conducted under controlled
circumstances, in which the scientist manipulates the conditions to ascertain what effect,
if any, manipulation has on the observations.
Experimental studies in epidemiology – investigator manipulates the exposure assigned
to participants in the study. E.g.: clinical trials, field trials, community intervention trials.
 Randomization – allocation of subjects is unrelated to the extraneous factors that
affect the outcome, so any association produced between treatment allocation
and extraneous factors is random. This process converts the effect of potential
biasing factors into random noise for the purpose of statistical analysis, and is
therefore a fundamental assumption of standard statistical methods which
assume all residual variance is random.
 Quasi-randomization – random allocation that does not meet quality standards
of full randomization (See SR section).
 Ethical problems with randomization – treatment assignment independent of
patient characteristics, therefore designed to assist study validity instead of
patient well-being.
 Ethical problems with experiments – requirement of equipoise may not be met.
 Clinical trial – an experiment with patients as subjects.
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Patient-blinded.
Double-blinded = assessor and patient are blinded to treatment
assignment.
 Triple-blinded = patient, assessor, and individual making the treatment
assignment unaware – alternatively, data analyst unaware.
 Field trial – Subjects are not defined by the presence of disease or by
presentation to clinical care – focus is on initial occurrence of disease. E.g.:
studies of vitamin C to prevent common cold.
 Consider selecting patients to increase R0. But reduces generalizabiltiy.
E.g. MRFIT study – selected high risk patients for AMI. Could also have
looked at patients who had already experienced an AMI.
 Community intervention and cluster randomized trials
 Is the intervention implemented separately for each individual?
 Required for convenience (e.g.: diet and households), or to examine
environmental interventions with widespread effects.
 Cluster-randomization – larger the size of each group (and therefore the
smaller the number of groups) relative to total study size, the less is
accomplished by randomization.
Non-experimental studies
 Unethical for investigators to expose persons to potential causes of disease
simply to learn about etiology. But people do this willingly or unwillingly to
themselves!
 Unable to assign exposure. Must rely on selection of subjects to achieve
comparability between groups and valid treatment of residual variance as
random.
 Gold standard – the natural experiment – e.g.: Snow’s study of cholera in
London, with the water supply of the Southwark and Vauxhall Company (water
pumped from the Thames) geographically intermixed with that of the Lambeth
Company, which had obtained a supply of water free of London sewage by
switching the collection point from opposite Hungerford Market to Thames
Ditton.
 Cohort studies
 Paradigmatic.
 Define two or more groups that vary with respect to the study exposure.
 Case control studies
 Define a source population, which represents a hypothetical study
population in which a cohort study might have been conducted. Identify
a single disease of interest.
 Cases are identified, as per cohort protocol. Exposure status measured.
But denominators not measured – instead, a control group of study
subjects sampled from the source population to estimate the relative
size of the denominators.
 Cardinal rule: Controls must be sampled independently of their exposure
status.
Prospective versus retrospective: Many perspectives. Two highlighted below. Key feature
– could outcome have influenced exposure information?
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1. Central feature: The order in time of recording of exposure information and the
occurrence of disease.
 Assessing both exposure and occurrence by recall = retrospective.
 Assessing exposure and occurrence by historical documentation, where
exposure documentation preceded disease occurrence = prospective
WRT exposure measurement.
2. Timing of accumulated person-time with respect to study conduct.
 Person-time accumulation before study conduct = retrospective.
 Prospective studies generally exposure classified before occurrence of
disease, but this may not be the case of exposure requires classification
that happens after data collection.
 But retrospective studies may still feature exposure measurement before
disease occurrence, preventing occurrence from affecting exposure
measurement. However, availability of exposure documentation may
depend on disease occurrence.
- Case control studies are commonly retrospective in both senses – recall bias may
lead to over estimation of exposure prevalence in cases. However, cohort studies
may also be similar, and case control studies may be prospective in the sense of
recording exposure information before occurrence of disease.
Cross-sectional studies: Includes all persons in the population at the time of
ascertainment (or a sample) without regard to exposure or disease status. Used to
estimate prevalence.
- Unable to ascertain temporality.
- Length-biased sampling – cases with long duration over-represented. Exposures
that are unrelated to disease risk but cause disease to be mild and prolonged
when contracted will be positively associated with disease.
Proportional mortality studies
Ecologic studies
Hypothesis generation vs hypothesis screening
Oleckno WA. Chapter 4: An overview of study designs. Essential Epidemiology.
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When describing study designs, start by describing how sampling occurs, and then how
one would define a positive association, and finally provide an overview of pros and cons.
Case control studies begin by classifying subjects according to their outcome status. The
cases and controls are then queried for their exposure status, preferably prior to
outcome occurrence. An association is considered to exist if the exposure prevalence in
the cases is higher than that of the controls.
RCS and PCS, on the other hand, assess exposure first and outcome second. An
association is positive if the incidence of disease is higher among those exposed than
those not. RCSs use construct a cohort using historical data available at the beginning of
the study, and follow patients from the past to the present, instead of present to future.
RCTs involve 3 fundamental steps – selection of cohorts, random allocation, and followup / outcome ascertainment.
Descriptive studies – characterize morbidity and mortality without a priori hypotheses,
with a focus on describe what exists – case reports (one individual described), case series
(a few individuals described), ecologic study without valid comparison groups (unit of
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analysis represents a group of people), cross-sectional study without valid comparison
groups.
Analytic studies – test exposure-outcome relationships – ecologic (unit of analysis is a
group of people), case-control study (outcome assessed prior to exposure), crosssectional study (outcome and exposure assessed at the same time), RCS (exposure
assessed before study commencement, outcome assessed subsequent to that date, but
also before study commencement), PCS (exposure assessed at or before study
commencement, outcome assessed after study commencement).
Experimental studies.
Rothman KJ, Greenland S. Chapter 7: Cohort Studies. Modern Epidemiology: 2008.
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Definition of cohorts and exposure groups.
- One may use incidence rate directly if LTFU and competing risks occur, whereas
average risk and occurrence time must be estimated suing survival methods.
- Accumulation of person-time in the denominator of rates – flexibility in the
analysis of cohort studies. A cohort of person-time units may not correspond to
specific cohorts of individuals.
- Fixed cohorts (left closed), closed populations / cohorts, and dynamic
populations (e.g.: my proposed person-time cohort study).
Classifying person-time
- Study hypothesis specified in appropriate detail important to define person time
as exposed or non-exposed.
- Induction time issues (e.g.: exposed but insufficient induction time) (e.g.: study of
delayed Japan atom bomb effects including events including earlier person-time
in denominator may dilute associations).
Chronic exposures
- Cumulative measures: a product of intensity and duration of exposure (e.g.: pack
years, 1 pack-year = 20 cigarettes per pack and 365 days = 7300 cigarettes).
- Average exposure, maximum intensity, etc.
- Composite nature of cumulative or average measures should be recognized and
separately analyzed.
Unexposed time in exposed subjects (e.g.: minimum induction time after exposure not
elapsed) (Other examples: Are cross-over analyses appropriate?) – options:
- Apportion to unexposed time – but will attenuate associations if induction time
hypothesis is wrong.
- Do not include – but will affect available data and precision.
- Stratify effects on time after exposure.
- Model induction time explicitly.
Immortal person-time: Must not enter the denominators. Studies with immortal persontime at risk of selection bias (e.g.: survival bias or prevalent user bias).
Post-exposure events – allocation of follow-up time should not depend on events
occurring after follow-up has accrued. E.g.: Do not remove total person time in a patient
that later comes off-protocol.
Expense
- Cohort studies may be expensive relative to the frequency of events expected.
- Solutions: Special exposure cohorts, otherwise selected cohorts (e.g.: high risk),
registry for disease occurrence (reduces monitoring costs), historical cohorts,
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replace unexposed cohort data with general population information, and
conduct a case control study within the cohort.
