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Confounding

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Confounding

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Principles of Epidemiology for Public Health (EPID600)

Victor J. Schoenbach, PhD�www.unc.edu/~vschoenb/

Department of Epidemiology�Gillings School of Global Public Health�University of North Carolina at Chapel Hill

www.unc.edu/epid600/

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“Brain Cramps” "interesting" comments by well-known people

(Received from Natasha Jamison, �EPID160 graduate)

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That’s what can be further from �the truth!

“I was provided with additional input that was radically different from the truth. I assisted in furthering that version.”

– Colonel Oliver North, from his �Iran-Contra testimony.

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Equal opportunity employer

“We don't necessarily discriminate. We simply exclude certain types of people.”

– Colonel Gerald Wellman, ROTC Instructor.

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Quite a high risk, I’d say

“If we don't succeed, we run the risk of failure.”

– President Bill Clinton

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Why I’m glad no one is taping me

“We are ready for an unforeseen event that may or may not occur.”

– Vice President Al Gore

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We are here

[Now leaving] Sources of error

Confounding

[Now entering] Data analysis and interpretation

Causal inference

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Setting the scene

“The data speak for themselves.”

versus

“Our data say nothing at all.”

(Epidemiology guru Sander Greenland, Congress of Epidemiology 2001, Toronto)

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Setting the scene

Logically sound inferences involve�(1) data + (2) assumptions
No assumptions no inference
So always need a conceptual model

Sander Greenland, Congress of Epidemiology 2001, Toronto

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Causal inference in everyday living

Does exercise make me feel better?

Try getting exercise – how do I feel?
Try not getting exercise – how do I feel?
Try getting exercise again – do I feel better?

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A key purpose of collecting, analyzing, and interpreting epidemiologic data is to make inferences about causal relations. We want to know what causes diseases, how behaviors, environmental exposures, public policies affect health, whether clinical and public health interventions improve health status, etc. It may be instructive to take a look at causal inference in everyday living.

As you know, the Centers for Disease Control and Prevention (CDC) tells us that sedentary living (lack of physical activity) is as bad for health as cigarette smoking. But longterm consequences are often not as effective motivators as is how something makes us feel in the present. So when my mentor tells me that I’ll feel better if I get more exercise, how do I assess whether that is true? I try an “experiment.” I try getting some exercise and see how I feel. Then I try not getting exercise and seeing how I feel. Then I may try getting exercise again and see if I feel better.

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Causal inference in everyday living

Does getting too little sleep make me irritable?

Try sleeping too little – ask my partner
Try sleeping enough – ask my partner
Try sleeping too little – ask my partner

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Desirable attributes of crossover experiments

Exposure is under investigator’s control
Comparison condition is a true control
Can go back and forth, providing some control for secular changes

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These trials are called “cross-over experiments” because we observe the same experimental subjects in each of the conditions being compared. By being able to change exposure status and compare the outcomes, we have controlled for many of the possible influences on the comparison being made – enduring characteristics of people, such as genetics and history. So this type of experiment is a powerful tool for causal inference and is a mainstay of both everyday causal inference and laboratory experiments.

Some of the desirable attributes of crossover experiments for causal inference are that because the exposure is under the investigator’s control, we do not have to worry about what factors in the environment or in the research subject might be influencing the presence of the exposure. Also, except for the time factor, the comparison condition is a true control – the same person exposed to the exposure or its absence. Even the time factor can be controlled to a large degree if we can apply and remove the exposure repeatedly.

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Constraints on cross-over experiments

Exposures may be harmful or not under our control
Effects may not be quickly reversible
Experimental subjects or the environment may have changed

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Key attribute of crossover experiments

Can compare what happens to people who are exposed to what happens to the same people when they are not exposed – almost at the same time

Confounding

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People

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People with an exposure

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Same people without the exposure

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With the exposure

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O

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Without the exposure

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O

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Modern formulation of causal inference

This comparison provides the best evidence that the exposure causes the outcome.

The modern formulation of causal inference and confounding is based on this “counterfactual model”.

Confounding

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Problem of causal inference

Problem: cannot observe both conditions

Solution: observe a “substitute population”, a population whose experience will represent that of the exposed population without the exposure

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“Counterfactual” model

Conceptual model for causal inference:

Compare experience of a population exposed to a factor with experience of the same population at the same time but without the exposure
Since cannot do that, compare to experience of a substitute population.

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Confounding

The substitute population is not equivalent to the counterfactual condition.

I.e., the substitute population does not show the “outcome in the exposed population without the exposure”.

Confounding

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Problem of comparison

Confounding is a problem of comparison – we compare the exposed population to a substitute population, but the substitute population does not show the “outcome in the exposed population without the exposure”

Confounding

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Why worry about confounding?

