observational epidemiologic studies descriptive (incidence, prevalence) analytic (associate...

Observational Epidemiologic Studies

Descriptive (incidence, prevalence)

Analytic (associate characteristics of

population with risk of disease)

Study type 1

Epidemiology - Design and Bias EvaluationSpring 2005

Reference:1. Szklo M and Nieto FJ. Epidemiology – Beyond the Basics. Aspen Publishers, Maryland 2000.2. Rothman K and Greenland S. Modern Epidemiology. Lippincott-Rven Publishers, Philadelphia, 1998.3. Rothman K. Epidemiology – An Introdution. Oxford University Press, New York, 2002.4. Kelsey JL, Whittemore AS, Evans, and Thompson WD. Methods in Observational Epidemiology. Oxford University Press, New York, 19965. Kleinbaum DG, Kupper LL, and Morgenstern H. Epidemiologic Research. Van Nostrand Reinhold, New York. 1982.

Study type 2

Types of Observational studies

A. Ecologic

B. Cross-sectional

C. Cohort 1. Prospective cohort 2. Retrospective (non-concurrent) cohort

D. Proportional mortality studies

E. Case-control

Study type 3

Variants of the case-control design

Case-based case-control

Case-cohort

Case-crossover

Study type 4

Steps in epidemiologic research

1.Define questions/hypothesis based on present states of knowledge.

2. Choose appropriate study design.

3. Define groups for comparison (e.g., cases vs. controls, exposed vs. nonexposed).

4. Define exposure variable(s), outcome variables, and measure of its frequency, and primary measure of association.

Study type 5

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5. Define extraneous variables to be measured.

6. Develop or choose measurement instruments that are valid and reliable.

7. Determine sample size.

8. Develop protocol, staff training .

9. Recruit subjects, collect data, quality control procedures.

10. Process data.

Study type 6

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11. Analyze data.

A. Determine if valid statistical association exists. 1. Rule out chance. 2. Rule out bias.

B. Determine if there are effect-modifiers of the association.

C. Judge if association is causal

12. Discuss practical significance of findings.

Study type 7

Studies making observations on groups of individuals vs.

individuals • Studies using group level data are usually

called ecological studies• Two main points about ecological studies

– Weak design for identifying cause and effect associations because of ecological fallacy

– In some study situations group-level measures may actually provide better inference than individual-level measures

Study type 8

Example from Szklo and Nieto of grouped datafrom cohorts in the Seven Countries Study

Study type 9

Ecological Fallacy

• Cannot tell whether the predictor and the outcome are related at the individual level

• In this example: cannot tell whether the individuals in the cohorts eating less saturated fat are the individuals who are experiencing a higher rate of heart disease

• Sometimes called confounding at the group level

Study type 10

Confounding in group data

• If no ecological fallacy, still left with possible confounding: some third variable really causing the increase in risk

• Difficult to control for because measures may not be available

• Even if data available, don’t know relationship of confounding variable to other two variables at individual level

Study type 11

Advantages of group data/ecological studies

1.Inexpensive: secondary data already

collected (vital statistics, disease registries, HMO’s, etc)

Study type 13

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2. Rapid test of hypothesis: a. Idea that ecological studies are hypothesis-generating doesn’t reflect their usual purpose b. If hypothesized risk factor is associated

with disease, it may well be seen in group level data

Study type 14

3. Can overcome “threshold” problem: exposure is so universal that effect is difficult to detect in one setting

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Study type 15

4. Some disease transmission dynamics can only be studied at group level (eg, herd immunity and infectious disease transmission)

Allows global measures of group characteristics (e.g., type of health care system)

Allows tests of area-level interventions (eg, closing of a public hospital)

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Strategies that can strengthen inferences from ecological Studies:1.Multiple kinds of comparisons to strengthen inference of association; eg, across geographic areas and over different time periods

Example: Valerie Beral’s study showing inverse association between average family size and ovarian cancer mortality using comparisons among different birth cohorts, different countries, and different social and ethnic groups (Lancet, 1978)

Study type 17

2. “Small Area” analysis: Used in health services research to investigate variation within small geographic areas.

Reduce confounding by comparing small areas from a larger area thought to be fairly homogeneous on potential confounders (SES, disease prevalence)

Example: Wennberg’s study of variation in rates of surgical procedures in 6 areas of Vermont with similar disease prevalence (Medical Care, 1987)

Study type 18

3. Mixed studies that collect data on individuals but use secondary group data for rare outcomes (multilevel studies)

Doesn’t avoid ecological fallacy but reduces confounding by key measures at individual level

Using group data may make study feasible that would be otherwise prohibitively expensive

Study type 19

Example: Bindman’s study of health care access (personal data) and rates of preventable hospitalizations (group data)in California medical service areas (JAMA, 1995)

Study type 20

Cohort Study Design

1.Gold standard because exposure/risk factor is observed before the outcome occurs

2. Randomized trial is a cohort design in which the exposure is assigned rather than observed

3. Other study designs can be understood by the way in which they sample the experience of a cohort

Study type 21

4. Easiest design to understand because it explicitly defines the study base as a cohort

5. Measures individual characteristics before disease occurrence fulfilling the temporal order required for cause and effect (but is not the only study design that can do this).

6. Provides conceptual basis for understanding sampling strategies of case-control, case-cohort, and cross-sectional designs

Study type 22

Study type 23

Study type 24

Time of Follow-up Begin End

Cohort StudyS

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Sub

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s dy

ing

or

lost

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ollo

w-u

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X = dead L = lost D = disease

XL

D X L

X

D L

DX

X

X

DD

DD

D

DD

Study type 25

Fixed (closed) v.s. dynamic (open) cohort

Fixed: When the exposure groups in a cohort study represent groups that are defined at the start of follow-up, with no movement of individuals between exposure groups during the follow-up, the exposure groups are sometimes called fixed cohorts.