Special exposure cohorts – more events, better records if the cohort was subject
to health surveillance. However, exposures are uncommon and subjects must be
identified.
Historical cohorts – See retrospective vs prospective – data quality may reduce
information availability and also introduce bias.
General population cohorts – very precise, but part of the general population
may be exposed (bias towards the null created by non-differential exposure misclassification), differences in quality of information (information bias), and
confounding (e.g.: health worker bias).
Oleckno WA. Chapter 12: Prospective and retrospective cohort studies. Essentials of
Epidemiology: 2002.
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Advantages: Demonstrate temporal sequence, permit direct calculation of incidence
rates, allow multiple outcomes (and sometimes multiple exposures) to be evaluated,
provide indication of incubation or latency period, allow study of rare exposures,
determination of outcome status unlikely to bias determination of exposures status.
Weaknesses: Large sample sizes and long follow-ups, diagnostic suspicion bias.
Cells of the 2x2 table may be directly interpretable as incidence rates.
Be able to draw the 2x2 table and demonstrate common measures of association – how
does this 2x2 table differ from that of a case-control study?
Rothman KJ, Greenland S, Lash TL. Chapter 8: Case-control studies. Modern Epidemiology: 2008.
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Case control study – more efficient version of a corresponding cohort study.
In a cohort study, the numerator and denominator of each disease frequency is
measured. Case control studies observe the population more efficiently by using a
control series in place of complete assessment of denominators. Control series provides
an estimate of the relative sizes of the denominators for exposed versus unexposed
cohorts. This increases efficiency in the cost-effectiveness sense, though not the
statistical sense.
Control selection – exposure distribution among the controls must be the same as it is in
the source population of cases. This need only be true within strata, and not between
strata, as long as stratification is taken into account.
- Represented by the relationship, r = B1/T1 = B0/T0, for a source population
defined with respect to person-time.
- In a cohort study, I1 = A1/T1 and I0 = A2/T2.
- But we replace the denominator with the control series, so that I1 = A1/B1 and I0 =
A0/B0. These are pseudo rates, which may be related to the true rates if the
control sampling rate, r, is known.
- Even if r is not known, if control selection correctly sampled from the source
population, then B = r*T and the ratio of pseudo-rates is equal to the incidence
rate ratio.
- The ratio of pseudo-rates, often called the cross-product ratio, is also commonly
thought of as the exposure odds ratio (i.e.: (A1/A0)/(B1/B0)) – the ratio of odds of
being exposed among cases versus controls.
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- Does not require rare disease assumption.
Defining the source population
- Primary base or population-based study – cases selected from a precisely defined
and identified population, and controls directly sampled from same population.
- Random sampling is most desirable.
- Secondary base studies – not possible to identify the source population explicitly,
and simple random sampling not feasible. Must select controls so that they
would simulate the exposure distribution in the source population. E.g.: Patients
treated for severe psoriasis at the Mayo Clinic – come from all over the world –
unable to identify folks who would attend the Mayo Clinic if they had psoriasis).
Case selection
- May be incomplete, so long as the case sampling rate is equal for exposed and
non-exposed cases.
Control selection
- Must be selected from same population that gives rise to study cases, or a
population with an identical exposure distribution.
- Within strata of stratification factors, controls should be selected independently
of their exposure status.
- Controls may represent person-time if the sampling probability of any control is
proportional to the amount of person-time that person spends at risk of disease
in the source population (incidence-density sampling) – allows estimation of
rates – density case control study.
- Controls may represent those at cohort entry if each subject in the source
population has an equal chance of selection as a control, regardless of time spent
at risk / under follow-up, and including those that ultimately acquire disease –
case-cohort study – allows estimation of RR.
- Controls may represent those without disease at the end of follow-up –
cumulative case-control study – allows estimation of incidence OR.
For density sampling or for estimation of risk ratios, a person may be selected as
a control and yet remain eligible to become a case – or may even be selected as
a control more than once – corresponds to person contribution multiply to
person-time and to both numerators and denominators in cohort studies.
- Fallacies – Do not restrict controls to those at risk for exposure. These subjects
would be part of the unexposed portion of the source population and would be
included in the corresponding cohort study.
Neighborhood controls: Used out of convenience. E.g.: service area of a hospital.
However, may be misleading – e.g.: VA hospitals – patients different from individuals in
the neighborhood – military experience. Possibly poor recall as well – unmotivated.
Dead controls: Great, so long as causes of death are not related to exposure. May
enhance comparability of information if cases are dead.
Random-digit dialing: Must distinguish commercial from residential, ensure that each
residence may has an equal probability of contact and response/enrollment. Expensive –
recent developments mean phone numbers may not be linked to geographic areas.
Possibly poor recall as well – unmotivated.
Hospital- or clinic-based controls
- Premise: Source population of cases in a given clinic is composed of those who
would seek medical care at that clinic, which may be represented by those who
do seek medical care at that clinic.
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Problem: Source population is actually those who would seek medical care at
that clinic if they had the given disease, which may be different for other
diseases.
- Problem: Exposure distribution may differ from those of the source population –
exposure may be related to hospitalization generally, or may be associated with
other diseases, or both. Over-representing exposure prevalence in the control
series will attenuate the study OR. E.g.: smoking and leukemia. Use of controls
with cardiovascular and respiratory diseases.
- Solution: Exclude from the control series those hospitalized with diseases known
to be related to smoking. Exclude liberally – if wrong, the series simply becomes
more homogeneous. But make sure there is some diversity in the series, just in
case one of the included sources does happen to be related to exposure – a
variety of diagnoses dilutes the biasing effects.
- Exposure related to hospitalization – Berkson’s bias – cannot be remedied.
Friend controls
- Uses individual matching – pros and cons.
- Friends and cases may be more likely to share similar exposure history.
Alternatively, friends of cases may be less likely to share exposures – e.g.: having
learning problems, disliking school. Exposure history of socially active people
more likely to be represented.
Types of case control designs
- Nested case-control study – primary based, within a fully enumerated cohort.
- Case-cohort – same control group representing every person in a cohort – used
with multiple case series. Produces risk ratios. Unable to implement density
sampling in this way, because sampling at the time of case occurrence (risk-set
sampling) requires a different control sample for each case series.
- Density case-control study – density sampling and risk set sampling are two
approaches to sampling that provide control series representative of the persontime experience of the source population.
- Cumulative case-control studies – where sampling begins after all the cases have
occurred – e.g.: epidemic of diarrheal illness. Results in OR, which may be equal
to RR or IR if R < 0.10. More sensitive to bias from exposure-related LTFU, since
the entire cohort was not enumerated to begin with.
Oleckno, WA. Chapter 11: Case-control studies. Essential Epidemiology: 2002.
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Strengths: relatively quick and inexpensive, appropriate for rare outcomes, conducted
with moderate numbers of subjects, examine multiple exposures (this is accomplished by
cohort studies as well).
Weaknesses: Incidence rates / risks cannot be estimate (without knowing the sampling
rate of cases and controls), not appropriate for rare exposures, subject to recall biases if
retrospective, difficulty assembling a correct control series.
Oleckno, WA. Chapter 7: Association and Causation. Essential Epidemiology: 2002.
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Associations are statistical findings.
Associations may be of three types:
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Spurious – false – Sampling error or bias. E.g.: False positives due to multiple
comparisons. E.g.: Confounding.
Non-causal associations. Real associations that are not causal. E.g.: Prevention of
death causes an increase in time at risk for car accident, giving rise to a noncausal association between therapy and car accidents.
Causal – See Bradford Hill criteria. Those in which changes in the exposure
produce changes in the outcome.
Rothman KJ, Greenland S, Lash TL. Chapter 9: Validity in epidemiologic studies. Modern
Epidemiology: 2008.
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Accuracy = value of the parameter is estimated with little error.
Errors = random or systematic.
Systematic errors = biases. Opposite of bias = validity. Systematic error has a non-zero
expected value, regarding its departure from the true value of an association.