Does air pollution cause bronchitis ?

Confounding

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Why do we need to worry about confounding? We worry because many of the the data that we collect to answer public health questions are susceptible to misinterpretation due to confounding.

For example, take the question “does air pollution causes bronchitis?” The counterfactual model says that to answer this question we need to compare bronchitis rates in people who are exposed to air pollution with bronchitis rates for the same people at the same time but when they have not been exposed to air pollution. Since we cannot do that, we compare people exposed to air pollution with a substitute population – people who are “just like them” except that they are not exposed to air pollution. But can we find such a population? People don’t usually like to live in polluted areas. So people who have choices live elsewhere. Powerful people can avoid pollution. So the people exposed to air pollution may be people with neither choices nor power. Might these disadvantaged people have a different risk of bronchitis than do powerful people with choices, for reasons other than air pollution?

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Why worry about confounding?

Does air pollution cause bronchitis ?

Confounding

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Breathe polluted air

Develop bronchitis

Have choices and power

?

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Why worry about confounding?

Does air pollution cause bronchitis ?
Do seatbelts reduce crash injuries?

Confounding

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?

Wear seatbelts

Risk averse

↓Injured in a crash

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Why worry about confounding?

Does air pollution cause bronchitis ?
Do seatbelts reduce crash injuries?
Do STD’s increase HIV transmission?

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STD

Risky sex

HIV

?

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Why worry about confounding?

Does air pollution cause bronchitis ?
Do seatbelts reduce crash injuries?
Do STD’s increase HIV transmission?
Does smoking lead to illicit drug use?

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Three questions

What comparison should we make according to the counterfactual model?
What comparison will we make instead (i.e., what substitute population will we use for the comparison)?
How likely is this substitute population to show us what will happen in the exposed population without its exposure

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F

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Learning objectives

Understand (basic) confounding
Recognize potential confounding and actual confounding
Know how to control confounding
Follow discussions about confounding

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Learning objectives - 2

Define and explain:

– confounding

– potential confounder

– actual confounder

– control of confounding

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Conventional perspective

Confounding: “mixing of effects”

> Some other risk factor may be responsible for at least some of the association under investigation.

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Common confounders

Age -- e.g., exposed persons are older
Sex -- e.g., more exposure in men
Risk factors - more exposed persons (or unexposed) smoke(-), exercise(+), eat vegetables(+), use drugs(-), . . .

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Some of the most common confounders are age, sex, and other familiar risk factors. Age is related to most diseases. Even if “age” is not a cause of those diseases, it is often a marker of risk for developing them, presumably due to accumulation of various insults. When we compare disease incidence or mortality in an “exposed” group to that in an “unexposed” group, we would almost always be concerned if the two groups had different age distributions. That is why age standardization is a routine practice for comparing mortality rates and rates of other age-related outcomes.

Sex is another common confounder, though in this case we often avoid the problem by analyzing females and males as two separate populations. We stratify our analyses by sex and in this way ensure that the “exposed” and “unexposed” groups have the same sex distribution (i.e., both are all female or both are all male).

Exposures of interest are often associated with known risk factors, such as smoking, exercise, eating vegetables, use of illicit drugs, etc., so if the outcome is believed to be related to one or more of these factors then we need to find some way to differentiate effects of these “extraneous” factors from the one of primary interest.

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Example of confounding in a cohort

Confounding

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Baseline

_____________________

Diseased

Not diseased

follow-up

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Cohort study – known risk factor

Confounding

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Risk factor

absent

_____________________

Risk factor present

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Cohort study – known risk factor

Confounding

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Risk factor

absent

_____________________

Risk factor present

Diseased

Not diseased

- - - - - - - - - - - - follow-up - - - - - - - - - - - -

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Cohort study for a new exposure

follow-up

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

(Angry)

(Not angry)

The reason we are conducting the cohort study, however, is to study the exposure (frequent anger) that is suspected of increasing risk for the disease (memory impairment). We will compare disease incidence in people who are frequently angry to disease incidence in people who are not. So this slide shows the cohort divided into a subcohort of angry people [the exposed] and a subcohort of people who are not frequently angry [the unexposed]. Together they make up the original cohort.

Note that I have drawn the boxes in a size that suggests that the incidence of the disease is greater in the exposed cohort. You can see this by noting that although the box for the Exposed population is much smaller than that for the Unexposed population, the box for Diseased people on the left is larger than the box for Diseased people on the right. We don’t see the distribution of inadequate sleep, but we know that it is contributing to the rates of memory impairment (the disease).