Dynamic (open): It describe a population in which the person-time experience can accrue from a changing roster of Individuals.

Study type 26

Cohort Design

Prospective cohort design:

Present exposure data --> Future diseases

Retrospective cohort design:

Past recorded exposure --> Diseases accumulated to the present

Study type 27

Past Present Future

Select cohort:classify as to exposure status

Follow to see if disease develops

Identify cohort defined in past

Determine whether disease has develop

On basis of existing recordsclassify individuals in cohort as to pastexposure status

Study type 28

Groups Investigated in Cohort Studies

A. General population sample

B. Select groups of the population

1. Special groups - professional, insured, alumni, veteran, etc.

2. Exposed groups - medically or toxically exposed, occupational, etc.

Study type 29

Defining Exposed/Nonexposed Groups for Comparison

I. Sources of exposure data A. Types 1. Records (e.g., hospital, employment) 2. Interviews, questionnaires 3. Direct examination 4. Indirect measures of exposure estimated from investigating the environment

B. Retrospective cohort studies use records or indirect measures and generally obtain less detail on exposure (and confounding)

Study type 31

II. Defining nonexposed

A.Internal comparison group

B. External comparison group 1. Common in retrospective cohort (especially occupational studies) 2. Drawbacks a. Typically assumes exposure is rare in comparison group b. Wrong comparison group (e.g., Healthy worker effect) 3. Must be certain endpoint is comparably defined

Study type 32

III. Other considerations

A. Exposed should be truly “exposed”; Non exposed truly “nonexposed.”

B. Exposure should be measured similarly in exposed and nonexposed.

C. Can select exposed/nonexposed groups with equal or unequal sampling fraction

D. Matching

E. Problem of homogeneity of exposure

Study type 33

Follow-up

I. Objective

A. Uniform and complete follow-up of all cohort groups

B. Complete ascertainment of outcome events

C. Standardized diagnosis of outcome events

Study type 34

II. Considerations

A. Length of follow-up is related to : 1. The natural history of the disease 2. The incubation period (latency) between exposure and disease

B. Obtain tracing information at baseline 1. Name, address, phone number 2. Age, birthdate, states of birth, maiden name 3. Social Security Number, driver’s license number 4. Name and address of friends, employer, physician

Study type 35

III. Methods

A. Direct contact throughout the study 1. Correspondence, telephone 2. Re-examination

B. Indirect surveillance 1. Hospitalizations/physician records 2. Disease registries 3. Death records 4. National Death Index 5. Social Security Administration 6. Pension/retirement associations

Study type 36

Sources for tracing subjects

Post office Tax recordPhone directory Prison systemRelatives Medical recordNeighbors Family physicianDrivers Bureau National Death IndexSchools Commercial tracing firmVeterans groups Credit bureau UnionChurchEmployment (payroll files)Pension/Retirement association

Study type 37

Study type 38

Cumulative Incidence

Cohort is followed a uniform length of time

D D Total E a b N1 Risk = a/N1

E c d N0 Risk = c/N0

a/N1

Relative Risk = c/N0

Study type 39

Life table analysis: (Survival Analysis)Example: Assume that 100 persons have received cardiac transplants and that we wish to estimate the probability of surviving the surgery. The data was follows:

Time Individual number of loss to (interval) at risk events observation 1 100 10 10 2 80 10 0 3 70 10 10 4 50 10 10 5 30 10 0 6 20 10 0

Study type 40

Probability of Under observation Died during Dying during Surviving interval at time interval interval through interval

1 100 10 .1 .9 2 80 10 .125 .875 3 70 10 .143 .857 4 50 10 .2 .8 5 30 10 .333 .667 6 20 10 .5 .5 Cumulative probability of surviving 24 months is (.9) (.875) (.857) (.8) (.667) (.5) = 0.18

Life table calculation:Study type 41

Survival CurveStudy type 42

Assumptions in the estimation of cumulative incidence based on survival analysis

1.Uniformity of events and losses within each interval:

If risk increases or decreases too rapidly within a giving interval, then calculating an average risk (from our example,0.18) over the interval is not fully informative.

One good way is to shortening the interval for calculation.

Study type 43

2. Independence Between Censoring and Survival:

One need to assume that the censored observations have the same probability of the event (after censoring) as thoseremaining under observation.

Study type 44

Examples of non-independence Between Censoring and Survival:

In an outcome observation of lung cancer,participants dying from coronary heart disease are censored. Since lung cancer and CHD share an important risk factor, smoking, it is possible that individual dying from CHD would have had a higher risk of lung cancer if they had not died from heart disease. The risk of smoking will be under-estimated.

Study type 45

3. Lack of Secular Trends

In studies in which the accumulative time covers an extended period, the decision to pool all individuals at time 0 assumes lack of secular trends with regard to the type and characteristics of these individuals that affect the outcome of interest.

Study type 46

It would not be appropriate to carry out asurvival analysis pooling at time 0 all HIV positive individuals recruited into a cohortaccrued between 1995 and 1999 – that is, both before and after a new effective treatment (protease inhibitors) became available.

Examples of lack of secular trend

Study type 47

Incidence DensityCohort has variable lengths of follow-up, due to:1. Losses to follow-up2. Deaths3. Termination of the study4. No longer “at risk” (able to develop the disease)

D D Person Years E a b N1 Incidence rate = a/N1

E c d N0 Incidence rate = c/N0

a/N1

Rate ratio = c/N0

Study type 48

Assumptions in the estimation of incidence rates based on person-time

1.Assumptions of independence between censoring and survival

2.Lack of secular trends

Study type 49

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3. Estimated risk apply equally to any time unit within the interval

n persons followed during t units of time are equivalent to t persons observed during n units of time.