Opposite of random error = precision. Random error has an expected value of zero,
regarding its departure from the true value of an association.
Internal validity – violations – confounding, selection bias, and information bias.
Confounding
Mixing of effects. Apparent effect of the exposure is distorted.
When the measure of association does not equal the measure of effect, because of
differences in variables other than the exposure.
Surrogates can stand in for confounders – e.g.: age as a surrogate for aging.
Confounder must be an extraneous risk factor for the disease under study, where
extraneous means apart from the exposure. I.e.: it must be exposed with the disease in
the unexposed group. E.g.: Pizza consumption is a confounding factor for the beer –
rectal cancer relationship? No, pizza consumption is associated with rectal cancer only
because of its association beer consumption. In fact, the pizza-rectal cancer relationship
is confounded by beer. For case control studies, must look at the control series / source
population, not the case series. The confounder might not actually be a risk factor for the
disease – but then it must be a surrogate for one. Judging this criteria requires external
knowledge – one would not want to over-adjust, or adjust the estimate for a random
error.
Confounder must be associated with the exposure in the source population. For cohort
studies, the cohort is the source population – just check the data. For case-control
studies, check the controls, if the control series is sufficiently large. May need external
information. Nested case-control studies – check the cohort.
Confounder must not be affected by the exposure or disease – not an intermediate
factor, or a consequence of disease. This must be true if confounder precedes exposure
and disease.
Exceptions – colliders that are neither direct descendents of exposure or disease, but
might instead be linked to exposure and disease through a pathway of common causes.
E.g.: Figure 12-2
X = Low education  Z1 = Family income  W = Mother had diabetes  Z2 = Mother’s
genetic risk  Y = Diabetes. W is a collider. Conditioning on it opens up a confounding
pathway, but it would not cause confounding to begin with.
If a confounder is no longer a confounder within strata of a second confounder, then the
first confounder is only a surrogate for the second.
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Implications of adjusting for a descendent of the outcome – may open confounding, if X
 Y and U Y but U and X have no relation. Y  Y*. Conditioning on Y* opens up a U 
Y  X pathway. E.g.: Education  MMSE score, U also affects MMSE but not education.
Among those with MMSe score greater than 24, those with low education are more likely
to have other factors that raise MMSE, while those with high education are less likely to
have such factors. A negative association between U and X is induced.
Another example: Speed  basketball ability, height  basketball ability. Speed
unrelated to height. If we examine this association only in those who are drafted into the
NBA (very high basket ball ability), we will introduce a negative association between
speed and height, because those who are short in the NBA had to have been faster to get
drafted.
Salas M, Hofman A, Stricker BH. Confounding by indication: an example of variation in the use of
epidemiologic terminology. American Journal of Epidemiology, 149(11): 1999.
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Confounding by indication – refers to an extraneous determinant of the outcome that is
present if a perceived high risk or poor prognosis is an indication for intervention.
Classic: The disease for which the intervention is prescribed is over-represented in those
with the intervention. E.g.: Anti-depressants  infertility, but this may be due to
depression  anti-depressants and depression  infertility, a confounding pathway.
Protopathic bias – the first symptoms of the outcome of interest are the reasons for use
of treatment. A spurious association between aspirin and Reye’s syndrome will occur if
aspirin is prescribed preferentially to those exhibiting early (undiagnosed) signs of Reye’s
syndrome. The bias may be in the opposite direction. For instance, if the early
(undiagnosed) signs of Reye’s syndrome cause children to cease aspirin therapy, then
cessation of aspirin therapy will be associated with Reye’s syndrome, and aspirin therapy
will appear preventive. Protopathic bias is often confused for confounding by indication.
Confounding by severity is a class of confounding by indication – if the study intervention
is more likely to be provided to patients with lower health status, then health status will
confound the intervention - outcome relationship. E.g.: Fomoteral and asthma, fomoteral
may appear to be linked to higher mortality if sicker asthma patients were prescribed
fomoteral to begin with.
Confounding by prognosis or confounding by comorbidity – refers to the slightly different
concept that the physician’s perception of the patient’s prognosis, rather than the actual
severity of disease, acts as the confounder. This is also a sort of confounding by
indication.
Definition – selection bias – a distorted estimate of the effect that results from the way in
which subjects are ascertained or selected for the study population, and includes factors
such as differential surveillance, diagnosis, and referral of persons into the study.
(Hennekins CH, Buring JE. Epidemiology in Medicine. Boston, MA: Little, Brown & Co.:
1987. Pp. 272-286.).
Selection bias may be confused for confounding by indication, but should not be.
However, the examples of this provided by Salas et al. all depict circumstances where the
selection factor is not a confounder – however, in all examples, the selection factor is, in
fact, a surrogate for a confounder, which can be treated as if it were a confounder. Thus,
Salas et al. do not actually present an example of selection bias falsely labeled as
confounding by indication.
Rothman KJ, Greenland S, Lash TL. Chapter 9: Validity in epidemiologic studies. Modern
Epidemiology: 2008.
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Selection bias
Distortions that result from procedures used to select subjects and from factors that
influence study participation. The relation between exposure and disease is different for
those who participate and for all those who theoretically should have been eligible for
the study.
Self-selection bias. Volunteer bias. Response bias.
Healthy worker effect. Membership bias.
Prevalence-incidence bias – mild, resolved, or fatal cases are excluded from the case
group. Available cases may have a different exposure distribution than all cases.
Survivor bias or immortal time bias.
Berksonian bias
 Occurs when both the exposure and the disease affect selection.
 E.g.: Estrogens causing endometrial cancer. Horwitz and Feinstein suggested that
estrogens were merely advancing diagnosis, because estrogens induce bleeding,
which would cause women to seek medical attention. As it turns out, this
reasoning is flawed because endometrial cancer is still diagnosed (serious
disease, inevitably becomes symptomatic), even if the time of diagnosis varies for
unexposed patients. Anyways – proposed solution – control series of women
with benign gynecologic diseases. But administration of estrogen would cause
the diagnosis of benign conditions that otherwise may not have been detected,
so exposure prevalence over-estimated for source population.
 Alternative solution – restrict cases and controls to women with vaginal bleeding.
However, estrogen causes bleeding, and endometrial cancer causes bleeding. By
restricting to those who bleed, we introduce a negative association between
endometrial cancer and estrogen use, because if you are bleeding and you do
not have endometrial cancer, you probably have some other cause of bleeding,
like estrogen use.
Some of the above examples are really forms of confounding, because they relate to
third variables that can be captured and adjusted for (theoretically, at least). E.g.: health
status, fitness. They may not be measured though, so removal of confounding may
require restriction.
Not all selection bias can be dealt with as confounding.
 LTFU affecting risk of disease – collider of exposure and disease. Exposure itself is
generating LTFU, cannot adjust for exposure.
 Inadequate choice of control series in case-control studies. For selection factors
unaffected by exposure (e.g.: sex), one may control. For those affected by
exposure (e.g.: Berkson’s bias), one cannot control – no confounder to control.
Lau D, Gamble JM. Berkson’s Bias. Notes from discussion on September 17, 2010.
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Berkson’s bias – direction explored using TIA and blood pressure medications
Assume that all cases have been sampled – all relevant cases of TIA present to hospital.
Blood pressure medication (protective)  TIA, blood pressure medication 
hospitalization (for whatever reason, patients with more medications are more likely to
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be hospitalized), and TIA  hospitalization. True case exposure rate = 25%. Source
control exposure rate = 50%. OR = (1/3)*(1/1) = 0.333.
Then within strata of hospitalization, if subjects do not have a TIA, they are more likely to
be on BP meds, and vice versa. Subjects who do not have a TIA will over-represent the
exposure distribution of BP meds and bring the OR towards the null. The effect is away
from the null for a protective exposure. Hospitalized control exposure rate = 75%. OR =
(1/3)*(1/3) = 0.111
Now stipulate blood pressure medication (protective)  MI  hospitalization. Those
hospitalized without TIA will be more likely to have MI and less likely to be on blood
pressure medications, so that the exposure prevalence of the source population is underestimated in the control series. This leads to an effect toward the null (and perhaps
across the null in the other direction) for a protective exposure. Hospitalized control
exposure rate = 33%. OR = (1/3)*(2/1) = 2/3 = 0.66.
No let’s look at a deleterious exposure – BP instead of BP meds. BP  TIA, BP 
hospitalization, and TIA  hospitalization. Case exposure rate = 50%. Control exposure
rate if sampled from source = 25%. OR = (1/1)*(3/1) = 3.00.
Condition on hospitalization. Non-TIA hospitalized patients are more likely to have high
BP. Control exposure rate if sampled from hospital = 33%. OR = (1/1)*(2/1) = 2.00.
Now say BP (protective)  MI  hospitalization. Non-TIA hospitalized patients are
probably, in reality, more likely to have an MI and high blood pressure. But if BP were,
strangely, protective of MI, perhaps because it singles you out for lipid lowering therapy,
then having increased MI also means having lower BP, so that the controls underestimate the exposure prevalence of the source population. Control exposure rate = 20%.
OR = (1/1)*(4/1) = 4.00.
Now, let’s say the cases are not complete – hospitalized cases are not all cases in the
population. Again, case and exposure status are linked to hospitalization due to patterns
of medical care. Hospitalized patients are more likely to be exposed than source patients,
and are more likely to be both exposed and have disease than members of the source
population. The bias in this case is away from the null.
Here’s how to write out a bias analysis for Berkson’s bias on the board. Start by drawing
out the DAG. Then, writing from right to left:
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Exposure = 25%  Case – TIA – hosp.
 OR = 0.33 Exposure = 50%  Control – source.
 OR = 0.11 Exposure = 75%  Control – hosp.
Rothman KJ, Greenland S, Lash TL. Chapter 9: Validity in epidemiologic studies. Modern
Epidemiology: 2008.
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Information bias
Bias in estimating an effect caused by measurement errors in needed information.
Classification error (discrete variables). Differential vs non-differential (does not depend
on values of other variables). Independent or dependent (depends on errors in
measuring other variables).
Differential misclassification
 Exposure suspicion bias and recall bias.
 Outcome suspicion bias.
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May also underestimate an association (e.g.: recall bias generated by cases of
Alzheimer’s disease may under-report exposures).
Non-differential misclassification – does not depend on the status of the subject WRT
other variables. Predictable in direction – towards the null. However, exceptions.
Non-differential misclassification of exposure
 Exposed classified as unexposed, or vice versa, brings the disease experience of
the cohorts towards each other.
 Important relation: When sensitivity and specificity of exposure classification sum
to 1, the expected estimate will be null, regardless of the magnitude of effect.
This is tantamount to randomly assigning exposure status.
 Important relation: When the sensitivity and specificity of exposure classification
is zero, the expected odds ratio is the inverse of the correct value. This is
tantamount to labeling all exposed as unexposed, and vice versa.
 Exception to bias towards the null: More than 2 exposure categories, ordinal
data. Non-differential misclassification between any two categories will draw
estimates towards each other, which may mean away from a third (or other)
categories, such as the reference category – this would cause a bias away from
the null.
Non-differential misclassification of disease – independent errors.
 Lower sensitivity will not bias the risk ratio, but will downwardly bias the riskdifference by a factor equal to 1-sensitivity. In this case, a similar proportion of
those with true disease are missed in both exposed and unexposed groups.
Because disease is the numerator, this means decreasing both numerators by a
similar amount – this cancels in the ratio scale, but not in the difference scale.
 Lower specificity – a similar proportion of those without disease are marked
diseased in both exposed and unexposed groups. This increases the amount of
disease in both groups, but not by a similar amount – the amount, rather, is
relative to the true 1-R. If there are more non-cases in the unexposed cohort
(consistent with a positive effect of exposure), then the amount by which disease
increases in the unexposed cohort will be relatively higher than the amount by
which disease increases in the exposed cohort. Relative measure will bias
towards the null. So will difference measures, by a factor equal to 1-spec.
 With both imperfect sensitivity and specificity, the bias in the risk difference
independent of other errors will equal the sum of 1-sens and 1-spec.
Non-differential misclassification of any sort with dependent errors may bias away from
the null, and simple bias relations will not apply. E.g.: Both exposure and outcome
measured in interviews – NOT SURE WHY.
Common for many researchers to satisfy themselves with achieving non-differential
misclassification in lieu of accurate classification. This helps assure that an effect that is
observed is valid, at least qualitatively.
 Non-differentiality must, however, be accompanied by independence and binary
variables.
 Categorization of continuous outcomes can chane nondifferential to differential
error.
 Misclassification of confounding may cause residual confounding in any direction.
 Missclassification towards the null will not necessarily produce an upward bias in
the P-value (DL – WHY NOT?).
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Serious distortions for SRs. Secondary study characteristics such as exposure
prevalence will affect degree of bias (PPV and NPV) even when sens and spec are
constant from study to study – in any case, why would sens and spec be
constant? Heterogeneity. Interestingly, this may be induced by overbroad
exposure (e.g.: including induction time) or outcome definitions (e.g.: broad
composite outcomes), which also cause a bias towards the null.
Confounder mis-classification – if independent and non-differential, will reduce degree of
control and allow for residual confounding. Final bias will be between true value and
unadjusted value – bias is still attenuated. Differential or dependent misclassification may
cause further distortion, making bias worse. E.g.: Food diaries. If high values reported for
a confounder are more likely when high values are reported for an exposure …
Misclassification of exposure, disease, or confounders may be introduced simply by overbroad categories!
Generalizability
 Requires sample subjects from the target population, so that the study
population is “representative” of the target, in the sense of being a probability
sample from that population (or, in a two stage design, so that a representative
sample may be constructed). Allows inference to the target.
 However, validity threats – may require more homogeneous study groups with
highly cooperative behaviour, and availability of accurate information. E.g.:
Nurses’ Health Study. Non-representativeness presumed to be unrelated to the
effects studied, so generalizing okay. If generalizability concerns arise, may be
addressed after internal consistency – are the factors different between the
study and target populations important modifiers of the association?
 Therefore representativeness is one way of attaining generalizability, but should
not be pursued at the expense of internal validity or efficiency (in both the
statistical and the cost-effectiveness sense). Representativeness is not always
necessary for generalizability.
Oleckno WA. Chapter 8: Assessing the accuracy of epidemiologic studies. Essentials of
Epidemiology: 2002.
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Recall bias – results from the fact that cases often remember past exposures better than
controls.
Interviewer bias – interviewer awareness of outcome of exposure status affets how they
solicit, record, or interpret data.
Diagnostic suspicion bias – knowledge of subjects’ exposure status leads to systematic
differences in the procedures for diagnosing the outcome.
Exposure suspicion bias – knowledge of the subjects’ outcome status influences how
exposures is assessed.
Prevalence-incidence bias – cases more likely to be sampled are those with long duration,
which may not represent the exposure distribution in all cases.
Membership bias – those who belong to an organized group tend to differ systematically
on health status from the general population.
Volunteer bias – those who take part in epidemiologic studies are systematically different
from those who do not.
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Berkson’s bias – a type of selection bias that can occur in hospital-based case-controls
studies. The bias results when the combination of the study exposure and outcome
increases or decreases the chance that cases will be admitted to the hospital.
Berkson’s bias – DL version – The bias results when hospitalized patients are
systematically different from members of the source population because both exposure
and disease affect the risk of hospitalization.
Rothman KJ, Greenland S, Lash TL. Chapter 11: Design strategies to improve study accuracy.
Modern Epidemiology: 2008.
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Design options to control confounding
 Experiments – control of extraneous factors.
 Randomization – Extraneous factors are expected to be distributed evenly across
treatment assignments.