The effect resulting from the exposure is not cumulative within the follow-up interval of interest

Study type 50

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For example, the risk of chronic bronchitis for 1 smoker followed for 10 years is certainly not the same as that of 10 smokers followed for 1 year, In view of strong cumulative effect of smoking.

Study type 51

Incidence Rate

average risks (cumulative incidence): measured with individuals as the unit in the denominator; are conceptually tied to the identification of specific cohorts of individuals,

Incidence rates:have person-time as the unit of measure;can define the comparison groups in terms of person-time units that do not correspond to specific cohorts of individuals.

Study type 52

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Thus, an individual whose exposure experience changes with time can, depending on details of the study hypothesis, contribute follow-up time to several different exposure-specific rates.

Study type 53

The main guide to the classification of persons or person-time is the study hypothesis, which should be spelled out in as much detail as possible.

In studies with chronic exposures, it is easy to confuse the time during which exposure occurs with the time at risk of exposure effects.

Classification of Person-TimeStudy type 54

Time of employment: a time during which exposure accumulates

Time at risk for exposure effects:must logically come after the accumulation of a specific amount of exposure, because only after that time can disease be caused or prevented by that amount of exposure.

in occupational studies, time of employment is sometimes confused with time at risk forexposure effects:

Study type 55

Comments:1.The length of these two time periods have no inherent relation to one another.

2. The time at risk of effects might well extend beyond the end of employment. 3. It is only the time at risk of effects that should be tallied in the denominator of incidence rates for that amount of exposure

(Continue)Study type 56

In a study of the delayed effects of exposure to the atomic bomb, the exposure is almostinstantaneous, but the risk period during which the exposure has an effect may be very long, perhaps lifelong, and the risk forcertain diseases may not go up immediately after exposure .

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Study type 57

There is no way to estimate exposure effects without making some assumption about the induction time.

For example, one year of induction time for the atomic bomb subjects in Japan. Disease occurred within one year of the exposure were not considered as an outcome.

Hypothesis of Induction timeStudy type 58

If the investigator does not have any basis for hypothesizing induction period, s/he can:

=> estimating effects according to categories of time since exposure.

In an unbiased study, we would expect the effect estimates to rise above the null value when the minimum induction period has passed.


This procedure works best when the exposure itself occurs at a point or narrow interval of time, but it can be used even if exposure is chronic, as long as there is a way to define when a certain hypothesizing accumulation of exposure has occurred.

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Study type 60

Categorizing Exposure

One problem to consider is that the study Hypothesis may not provide reasonable guidance on where to draw the boundary between exposed and exposed.

Study type 61

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1. exposure as continuous: it is not necessary to draw boundaries at all, but rather to use the quantitative information from each individual fully either by using some type of smoothing method, such as moving averages, or by putting the exposure variable into regression as a continuous term.

Study type 62

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2. Rate calculations: will require a reasonably sized population within categories.

It should be possible to form several cohorts that correspond to various levels of exposure. There are two ways to allocate the person-times of exposure:

Study type 63

a. An individual who passes through one level of exposure along the way to a higher level would later have time at risk for disease that theoretically might meet the definition for more than one category of exposure.

Usually the time is allocated only to the highest category of exposure that applied.

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Study type 64

b. The following time that an individual spends at a given exposure intensity (induction time) could begin to accumulate as soon as that level of intensity is reached.

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Once the person-time spent at each category of exposure has been determined for each study subject, the classification of the disease events (cases) follows the same rules.

Study type 65

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Allowing for a 5-year induction period

Study type 66

c. One can also define current exposure according to the average (arithmetic or geometric mean) intensity or level of exposure up to the current time, rather than by a cumulative measure.

In the occupational setting, the average concentration of an agent in the ambient air would be an example of exposure intensity, although one would also have to take into account any protective gear that might affect the individual’s exposure to the agent.


Intensity of exposure is a concept that applied to a point in time, and intensity typically will vary over time. Studies that measure exposureintensity might use a time-weighted average ofintensity, which would require multiplemeasurements of exposure over time.

The weight for each exposure intensity wouldequal the amount of time that an individual isexposed to that intensity.


For some events, such as death, it is not difficult to determine the time of the event.

For others, such as human immunodeficiency virus (HIV) seroconversion, the time of the event can be defined in a reasonably precise manner (the appearance of HIV antibodies inthe blood stream), but measurement of the time is difficult.

Timing of Outcome EventsStudy type 69

start with at least one written protocol to classify subjects based on available information.

For example, seroconversion time may be measured as the midpoint between time of last negative and first positive test.

Suggestions for determiningoccurrence of Outcome Events

Study type 70

For unambiguously defined events, any deviation of actual times from the protocol determination can be viewed as measurement error.

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Study type 71

Ambiguously timed diseases, such as cancers or vascular conditions, are often taken asoccurring at diagnosis time, but the use of aminimum lag period is advisable whenever a long latent (undiagnosed) period is inevitable.

It may sometimes be possible to interview cases about the earliest onset of symptoms, but such recollections and asymptoms canbe subject to considerable error and between-person variability.


A. Bias related to follow-up In principle, a cohort study could be used to estimate average risks, rates, and occurrence times. Loss of subjects during the study period will prevent direct measurements of these averages, since the outcome of loss subjects is unknown.

Key Potential Biases in Cohort StudiesStudy type 73

Subjects who die from competing risks (outcomes other than the one of interest) likewise prevent the investigator from estimating conditional risk directly.

When loses and competing risks do occur, one may still directly estimate the incidence rate, where average risk and occurrence time must be estimated using survival (life-table) methods.


A substantial number of subjects lost to follow-up can raise serious doubts about thevalidity of the study.

Follow-ups that trace less than about 60% ofsubjects are generally regarded withskepticism, but even follow-up of 70% or 80%or more can be too low to provide sufficientassurance against bias if there is reason tobelieve that loss to follow-up may be correlatedwith both exposure an disease.


B. Bias related to participation (nonresponse) Participants and non-participants may differ on their exposure status or disease outcome.

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C. Bias of misclassification of exposure

1. Change in exposure level over time may lead to random error and/or, if related to disease outcome, may lead to bias.

2. Misclassification due to measurement error.

Study type 76

D. Bias related to observation and detection of disease

1. Those with certain exposure may be followed more intensively for disease than those without the exposure (diagnostic suspicion bias)

2. Unmasking bias (innocent exposure leads to greater likelihood of detecting disease)


Selected cohort 1000

250 exposed 750 unexposed

13% refused participation 14% refused participation 250-32=218 750-105=645

14% of those entering 14% of those entering were lost to follow-up were lost to follow-up 218-35=183 645-105=540

183 remaining 540 remainingGreenland. Response and follow-up bias in cohort studies. Am J Epid 1977; 106: 184-7

Effects of Study Loss in Cohort StudyStudy type 78

Effects of Study Loss in Cohort Study

Study outcome:

Disease No Disease TotalExposed 16 167 183Not Exposed 23 517 540 39 684 723

16/183 Relative Risk = = 2.05 23/540

Study type 79

Evaluation of Extremes of Outcome

A. All of exposed developed disease None of unexposed developed disease


83/250 Relative Risk = = 10.83 23/750

Study type 80

Evaluation of Extremes of Outcome

B. None of exposed developed disease All of unexposed developed disease


16/250 Relative Risk = = 0.21 233/750

Study type 81

Case-Control StudiesStudy type 82

Case-Control Studies

Potential Advantages

A. Quick and less expensive

B. Well-suited to evaluation of diseases with long latent periods

C. Optimal if disease is rare

D. Can examine multiple etiologic factors for a single disease.

Study type 83

Selection of Cases

A. Sources: Hospital Physicians’ office Disease registries Vital statistics bureau

B. Type: General population vs. special group Incident and/or prevalent cases Representativeness

Study type 84

C. Definition:

1. Should truly be a case: validation of diagnosis using objective criteria

2. Should represent a defined eligible population: inclusions and exclusions should be specified clearly

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Study type 85

3. Detection issues that may be important

a. Variation among cases in medical care, self or medical diagnostic procedures

b. Must a series of sequential events be present for detection to occur? E.g., perceived symptoms followed by drug use

Study type 86

Pathway Between A Disease and A DiagnosisDisease person at home Referal for definitive test procedure?Clinical signal Procedure performed?Is signal overt? Positive result?Medical surveillance Patient is diagnosed Diagnostic suspicion? “case”

Exploratory exam?

Study type 87

Selection of Controls - Principles

A. Controls should be selected form the same population - the source population or study base – that gives rise to the cases.

Case-control studies can be viewed as efficient versions of cohort studies, in which the relative sizes of the denominators of the incidence rates are estimated by taking a sample of the source population.

Study type 88

B. Controls should be selected independently of their exposure status and should be representative of the source population with respect to exposure.


C. For unmatched control selections, the probability of selecting any potential control subject should be proportional to the amount of time that he or she contributes to the denominator of the rates that would have been calculated, had a cohort study of the source population been undertaken.

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Study type 90

In doing so, the sampling rate for exposed and unexposed controls will be the same,And the ratio of pseudo-rates will be equalto the incidence rate ratio in the source population.

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For example, if in the source population one subject contributes twice as much person-time during the study period as another subject, the first subject should have twice the probability of the second of being selected as a control in the case-control study.

Study type 91

D. If a subject’s exposure may vary over time, cases’ exposure (or exposure history) at the time of disease occurrence should be used as the indicator of exposure.


one must sample controls at a steady ratethroughout the study period and use the control’s exposure (or history) at the time of sampling; exposure after the time of selection must be ignored.

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E. To ensure that the number of exposed and unexposed controls will be in proportion to the amount of exposed and unexposed person-time in the source population:

Study type 93

F. The time during which a a subject is eligible to be a control should be the same in which that individual is eligible to be a case, if the disease should occur.


One way to implement this rule is to choose controls from the set of individuals in the source population who are at risk of becoming a case at the time that the case is diagnosed; this set is sometimes referred to risk-setfor the case.

Controls sampled in this manner are matched to the case with respect to sampling time; thus, if time is related to exposure, the resulting data should be analyzed as matched data.


It is also possible to enforce the rule in unmatched sampling if one knows the time interval at risk for each population member; one then selects a control by sampling members with probability proportional to time at risk and then randomly samples a time to measure exposure within the interval at risk.