 Restriction – Effective and inexpensive means of preventing confounding by
known factors. However, may shrink pool of available subjects, and may lead to
collider bias (i.e.: Berkson’s bias in hospital-based case-control studies). Any form
of control may lead to other collider biases so triggering collider biases is not
unique to restriction, although it may make collider biases harder to diagnose.
May also reduce generalizability, if the effect under study is suspected to vary
across categories of the restriction variable.
Matching
 Selection of a reference series that is identical, or nearly so, to the index series
with respect to the distribution of one or more potentially confounding factors.
In experiments, analogous to controlling extraneous factors – observational
analog of randomization, since the only condition investigators may control,
aside from the process of data collection and analysis, is subject selection.
 Individual matching – subject by subject.
 Frequency matching – groups of subjects – selection of an entire stratum of
reference subjects with matching values.
 May require control in analysis. This may take the form of stratified analyses
(e.g.: Mantel-Haenszel analyses or the extension to paired data, McNemar’s
test), or explicit control, if the matching variable is tangible and tenable to
adjustment.
 Matching in a cohort study
 No additional action required in the analysis to control for confounding
by matching factors.
 Exception: Exposure and matching factors affect disease risk or
censoring, then the original balance will not extend to persons and
person-time available for analysis.
 Expensive to match large cohorts, except in registry or database studies.
 Matching also increases precision (classic theory) – reduces variance of
extraneous factors within matched sets. E.g.: continuous outcome,
treatment assignment within pairs, paired T-test. Exceptions – not well
explained.
 Matching in a case-control study
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We do this to adjust for confounders – however, potential confounders
are related to the exposure. Matching will therefore cause the control
series to over-estimate exposure prevalence and bias the association
towards the null.
Case-control studies involve matching non-diseased to diseased.
Selecting controls by matching factors associated with exposure
introduces a bias with no counterpart in cohort studies.
E.g.: Let’s say the matching factor was really a surrogate for the
exposure. Then we would have identical exposure distributions between
cases and controls, OR = 1.0.
Always a bias towards the null, because controls are matched to identical
values for cases.
If matching factor not associated with exposure, then no bias. But also
no internal validity reason to match.
Matching may introduce bias where none previously existed.
Requires some analytic control for matching factors.
Other reasons for matching in case-control studies: Efficiency, statistical.
Suppose one anticipates stratifying for age – potential confounder. An
unmatched case-control series may be sparse in certain categories.
Extreme inefficiency is produced in strata with no cases or controls – no
discordant pairs – discarded, no contribution to M-H pooled OR.
Matching ensures that all strata are able to provide useful data, prevents
extreme departures from statistically optimal apportionment. However,
matching on correlates of exposure will also increase the similarity of
exposure distributions between cases and controls and increase the
chance of non-discordant pairs! = Overmatching.
Other reasons to match: The variable is a confounder but is intangible or
difficult to model, explicitly. E.g.: Sibship, any nominal variable with
numerous categories – sparse data issues.
Case-control matching on a non-confounder will harm efficiency, since
the most efficient approach is not to stratify or match.
Matching good if it is too expensive simple to increase study size, focus
on increasing efficiency of a few cases and controls.
Matching in a case control study prevents the effect of the matching
factor from being estimated – distribution of the matching factor as an
exposure is constrained – no direct estimation of rates or risks. Also may
be expensive. Matching on many factors is untenable.
Of course, matching great for examining effect-modification.
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Over-matching
1. Harm to statistical efficiency by matching on factors that would not be
confounders anyways (e.g.: case control studies).
2. Increased bias – collider of exposure and disease. Berkson’s bias in case-control
studies. Also applies to cohort studies. E.g.: Assume no association between
height  speed. Examining basketball players only will induce an association –
adjusting for this factor unnecessarily – e.g.: because we think that NBA
professionals have a genotype that affects both speed and height will induce
bias.
Ferreira-Gonzalez I, Permanyer-Miralda G, Busse JW, Bryant DM, Montori VM, Alonso-Coello P,
Walter SD, Guyatt GH. Methodologic discussions for using and interpreting composite endpoints
are limited, but still identify major concerns. Journal of Clinical Epidemiology, 60(7): 2007.
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Composite end-point = CEP = occurrence of any event from among a given set of events
after a certain period of follow-up.
SR of texts providing a commentary, analysis, or discussion about CEPs.
Advantages
- Reduced sample size requirement / increased statistical power.
- Capture the net benefit of the intervention.
 Requires elements of the CEP to be similar in importance
- Avoiding competing risks, or other situations where outcomes are linked in a
causal or non-causal fashion.
 Important not only for comparison of proportions, but also for survival
time analysis if assumptions like independence among the main events,
the competing event, and the censoring times are uncertain.
- Avoid multiple comparisons
- Avoid committing to a single primary outcome when outcomes are disputed.
More charitably, there may be no single natural primary outcome.
Disadvantages
- Heterogeneity in outcomes – misinterpretation and decreased power.
 Decreased power due to increased variability of the primary outcome.
 Variations in clinical and patient importance – misleading if an overall
effect is driven by a less serious or important component.
 Invalid or non-informative outcome estimate – e.g.: if components move
in different directions.
 Vulnerable to clinician judgement – i.e.: presence of a clinician-driven
component, like photocoagulation.
- Does not permit conclusions about components to be drawn without adjustment
for multiple comparisons.
 Otherwise, adjustment for multiple comparisons is necessary.
 In that case, sample size should also be increased, based on the event
rate of the CEP and its components the type I error, and the degree of
correlation among the components.
Recommendations
- Avoid components unlikely to be influenced by intervention.
- Homogeneity of pathophysiologic rationale among components
- Homogeneity of importance among components.
Tomlinson G, Detsky AS. Composite end points in randomized trials: there is no free lunch. JAMA,
303(3): 2010
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Recommendations
Also need similar frequency in outcomes, because composites will be driven by the more
frequent outcomes.
Homogeneity of treatment effect – otherwise bait and switch possible …
Similarity of clinical importance.
Moye LA. End-point interpretation in clinical trials: the case for discipline. Control Clin Trials,
20(1): 1999.
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Non-specified endpoint of a trial attained significance while both primary and secondary
specified endpoints were NS – how to interpret?
There was never a question about the relationship revealed in the data – clearly it exists.
Concern should be focused, however, on identifying the correct implications for the
population to whom the results would be generalized.
Interpretation requires a priori specification of outcomes – otherwise sampling error is
allowed to influence the choice of outcome, rendering the p-value meaningless. The
analysis chosen is one of an infinite number of analyses possible.
Allocating alpha is the means by which physician-scientists uphold their duty of
beneficence to the community.
Spending alpha – procede sequentially, preserve the family-wise alpha < 0.05.
What alpha is available for secondary outcomes?
- 1 – alphatotal = (1-alphaprimary)*(1-alphasecondary)
- Then asecondary = 1- (1-atotal) / (1-aprimary)
The alpha-standard for rejecting the null hypothesis of a secondary outcome depends on
the family-wise alpha desired and the alpha of the primary outcomes.
These computations are only valid of endpoint have been prospectively identified.
Otherwise many post hoc analyses can e performed with only the most favorable ones
being promulgated, leading to hidden spending of alpha.
Ray WA. Evaluating medication effects outside of clinical trials: new-user designs. American
Journal of Epidemiology, 158(9): 2003.
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Hormone replacement therapy in post-menopausal women.
o Observational studies – 35% to 60% reduction in coronary heart disease – even
with extensive adjustment for potential confounding factors.
o Two RCTs and results from the WHI – no benefit – using estrogen with a
progestin increased the risk of coronary heart disease.
How could observational studies be so misleading?
“Healthy user effect” – investigators did not assign treatment.
Also prevalent user effects
- Under-ascertainment of early events
 Rate at which treatment-related outcomes occur may vary with time
since the start of therapy.
 E.g.: Surgeries – recruitment after surgery – exclude peri-operative
deaths – serious bias.