A. General population Controls

1. Useful when the series of cases is population-based

2. Select from a population registry or random digit dialing (RDD)

3. Advantages: generalizability

Sources of ControlsStudy type 97

B. Hospital controls

1. Select from other hospital admissions

2. Advantages:

a. Feasibility b. High cooperation rate c. Have been ill, therefore, “mental set” is similar (potentially less recall error), d. Makes cases and controls similar with respect to some determinants of hospitalization

Study type 98

3. Disadvantages:

a. Selection (Berkson’s) bias

b. Controls may have a condition that shares etiologic features with the disease under study

4. Preferable to select from many diagnostic categories

Study type 99

C. Neighborhood Controls

1. Similar to general population but also matches on factors related to geography

2. Select by a modification of random digit dialing on “walking algorithm”

D. Others: Friends Siblings Co-workers

Study type 100

A.Goal: avoid selection bias

B. Draw controls from same reference population as cases

C. Subjects not at risk for disease should be excluded from control group

D. If cases are excluded because they are not at risk for exposure, similar criteria should be applied to controls

Guidelines for control selectionStudy type 101

F. Individuals with medical conditions known to be associated with the exposure under study (positively or negatively) usually should be excluded from the control series

e.g., aspirin exposure for MI: rheumatoid arthritis or peptic ulcer controls

G. Customary rule: Hospital controls should be selected from more than one disease category.


H. Ideally, controls should undergo the same diagnostic procedures as cases. However, this often isn’t practical.

I. Exposure status and confounders must be able to be measured comparably in cases and controls. Cases or control status must be defined before exposure determined.


J. Problems: agents that cause one disease in an organ often cause other diseases of that organ e.g., smoking -> lung cancer and chronic bronchitis may bias association towards the null.


A. Increased cost

B. Useful when no single control group is best

C. Useful to compare findings among groups

D. If findings contrast may help determine etiology

e.g., association of Hodgkins Disease and tonsillectomy using spouse controls OR= 3.1 using sibling controls OR=1.4 So, same aspect of life-style is childhood, perhaps an infection, may be a cause of HD.

F. Caveat: may be hard to explain the results

Multiple Control GroupsStudy type 105

A.Refers to the selection of a reference series - unexposed subjects in a cohort study or controls in a case-control study – that is identical, or nearly so, to the index series with respect to the distribution of one or more potentially confounding factors.

Individual matching: performed subject by subject frequency matching: performed for group subjects

MatchingStudy type 106

B. In a cohort study, the index subject is exposed, and one or more unexposed subjects are matched to each exposed subjects.

C. In a case-control study, the index subject is a case, and one or more controls are matched to each case.


D. Frequency matching involves selection of an entire stratum of reference subjects with matching-factor values equal to that of a stratum of index subjects.

e.g., case: 50% male and 50% female control: also select a combination of 50% male and 50% female


A.The chief importance of matching in observational studies stems form its effect on study efficiency.

B. In a cohort study, without competing risks or losses to follow-up, no additional action is required in the analysis to control confounding of the point estimate by the matching factors, because matching unexposed to exposed prevents an association between exposure and the matching factors.

Purpose and Effect of MatchingStudy type 109

C. In case-control studies, if the matching factors are associated with the exposure in the source population matching requires control by matching factors in the analysis, even if the matching factors are not risk factors for the disease.


Hypothetical source population: 2,000,000

Male Female

diseased

total

exp unexp exp unexp

4500 50

900,000 100,000

100 90

100,000 900,000

RRmale= RRfemale=10 10

Crude RR = 32.9 Gender is a confounder

Study type 111

Matching in cohort study

1,000,000 exposed

100,000 exposed

10% sample

Male : Female =9:1

90,000 Male

10,000 Female

Male : Female =9:1

90,000 Male

10,000 Female

Study type 112

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Male Female

diseased

total

exp unexp exp unexp

450 45

90,000 90,000

10 1

10,000 10,000

RRmale= RRfemale=10 10

Crude RR = 10 Confounder controlled!

Study type 113

Matching in case-control study

4,740 cases 1,995,260 non-cases

4,550 Male190 Female

Male : Female = 24 : 1

Using frequency match select 4,740 controls

Sampled 4,550 Male and 190 Female controls

4,550/995,450 selection proportion in male non-cases

190/999,810 selection proportion in female non-cases

995,450 Male 999,810 Female

Study type 114

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Male Female

cases

controls

exp unexp exp unexp

4500 50

4092 457

100 90

19 171

ORmale= ORfemale=10 10

Crude OR = 5 Confounding!

Study type 115

In a cohort study, matching is of unexposed to exposed. It is undertaken without regard to disease status, which is unknown at the start of follow-up, and it alters the distribution of the matching factors in the entire sourcepopulation from which study cases arise.

What accounts for this discrepancy?

Study type 116

In contrast, matching in a case-controlstudy involves matching non-diseased todiseased and thus affects only the distribution of controls; if the matching factors are associated with exposure, theselection process will be differential withrespect to both exposure and disease,thereby resulting in selection bias.

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Study type 117

Suppose the one anticipates that age distribution for cases is shifted strongly toward older ages, compared with the age distribution of the entire population.

As a result, without matching, there may be some age strata with many cases and few controls, and others with few cases and many controls. If controls were matched to cases by age, the ratio of controls to cases wouldinstead be constant over age strata.

Matching and EfficiencyStudy type 118

A. Research limitation: If a factor has been matched in a study, it is no longer possible to estimate the effect of that factor from the stratified data alone, since matching distorts the relation of the factor to the disease.

B. It is Still possible to study the factor as a modifier of relative risk by seeing how the odds ratio varies across strata.

C. Cost $

Cost of MatchingStudy type 119

A. Matching that harms statistical efficiency, such as case-control matching on a variable associated with exposure but not disease.

B. Matching that harms validity, such as matching on an intermediate between exposure and disease.

C. Matching that harms cost efficiency, such as matching on a variable not associated with disease and exposure.

OvermatchingStudy type 120

Besides enhancing efficiency, here are some situations in which matching is desirable or even necessary.

A. If the process of obtaining exposure and confounder information from the study subjects is expensive, it may be more efficient to optimize the amount of information obtain per subject than to increase the number of subjects.

B. In the process of control selection, neighborhood, sibling, spouse, friend, and occupation are sometimes chosen and were inevitably matched on some factors.

Why perform Matching?Study type 121

Selection of neighborhoods, friends, sibling, spouse,and occupation, may induce bias under ordinary circumstances. For example, friendship my be related to exposure (e.g., through lifestyle factors), but not todisease. As a result, use of such friend controls could entail a statistical efficiency loss.

The decision to use convenient controls should weightany cost savings against any efficiency loss and biasrelative to the viable alternatives ( e.g., general population controls)

(however)

Study type 122

C. Matching is sometimes employed to achieve comparability in the quality of information collected.

A typical situation in which such matching might be undertaken is a case-control study in which some or all of the cases have already died and surrogates must be interviewed for exposure and confounder information. Many investigators prefer to match dead controls to dead cases.


A. Improved precision Efficiency of matching often expressed as ratio of variance of odds ratio with M controls per case to the variance of odds ratio with infinite controls per case.

Efficiency = M/M+1 So, one control is 50% efficient four controls is 80% efficient Little gained beyond M=4

Multiple Controls per CaseStudy type 124

B. Useful when controls plentiful and inexpensive and/or when cases are rare.

C. Varying number of controls per case is possible

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Study type 125

A. Most commonly obtained by interview or records.

B. Must be obtained comparably in cases and controls.

C. Greater potential for interviewer bias and need for blinding interviewers than in cohort studies.

Classifying ExposureStudy type 126

D. Latency period and temporality considerations if measurements made directly on study subjects.

E. Recall bias

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Study type 127

I. Selection bias

A. When case and control are not selected from the same (or similar reference population). (e.g., Berkson’s bias)

B. Nonresponse

C. Cases died form competing risks

Potential Bias Occurred in Case-Control Studies

Study type 128

II. Measurement Biases

A.Diagnostic suspicion

B. Exposure suspicion

C. Recall

D. Random (Non-differential) misclassification


Various Designs of Case-Control Study

Study type 130

Case-based case-control studyCases and noncases are identified at a given point intime among living individuals. This study is carried out “cross-sectionally” (ie, cases and controls are identified at the same time), cases must necessarily occur over given time period prior to their inclusion in the study.

Thus, it is necessary to assume that the cases who survive through the time with regard to the exposure experience and that if exposure data are obtainedthrough interviews, recall or other bias will not intrude regarding to their exposure status.

(Szklo and Nieto, Epidemiology- beyond the basic, 2000)

Study type 131

(continue)

• Source of cases is often one or more hospitals or other medical facilities

• Problem is identifying the population who would come to those institutions if they were diagnosed with the disease

• Careful consideration has to be given to factors causing someone to show up at that institution with that diagnosis

Study type 132

Case-based design using prevalent cases: essentially same as cross-sectional design

Study type 133

Sampling within a Cohort Study: Ascertaining all cases and sampling controls from subjects disease free at end of follow-up

Sub

ject

s in

Cas

e-C

ontr

ol S

tudyD

DD

D

D

D

D

D

D

D

D = disease = case C = control (no disease)

CCC

CC

C

CCC

C

Case-Control Study with Case-Based Sampling

Possible bias: Potential controlsnot in study at end of follow-up

Study type 134

To validly compare cases and controls regarding their exposure status, it is necessary to assume that they are originate from the same reference population.

(continue)

Study type 135

Example of case-based design using prevalent

cases• Sampling glioma patients under treatme

nt in a hospital during study period

• Poor survival so patients in treatment will over-represent those who live longest

• Nature of bias variable are not predictable

Study type 136

When cases are identified within a well defined cohort,it is possible to carry out nested case-control orcase-cohort studies.

Case-control study within a cohort are also known as“hybrid or ambidirectional” designs because theycombine some of the features and advantages of both cohort and case-control designs.

Case-cohort Study andNested Case-Control Study

Study type 137

Nested Case-Control Study

Controls are from a random sample of the cohort selected at the time each case occurs. This study design is called a nested case-control design and is based on a sampling approach known as “incidence density sampling” or “risk-set sampling.”

The idea underlying this sampling schemes is that it allows the comparison of cases with a subset of thecohort members at risk of being cases at the timewhen each case occurs - that is, a “risk set” of allcohort members under observation at the time ofeach case’s occurrence.

Study type 139

Study type 140

Nested Case-Control (Incidence Density Sampling)

Sampling within a cohort: Including all cases and sampling controlsfrom subjects disease free at the time each case is diagnosed

Cases = 10 D’s

Controls= 10 C’s

Formedfrom 9 risk sets

Sub

ject

s in

Cas

e-C

ontr

ol S

tudy

D

DD

D

DD

DD

D

D

RiskSet 1

C

RiskSet 2

C

Etc.

C

C

C

C

C

C

C

C

RiskSet 9

Study type 141

A risk set is a set of people in the source Population who are at risk for disease at that time.

The definition of the risk set changes for each case because the identity of the risk set is relating to timing of the case.

If several diseases are to be studied, each one will require its own control group to maintain risk-set sampling.

Risk setStudy type 142

The control series represents the person-time distribution of exposure in the source population.

The probability that any person in the source population is selected as a control is proportional to his or her person-time contribution to the incidence rates in the sourcepopulation.

By this strategy, cases occurring later in the follow-up are eligible to be controls for earlier cases.

Nested Case-Control StudyStudy type 143

Incidence density sampling is the equivalent ofMatching cases and controls on duration offollow-up.

In this situation, it can be demonstrated thatthe estimated exposure odds ratio is a statistically unbiased estimate of the rate ratio.

(continue)

Study type 144

Example of Case-Control Incidence Density

Sampling

• Use cancer registry covering San Francisco County to identify all new cases of glioma during a defined time period

• At time each new glioma case is reported, randomly sample two controls from current residents of San Francisco

Study type 145

Case-cohort Study

Controls are from a random sample of the total cohortat baseline (case-cohort study), thus allowing somecases that develop during follow-up to be part of boththe case and control groups.