 HRT – evidence from the Heart and Estrogen/Progestin Replacement
Study (HERS III) – HR of CHD is initially over 2.0, fell over time, reaching
1.0 at 2 years.
 Mechanisms – physiologic effects vary with time.
 Induction periods different for certain risks and benefits
 Physiologic adaptation after prolonged treatment
 Other selection factors that vary with duration of treatment.
 Mechanisms – amplification of adherence bias.
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Problem cannot be adjusted by recording duration of prior therapy
because prevalent users exclude those whose duration of use is
comparable, but who stopped use because of events or other adverse
effects.
- Inability to control for disease risk factors altered by the study drugs.
 HRT – alters both HDL and LDL
 HDL and LDL – adjustment for healthy user effect
 But may also be adjusting for an intermediate!
 Conundrum does not occur with new user design, due to adjustment for
confounders measured prior to treatment – cannot be consequences of
treatment.
New user designs
- Identify all the patients in a defined population who start a course of treatment
with the study medication.
- Follow-up begins at the same time as therapy initiation.
- Washout – prior period of nonuse to ensure incident users.
- Prevalent users excluded.
- May need to match cohort on previous exposure to similar drugs, especially if
washout is not expected to be complete – but generalizability may be limited.
New users in case-control studies
- Define a study period for accrual of cases.
- Those exposed before this period are prevalent users and should be excluded.
- E.g.: A patient using HRT 1 year prior to study accrual, who suffers a heart attack
just before study accrual, would not be included. Then neither should a similar
patient who is not a case, i.e.: does not experience the outcome.
Logistical challenges with new user designs
- Identifying new users from primary data collection may require tracking drug use
and confounders on a day-to-day basis.
- Automated data linkages and databases make this easier.
- Restricting studies to new users will reduce sample size, especially for drugs that
have been on the market for several years – the pool of new users may be much
smaller than the pool of prevalent users.
 Potential solutions – Use databases that follow populations over time.
 Include prevalent users if hazard does not vary with time, adherence bias
is not present, and important covariates are not affected by study
exposures.
- New user designs may give excessive weight to short-term users if the
medication is prescribed for both acute and long-term indications – e.g.: NSAIDS
for acute pain vs chronic osteoarthritis.
- Solutions – Measure behavioral factors and indications.
The inclusion of prevalent users engenders susceptibility to biases related to underascertainment of early effects and modification of variables in the causal pathway.
New-use designs have their own limitations, but can eliminate the two biases specific to
the inclusion of prevalent users.
Suissa S, Garbe E. Primer: administrative heatlh databases in observational studies of drug effects
– advantages and disadvantages. Nature Clinical Practice Rheumatology, 3(12): 2007.
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Studies exploiting existing computerized health databases, comprising administrative
data routinely collected for the purposes of insurance management, or clinical data
collected by general practitioners (e.g.: GPRD), have revolutionized the conduct of
observational research
- Quicker
- Less expensive – data already collected.
North American administrative health databases
- Databases initially created to administer payments to health care providers in
MCOs or nationally funded health care systems.
- Patient-level information from several data files that can be linked by a unique
patient identifier.
- Person-based longitudinal files may be created.
European medical records databases
- E.g.: UK GPRD – anonymous longitudinal patient records from hundreds of GP
practices with data on approximately 3 million patients.
- Data entered by GPs into their practice computers
Advantages
- Large size – rare events
- Accurate medication information vs self-report (e.g.: for elderly, or for mortal
cases).
- Rapid, low cost studies possible.
- Population-based data – representative.
- Patient consent not required – less prone to selection bias from non-response.
Disadvantages
- Valididy of diagnostic information, because diseases are primarily coded for
billing.
- Limited confounder information – e.g.: disease severity, smoking, alcohol use.
- Drug compliance, in-hospital drug use, and over-the-counter drug use
unavailable.
- Limited coverage of drugs unavailable from the formulary.
Rofecoxib example
- APPROVe RCT – 2-fold increase in thrombotic event – withdrawal of Vioxx.
- 4 years earlier – VIGOR study – reduction in the rate of GI complications – 5-fold
increase in rate of AMI.
- Between VIGOR and APPROV – 3 observational studies using North American
administrative health databases – Wide divergence in findings.
Duration of rofecoxib use
- VIGOR hazard functions show rapid increase in CVD events, decrease thereafter,
and a later increase at 8 months after rofecoxib initiation.
- Tennesse study – included new users – captured person-time experience of early
roficoxib users
- However, analyzed all person-time units as equals
- Differences detected in RRs of different dosing groups may have been due to
different durations of exposure.
- Solutions
 Plot the hazard functions.
 If proportional hazard assumption is valid, use a CPH regression.
Immortal time bias
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Ontario study required rofecoxib users to have two prescriptions for study entry
– CVD events were captured any time after the first prescription – however,
death between first and second prescriptions could not be captured, by design,
whereas control patients could have died at any time.
- Immortal time = a period during cohort follow-up during which, by design,
subjects could not have died.
- Immortal time bias – tends to underestimate RR.
- Solution – start follow-up at equivalent time points for exposed and unexposed
cohorts.
Depletion of susceptibles – a drug whose risk is high early after initial use – subjects who
are unaffected early will have a lower risk subsequently.
- Observational studies should include all drug exposures, particularly the first one.
- Ontario study – those with only one prescription for rofecoxib excluded.
- This amounts to 2427 subjects excluded (12156 subjects were included) – bias
towards underestimation – likely that the excluded group had a higher MI
incidence.
- Solution – new user designs – avoid over-represetation of the subset of patients
who are long-term users.
Overadjustment
- Ontario study – adjusted for HTN drugs and CHF drugs – markers of comorbidity.
- VIGOR trial – found that rofecoxib led to increase in the rate of HTN and CHFrelated adverse events.
- Adjustment in the Ontario study – adjustment for factors affected by drug use –
biased estimates of association – bias towards reduced association.
Multiple comparisons
- Pennsylvania and New Jersey Medicare databases – presented 14 different ORs –
many unreported.
- In a database study, selecting the most accurate risk estimate is not
straightforward.
Misclassification of incident and prevalent users, failure to account for carry-over effects
from similar previous therapy
- Need long washout periods.
- Choose a common and unambiguous reference period.
- Misclassification will bias estimates towards the null.
Observational studies conducted with databases overcome the limitations of RCTs (broad
exclusions, short observation, selected population due to refusal and withdrawal, and
monitoring / placebo effects).
Databases enable the conduct of observational studies in diverse patient populations
over long periods of time in a real world setting without patient selection through subject
refusal.
Roos LL, Nicol JP, Cageorge SM. Using administrative data for longitudinal research: comparisons
with primary data collection. J Chronic Dis, 40(1): 1987.
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Discuss the advantages and disadvantages of administrative compared to primary data
collection with respect to mechanisms of loss to follow-up.
Manitoba data, circa 1987
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LTFU
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Claims data – lack of unique identifier, but combination of family registration
number, sex, and birth year identifies almost all individuals.
Population registry – critical to successful use – successive cross-sectional
registry files compared to develop a summary record of coverage and mortality
for each individual in the claims files
 Distinguishes those without claims due to migration from those
generating no claims because of death.
 Allows denominator estimation for small epidemiologic studies – place of
residence codes.
Confidentiality provisions
 Hardware and software protocols
 Unable to identify individuals – limits research – cannot collect primary
data prospectively – linkage (e.g.: to CCHS, interview data) must be
retrospective.
Large breadth of research questions addressed
Cross-sectional response rate = (locating individuals) * (participation rate of
those located).
- Longitudinal response rate = (cross-sectional response in the original sample) *
(cross-sectional response in the follow-up sample).
- Primary data – mortality studies often able to achieve excellent follow-up due to
centralized record keeping – however, for data beyond vital status …
- Manitoba health data provided >90% follow-up of a probability sample of 8000
adults over eight and a half years.
- Compares favorably with primary data collection under short-term and long-term
follow-up.