Every person in the source population has the samechance of being included as a control, regardless ofhow much time that person has contributed to the person-time experience of the cohort.

Study type 146

Study type 147

Case-Cohort StudySampling within a cohort: Including all cases and samplingcontrols from all subjects at baseline of cohort

Cas

es in

Cas

e-C

ohor

t Stu

dy

Con

trol

s in

Cas

e-C

ohor

t Stu

dy DD

D

C

C

CCC

C

C

CC

C

Study subjects

DD

D

D

D

DD

D = disease = case C = control (no disease)

Study type 148

Case-cohort Study

An important advantage of case-cohort design is thatthe availability of a sample of the cohort (the control group) allows the estimation of risk factor distributionsand the odds ratio is an estimate of the risk ratio ratherthen rate ratio.

If the risk are small, then the risk ratio is approximately equal to the incidence rate ratio, so in many instancesthere may be little difference between the result from a case-cohort study and the the result from a density ornested case-control study.

Study type 149

Selection of Case-Cohort or Nested Case-Control?

The definition of the risk set changes for each case because the identity of the risk set is relating to timing of the case. If several diseases are to be studied, each one will require its own control group to maintain risk-set sampling.

Control sampling for case-cohort study, however,requires just a single sample of people from the rosterof people who constitute the cohort. The same control group could be used to compare with various caseseries, just as the same denominators for calculation ofrisk.

Study type 150

Why use case-control study within a cohort?

It is an efficient approach when additional information that was not obtained or measured for the whole cohortis not needed.

Atypical situation is a concurrent cohort study in which serum samples are collected at baseline and stored in freezers. Once a sufficient number of cases is accruedduring the follow-up, the frozen serum samples for cases(or a sample of cases) and for a sample of controls can be thawed and analyzed.

Study type 151

Why use case-control study within a cohort?A similar situation arises when the assessment of keyexposures or confounding variables requires labor-intensive data collection activities. Collecting thisadditional information in cases and a sample of the total cohort is a cost-effective alternative to using the entire cohort.

(Szklo and Nieto, Epidemiology- beyond the basic, 2000)

Study type 152

Case-crossover

This design is a case-control study analogue of thecrossover study.

A crossover study is an experimental study in which two (or more) interventions are compared, with eachstudy participant acting as his or her own control.

Each subject receives both interventions in a randomsequence, with some time interval between them sothat the outcome can be measured after eachintervention.

Study type 153

Case-crossover

A crossover study thus requires that the effect periodof the intervention is short enough so that it does notpersist into the time period during which the next treatment is administered.

In case-crossover study, all subjects in the study arecases. The control series dose not comprise a differentset of people but, rather, a sample of the timeexperience of the cases before they develop disease.

The control information is obtained from the casesthemselves.

Study type 154

Case-crossover

Only certain types of study question can be studiedwith a case-crossover design. The exposure must besomething that varies from time to time within a person.

Case-crossover study is convenient to evaluate exposures that trigger a short-term effect. And the disease must have an abrupt onset.

How short is brief? The duration of the exposure effect should be shorter than the typical interval between episodes of exposure so that the effect of exposureis gone before the next episode of exposure occurs.

Study type 155

Case-crossover

First, a study hypothesis is defined in relation to aspecific exposure that causes the disease within a specified time period. Each case is considered exposed or unexposed according to the time relation specified in the hypothesis.

Study type 156

Hypothesis Testing

A. Significance Testing: Tests whether, beyond chance, a point estimate is different from expected or is different from another point estimate

B. Confidence Interval (CI): The limits of precision of a point estimate within which the true population value lines (with a specified probability)

Study type 157

C. A 95%CI can be interpreted as the range in which the population value would lie 95 times out of 100 study samples. For a proportion the confidence interval is: p z pq/n

Therefore, CI depends on the standard error (variance of point estimate, sample size) and a probability value.

Study type 158

Measures of Association in Case-Control study

Odds Ratio = odds of cases/odds of controls = ad/bcodds of case exposure status = exposed/unexposed = a/codds of controls exposure status = exposure/unexposed = b/d

Case ControlExposed a b

Unexposed c d

Study type 159

Equivalent Hypotheses in Case-Control Study

A. Is disease (case vs. control) status associated with exposure status?

B. Does the odds of exposure differ between cases and controls?

C. Does the odds ratio differ significantly from one?

D. Does the confidence interval for the odds ratio include 1.0?

Study type 160

Unmatched Case-Control StudyI. Point estimate

OR=ad/bc

II. Significance tests of Ho: OR =1

X2=[(ad-bc)2 T]/[n1n2m1m2]

If cell number less than 5, use Fisher’s exact test.

Study type 161

III. Confidence interval for OR

A. Woolf’s method CI= exp (ln (OR) z SE[ln(OR)])

where SE[ln(OR)]) = (1/a)+(1/b)+(1/c)+(1/d)

ln is the natural logarithm

B. Test-based method

(1 z X2 ) CI= OR

where X2 is the chi-square value for the 2x2 table

Study type 162

Example: Colon cancer No colon cancer TotalObese 30 10 40Thin 120 140 260Total 150 150 300

OR = 3.5

X2 = 11.5, p < 0.001

Woolf’s 95% CI = [1.64, 7.45]

Test-based 95% CI = [1.69, 7.22]

Study type 163

Odds Ratio =

Relative prevalence of exposure (odds) among cases

Relative prevalence of exposure (odds) among controls

a b

c d

case Control

exp

unexp

a/c

b/d

(supplement)Study type 164

In density sampling, when:

1.the sample of cases gives an unbiased estimation of the exposure distribution among cases2.The sample of controls gives an unbiased estimation of the exposure distribution in the population at risk over the study period

Relative prevalence of exposure (odds) among controls

Relative prevalence of exposure among person-timein population at risk

Study type 165

=

Number of exposed cases

Person-time among exposed

person-time among unexposed

Number of unexposed cases

Relative prevalence of exposure among cases

Relative prevalence of exposure among person-time


=





(continue)

=





Study type 167

Odds Ratio =

a b

c d

case Person-time

exp

unexp

a/c

b/d

=a/b

c/d= Rate Ratio


OR=b/c

1:1 Matched Case-Control Study

a b

c dCase

exp

unexp

Control

exp unexp

Study type 169

Cross-Sectional Studies(Surveys, Prevalence Studies)

I. Features:

A. Selection often by probability sampling

B. Subjects observed, questioned, examined to determine disease status, their current or past study factor level, and relevant variables.

Study type 170

Cross-Sectional Studies(Surveys, Prevalence Studies)II. Uses:A. Descriptive 1. Measure prevalence of common diseases 2. Assess need for health services and facilities in a target population 3. Assess impact of a planned intervention on the health status of a target population

B. Analytic 1. Generate new etiologic hypotheses 2. Analyze the determinants of frequent diseases of long duration, which often goes undiagnosed or unreported

Study type 171

Cross-Sectional Studies

The cross-sectional study can be conceptualized as away to analyze cohort data, albeit an often flawed one,in that it consists of taking a “snapshot” of a cohort byrecording information on disease outcomes and exposures at a single point in time.

Study type 172

Study type 173

Cross-Sectional Studies

Accordingly, the case-based case-control studycan also be regarded as a cross-sectional study,as it includes cross-sectionally ascertained prevalent cases and noncases .

Study type 174

Study type 175

Cross-sectional sample of a dynamic population differs from sampling in fixed cohort setting. Persons enter as well as leave the population. Disease sampling is still of prevalent cases.

D

D

D

D

D

D

D

D = disease = case

Cross-sectional Study in a Dynamic Population

DD

D

D

Persons entering the population

Persons leaving the population

Subjects in cross-section

al stu

dy

Study type 176

Data Analysis for Cross-Sectional Studies

The analysis follows that when cross-sectional dataare obtained for a defined reference population orcohort, the analytic approach may consist of eithercomparing point prevalence rates for the outcomeof interest between exposed and unexposed individualsor using a “case-control” strategy, in which prevalentcases and noncases are compared with regard to odds of exposure.

Study type 177

Cross-Sectional Studies can also be done periodically for the purpose of monitoring diseaseOr risk factor prevalence rates, as in the caseOf the US National Health Survey.

Study type 178

Major Drawbacks of the Cross-Sectional Studies for Etiologic Research

I. Temporality:

Separating cause from effect is impossible

Temporal bias typically occurs in cross-sectional surveywhen information is lacking on the time sequence withregard to the presume risk factor and the outcome.In another words, it is difficult to know which came first,the exposure or the disease.

Study type 179

I. Temporal Bias

To prevent temporal bias it is occasionally possibleto improve the information on temporality whenobtaining data through questionnaires. By questionssuch as “When were you first exposed to … ?“

Obviously, even if temporality can be establishedin a cross-sectional study, the investigator will still have the incidence-prevalence bias to contend with.

Study type 180

Job A 80 well 80 well100 workers 10 ill workers 20 ill 10 ill Job B 95 well 95 well100 workers 5 ill 15 ill point x point yPrevalence in job A: 20% (20/100) 11% (10/90)

Prevalence in job B: 5% (5/100) 14% (15/110)

Ratio of prevalence (A/B): 4.0 0.8

Study type 181

Bias of Cross-Sectional Studies

II. Incidence-Prevalence Bias

A study of prevalent cases will have a higher proportion of cases with disease of long duration compared to incident cases

Data obtained reflects determinants of survival as well as etiology.

Study type 182

Choosing a Study Design

• What has already been done?– If no research, a rapid and inexpensive eco

logical study may be useful– If several case-control studies have alread

y been done, what would yours contribute?– Is it worth repeating a cohort study that has

been done in a one population in a different population (eg, in women rather than in men)?

Study type 188

(continue)

Cohort study decision:– Need to represent a larger population?

• Not necessarily relevant to biological question of relative disease risk in exposed and unexposed

• May be important to generalizing findings

Study type 189

(continue)

Larger cohort versus longer follow-up:

Shorter follow-up limits potential usefulness of cohort to examine other research questions.

Shorter follow-up desirable if rapid answer to research question is a high priority

Study type 190

Choosing a Study Design: Case-cohort versus nested case-control

• Nested case-control somewhat more statistically efficient in cohorts with long follow-up and substantial censoring

• Analysis is more familiar and available for nested case-control

• Power of nested case-control requires only estimate of number of cases and controls; case-cohort requires information on whole cohort and drop out rate

Study type 191

(continue)

• Case-cohort can use same controls for multiple disease outcomes

• Case-cohort allows direct modeling of disease incidence in exposed and unexposed

• Case-cohort allows multiple time scales (age, calendar time); nested case-control only one

• Nested case-control allows more efficient collection of time dependent exposures

Study type 192

(continue)

• Case-cohort can use same controls for a future period of additional cohort follow-up

• Case-cohort can use controls for other purposes (such as monitoring compliance)

• Controls can be selected more rapidly in case-cohort; nested case-control may require control selection at end of study for late cases

Study type 193

observational epidemiologic studies descriptive (incidence, prevalence) analytic (associate...

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