- Reasons for non-response – refusal to participate in primary studies – analogue
in database studies – primarily families moving into the province and neglecting
to register for health care coverage.
- Some difficulties
 Out-of-province migration (vs within-province migration)
 New registration numbers, e.g.: due to changed marital status.
 Missing but not identified as dead or having emigrated.
 Problem because those most likely to emigrate tend to be younger,
better educated, more affluent, more likely to be married.
Administrative databases – advantages
- No contact with individuals required – no participation, tracking, or reactivity
(Hawthorne effect) issues.
- Sample size constrained only by data base size and computing resources.
- Population coverage
 Important when, e.g.: complications are treated at a different hospital
from the initial surgical procedure – hospital based study may not
capture true rate of complications.
- Pre-histories as easy to construct as post-event histories – no reliance on
individual recall, no need for pre-history interviews.
- Long term follow-up as easy as short-term follow-up, and is continuous.
 Add as many time-series data points as you like!
- No reliance on recall
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Administrative data – disadvantages
- Desired information may not be available
 E.g.: lab values, diagnostic tests, dietary histories.
- Data inaccuracies
- Individual (not researcher) initiates system contacts.
 E.g.: Underestimate prevalence of disease burden
Billable events more likely to be recorded with sufficient accuracy to permit research.
Watch out for changes in billing practices.
Useful for analyzing changes in how a technology works – diffusion and impact.
Unfortunately, claims data measures health care utilization, not health.
Primary data collection’s ability to gather particular items of information must be
weighed against what may be available from nonintrusive claims data – researchers
should consider the use of a well-organized data base before primary data collection,
where available.
Olsen J. Chapter 23: Using secondary data. Modern Epidemiology (Rothman KJ, Greenland S, Lash
TL, Eds.). Lippincott Williams & Wilkins, Philadelphia, PA, USA: 2008.
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Chapter is fairly unorganized – only select points are recounted here.
Secondary data = data generated for a purpose different from the research activity for
which they are used.
Administrative data = databases originating from systems that provide or finance medical
care, and contain computerized records of encounters between patients and health care
providers.
Administrative data analyses may not be secondary, since some administrative data is
collected for research purposes.
The key question is not whether data are primary or secondary, but whether the data are
adequate to shed light on the research question to be studied.
Administrative data from complete populations
- For case-control studies, ensures temporality of exposure to outcome.
- Ensures that outcome cannot affect exposure classification or participation.
 In a case-control study, outcome may affect exposure classification or
participation directly.
 In a prospective cohort study, the evolving chance of an outcome, or
third-variables related to the outcome, may affect time under follow-up
or participation to begin with.
Some questions can only be answered with secondary data.
Some questions are best answered by combining secondary and primary data
- E.g.: identifying cancer cases from a registry – brain cancer – interviewing cases
and controls for exposure to cell phone use – or, possibly, obtaining cell phone
data from another secondary source, i.e.: billing records.
Data quality
- Accuracy of diagnostic labels.
- Completeness of the register – may be evaluated using a capture-recapture
technique, but subject to assumptions of independence.
Suissa S. Effectiveness of inhaled corticosteroids in chronic obstructive pulmonary disease:
immortal time bias in observational studies. American Journal of Respiratory and Critical Care
Medicine, 168(1): 2003.
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Evaluate the bias due to immortal time in standard observational studies of inhaled
corticosteroid therapy for COPD.
Data source = Saskatchewan health data
Study design – modeled after Sin and Tu, 2001 (Sin DD, Tu JV. Inhaled corticosteroids and
the risk of mortality and readmission in elderly patients with chronic obstructive
pulmonary disease. Am J Respir Crit Care Med, 164: 2001).
- Patient with incident COPD – at least 3 prescriptions for a bonchodilator on at
least 2 different dates within a 1 year period from 1990 to 1997.
- Entry = date of the third prescription.
- Study cohort = all subjects hospitalized for COPD – entry date = discharge date.
- Follow-up = 1 year
- Outcome = First of readmission with COPD or death from any cause – exclusion
of deaths within 30 days of cohort entry.
- Exposure
 Subjects considered to be “users” if they filled a prescription for an
inhaled corticosteroid anytime during the first 90 days of follow-up –
considered exposed for the entire follow-up period.
 This is an “intent-to-treat” approach (Sin and Tu, 2001)
Exploring potential bias
- The time window of exposure classification was varied – 15, 30, 90, 180, and 365
days.
Analysis – CPH models
- ITT approach as in Sin and Tu, 2001.
- Time-varying exposure approach with subjects classified as unexposed before
prescription for inhaled corticosteroid and exposed thereafter.
- Adjusted for age at cohort enry, sex, and for use of other COPD medications
dispensed during the 90-day period.
Source of potential selection bias
- The rate of events is not homogeneous over time – increases steeply after
discharge to almost 3 per 1000 per day, and decreases by the 100th day of followup to around 1 per 1000 per day.
- Those who obtain early events before having the chance to initiate inhaled
corticosteroid therapy are classified as unexposed – the unexposed outcome
frequency includes the experience of those who would have been classified as
exposed if they had not had the outcome.
- Those who are left to be exposed are those who did not incur the outcome
before they could initiate inhaled corticosteroid therapy
 Confounding – healthy bunch at that point.
 Selection bias – During the “immortal person time”, subjects contribute
person time to the denominator but not the numerator of the exposed
event rate.
- Immortal person time, in this instance, should be correctly allocated to the
unexposed group – this produces more stable estimates closer to the null (see
results, below).
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1072 subjects – first hospitalization for COPD – average 73 years old at hospital discharge
– Patients (93) died within 30 days of discharge – excluded.
Results – Relation of outcome to exposure – time-fixed analysis – crude
- 90-day window – 383 vs 596 subjects – RR = 0.68 [0.55, 0.84].
- 30-day window – RR = 0.89 [0.71, 1.13]
- 15-day window – RR = 0.98 [0.74, 1.31]
Results – Relation of outcome to exposure – time-varying analysis which correctly
partitions immortal time to unexposed subjects – crude
- 90-day window – RR = 0.94 [0.76, 1.17]
- 15-day window – RR = 1.06 [0.80, 1.42]
Results – Relation of outcome to exposure – adjusted analyses – time-fixed
- 90-day window – RR = 0.69 [0.55, 0.86]
- 15-day window – RR = 1.00 [0.79, 1.26]
A major bias was present in observational studies suggesting the effectiveness of inhaled
corticosteroids in preventing readmission and all-cause mortality in patients previously
hospitalized for COPD.
Bias due to
- Inclusion of immortal person-time
- Misclassification of exposure
A subject readmitted after 10 days and did not receive a prescription was considered a
“nonuser”, even if the patient was due to receive a prescription after the 10-day period –
those who incurred the outcome early less likely to be exposed.
A “user” who filed his/her first prescription on the 80th day of follow-up – immortal for
the first 80 days.
Therefore – nonusers permitted to have endpoints at any time during the initial 90-day
period, and particularly early, whereas users must receive their first prescription before
the event.
Bias further accented by misclassifying person time as “exposed” even before users
receive their first prescription.
Bias is corroborated by the finding that it is a function of the length of the exposure
period – increasing immortal time, increasing bias.
Bias is not specific to inhaled corticosteroids – also applied for beta-agonists.
This bias systematically underestimates the effect.
The study by Sin and Tu – hailed as an exciting study for COPD – but puzzling – 30%
reduction in all cause deaths could be obtained with as little as a single prescription for
inhaled corticosteroids?
Uncertainty remains about the effectiveness of inhaled corticosteroids in COPD.
DL comments – Immortal time bias
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Two ways of thinking about it
- Immortal time increases the relative likelihood of an event in the unexposed
cohort, since all patients with events occurring during the period of immortal
person time are allocated to the unexposed cohort, whether they would have
been exposed or not.
- Patients contribute both events and denominator-time to the unexposed cohort,
whereas they only contribute denominator-time to the exposed cohort.
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Immortal person time is a form of selection bias and is not amenable to adjustment using
standard confounder techniques.
Two ways of handling it
- Allocate immortal person-time to the unexposed cohort.
- Begin follow-up at the point of exposure – do not count immortal person-time –
do not count what would be immortal person-time for the unexposed patients if
they had been exposed.
Suissa S. Inhaled steroids and mortality in COPD: bias from unaccounted immortal time. Eur
Respir J, 23(3): 2004.
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An observational study has claimed to adjust for immortal person-time by defining time
zero by ICS exposure (Soriano JB, Vestbo J, Pride NB, Kiri V, Maden C, Maier WC. Eur
Respir J, 20: 2002).
Objective – Show that the ITT method used by Soriano et al, by its approach to cohort
formation and hierarchical exposure definition, introduces immortal time bias.
Data source – Saskatchewan Health
Study cohort – start of regular treatment with ICS or bronchodilators.
Comparison – Effectiveness of ICS vs bronchodilator therapy
Outcome = all cause mortality – all deaths within 6 months of cohort entry excluded.
Exposure classification
- Regular treatment = first dispensing of three or more prescriptions of a study
drug.
- Subjects assumed to remain users until the end of follow-up.
- Hierarchical exposure classification
 First, identify exposed.
 Unexposed reference group defined by subjects who did not receive ICS
during follow-up, but received regular therapy with abronchodilator.
- Exposed patients – hierarchical intention-to-treat for ICS exposure – ICS was the
group first identified by regular use of ICS, irrespective of whether a subject was
already a regular user of bronchodilators.
- Comparison group – hierarchical intention-to-treat – not really ITT at all for the
comparison group – regular users of bronchodilators who were not regular users
of ICS at any time during follow-up.
Follow-up occurred prospectively from the point of identification of regular drug use, in
contrast to the situation explored in Suisa 2003, when follow-up included immortal
person time.
Immortal time bias – due to hierarchical exposure classification
- In contrast with the immortal time bias demonstrated in Suissa 2003, this
immortal time bias arises from the exclusion of immortal time.
- Exposed patients likely have had bronchodilator therapy before ICS – therefore
incurred immortal person time during which they were unexposed.
- A large amount of person-time in which patients were unexposed is therefore
ignored among those who did not experience the event during the immortal
period – equivalent to removing person-time from the denominator of the
unexposed rate, while fixing the number of events in the numerator.
- This occurs because t=0 is not defined from time since diagnosis, but, rather, is
defined from time of regular drug use
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If exposed patients had instead died during the immortal period, their deaths
would have contributed to the unexposed cohort – however, this person-time is
ignored
- The rule that person time and events should accrue in the same group is violated.
Immortal time bias – due to selection of time zero as the first of three prescriptions
- Time from first to the third prescription is immortal.
- Patients not included if they die after the first or second.
- During the immortal time, any deaths would lead to the subject being allocated
to the reference group, increasing the event rate of the reference group relative
to the exposed group for that period of time.
- Time zero should be defined as the date of the third prescription.
Analysis
- CPH – time fixed and time-dependent.
- Hierarchical ITT vs conventional ITT – where all patients are analyzed according
to the first regular therapy.
- According to treatment received – where crossing patients have patient-time
allocated first to bronchodilators, then to ICS.
- Alternate definition of time zero.
5645 subjects newly treated for COPD between 1990-1999 – 1738 regular users of
bronchodilators, 951 regular users of ICS, 993 regular users of bronchodilators who
became regular users of ICS.
Results – RRs adjusted for age at cohort entry and sex, and occurrence of COPD
hospitalizations and use of other COPD medications dispensed during the 6 months prior
to cohort entry – using the first prescription as cohort entry
- Hierarchical ITT – RR = 0.66 [0.57, 0.76]
- Conventional ITT – RR = 0.75 [0.62, 0.90]
- According-to-treatment analysis – RR = 0.85 [0.73, 0.98]
Results – adjusted RR using the first prescription as cohort entry
- According-to-treatment – RR = 0.94 [0.81, 1.09]
Immortal time biases identified in this study, implying that the effectiveness of inhaled
corticosteroids in COPD remains debatable.
Phillips C. “…only shows correlation, not causation…” (http://epology.blogspot.com/2010/10/only-shows-correlation-not-causation.html). Ep-ology by Carl V.
Phillips: October 8, 2010 (Accessed October 13, 2010)
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“Only shows correlation, not causation” is a phrase frequently taken as showing the
observational studies can only show a correlation between the proposed cause and
effect, without directly showing causation.
This is correct. However, the implication is that RCTs can show causation.
No study design allows us to observe causation – all quantitative studies are based on
“mere” correlation.
What is causation? Counter-factual definition: E causes D if and only if D occurs when E
occurs, but not otherwise – cetaris paribus, save for those factors which may be
intermediate steps on the way from E to D.
If this is ever true for an individual, you can say for the entire class of E and D, that “E
sometimes causes D”, or, rather, that “E causes D”.
E and D are framed in terms of a specific individual.
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Counterfactual – because for one precisely defined E, it is only possible to observe a
world where E occurs, or one where it does not occur, but not both.
We can deal with the counterfactual conundrum by observing something as similar as
possible to the counterfactual states of E that did not occur.
But even a highly confident educated conclusion about sameness is not the same as
observing “causation” – this is true for both observational and experimental studies.
The advantage of RCT is better control of confounding – balanced covariates on average.
Some covariates may be unbalanced purely by chance – but the resulting confounding is
no longer systematic – it is random, and can be captured using random error statistics.
This is not the same as going from seeing correlation to seeing causation – one of the
many possible non-causal explanations for an association has been ruled out, increasing
your confidence in a hypothesis of causation – but the causation is nonetheless never
observed.
The conclusion about causation is in the mind of the observer, not the data.
West SG. Alternatives to randomized experiments. Current Directions in Psychological Science,
18(5): 2009.
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RCT – not always appropriate.
Campbell’s perspective
o Identify plausible threats to validity of causal inference (Shadish, Cook, &
Campbell, 2002) – DL comment – Campbell is credited as the originator of the
internal / external validity distinction.
 Statistical conclusion
 Internal – threats relevant to causal inference.
 Construct
 External
o Incorporate design elements to reduce the treat.
o Unanticipated threats revealed by mutual criticism.
o Randomization is useful because it rules out the widest range of plausible
threats.
Rubin’s perspective
o Potential-outcomes perspective – Holland, 1986; Rubin 2005 – A key figure in the
counterfactual model of epidemiologic causation.
o Simulated counterfactual comparisons, based on explicit, ideally verifiable
assumptions.
o Randomization is a method of comparison – balance is verifiable – treatment and
control groups theoretically equal, on average.
Broken RCTs
o Attrition – Modern techniques allow adjustment for MCAR and MAR – may
attempt to verify or convert missingness to MAR by measuring predictors of
participation.
o Treatment nonadherence – IV analysis making use of the exclusion restriction –
the effect of treatment assignment operates fully through the actual treatment
and not through other processes – may remove effect due to nonadherers.
Alternative designs
o Regression Discontinuity Design (RDD)
o ITS
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Observational designs
How well do alternative designs work?
o Initial reviews pessimistic about comparability of randomized and nonrandomized designs.
o This may have been due to other features of methodological quality –
confounding.
o More focused comparisons considering available studies sharing identical
treatment conditions suggest that ITS and RDD have led to estimates that did not
differ from those produced by randomized experiemnts.
o Observational studies also produced similar causal-effect estimates given a
control group of similar participants – results may, however, be vary disparate
from RCTs until appropriate adjustment for biases are performed.
o Similar findings may be obtained.
o However, RCTs are more reliable – operate under fewer assumptions, lead to
most transparent causal inferences.
NRS designs allow scientists to address a wider range of important research questions
rather than abandoning or altering them. Alternative designs do not depend on having a
sufficient number of units to randomize – may be used to evaluate large scale
interventions. Alternative designs may also permit more transparent generalization of
causal effects.