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Confounding in a cohort

Exposed

Confounding

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Exposed

Unexposed

Unexposed population is the “substitute population” to tell us what would happen in the exposed population without its exposure - but suppose that the exposed population have another risk factor:

(Angry)

(Not angry)

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Confounding in a cohort

Exposed

Confounding

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Exposed

Unexposed

Substitute population will not show us what would happen in the exposed population without its exposure

(Angry)

(Not angry)

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Confounding in a cohort

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

(Angry)

(Not angry)

This diagram shows the comparison of disease incidence in the exposed population (on the left) with that in the unexposed population (on the right). The figure also shows how inadequate sleep (in blue font) is more prevalent in the exposed members at baseline and at the end of follow-up (we are assuming that people’s characteristics and behaviors do not change). Again, the size of the boxes and the amount of blue font show the incidence of memory impairment associated with inadequate sleep and also with frequent anger. So on the left side – the exposed group, the angry ones – over half of the people do not get enough sleep. These sleepy people have a higher rate of memory impairment than do other angry people who do get enough sleep, so after follow-up we find the case group to have a higher prevalence of inadequate sleepers than does the noncase group (among the angry people, on the left). On the right side – the unexposed group – people who do not get enough sleep also end up disproportionately in the case group.

Because inadequate sleep increases risk of memory impairment and because inadequate sleep is more prevalent in the exposed group, the exposed group would have a higher incidence of the disease even if anger itself had no effect. The disease incidence in the exposed group represents a mixing of the effects of inadequate sleep and frequent anger. We can see this more clearly in the following slides.

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Cohort members without the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

(Not angry)

(Angry)

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Cohort members with the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

(Not angry)

(Angry)

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Cohort members without the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

8,300

100

2,400

166

8,134

(Not angry)

(Angry)

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Cohort members without the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

8,300

100 (0.04=4%)

2,400

166�(0.02=2%)

(Not angry)

(Angry)

8,134

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Cohort members without the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

8,300

100 (0.04)

2,400

166 (0.02)

RR = 0.04 / 0.02 = 2.0

(Not angry)

(Angry)

8,134

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Cohort members with the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

1,700

200

2,300

68

2,500

1,632

(Not angry)

(Angry)

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Cohort members with the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

1,700

200�(0.08=8%)

2,300

68�(0.04=4%)

2,500

1,632

(Not angry)

(Angry)

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Cohort members with the potential confounder

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

1,700

200 (0.08)

2,300

68 (0.04)

2,500

RR = 0.08 / 0.04 = 2.0

(Not angry)

(Angry)

1,632

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The entire cohort

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

1,700

8,300

100+200

2,400+2,300

166+68

2,500

8,134+1,632

(Not angry)

(Angry)

Now let’s put the two subcohorts – the people who are get enough sleep and the people who do not – back together into a single cohort. Let’s take a moment to see where the numbers on this slide come from. In each pair of numbers, for example, 100 + 200 in the lower left of the slide, the first number is for people who get enough sleep, and the second number is for people who do not. So if you look back 4 slides you will find the 100 in the lower left and if you move forward a slide from there you will find the 200.

So in the full cohort there are 100 + 200, or 300 cases among the exposed (the angry ones) and 166 + 68, or 234 cases among the unexposed. The incidence proportion of memory impairment among those with frequent anger is (100 + 200) / (2,500 + 2,500) = 300 / 5,000 = 0.06, or 6%; on the unexposed side, the incidence is (166 + 68) / (8,300 + 1,700) = 234 / 10,000 = 0.023, or 2.3%.

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The entire cohort

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

1,700

8,300

100+200�(0.06)

166+68�(0.023)

2,500

(Not angry)

(Angry)

2,400+2,300

8,134+1,632

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The entire cohort - RR for exposure

Exposed

follow-up

Confounding

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Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

1,700

8,300

2,500

RR = 0.06 / 0.023 = 2.6

(Not angry)

(Angry)

2,400+2,300

8,134+1,632

100+200�(0.06)

166+68�(0.023)

So the incidence proportion ratio for memory impairment in relation to frequent anger is 2.6 in the overall cohort. This ratio is greater than the 2.0 we saw in each of the two subcohorts. The higher RR for the full cohort arises from the “mixing” of the effect of the exposure, frequent anger, with the effect of the potential confounder, inadequate sleep. Thus, the potential confounder is an actual confounder.

Thinking back to the conceptual model from the beginning of the lecture, we can ask how well the substitute population represents the counterfactual comparison, the exposed population without its exposure. The answer is “not terribly well”.

The substitute population is the people who are not frequently angry. We are using their incidence of memory impairment as an indicator of what incidence to expect among the people who are frequently angry if anger had no effect. But because the potential confounder, a risk factor for memory impairment, is less frequent in the unexposed group (the substitute population) than in the exposed group, this substitute population is not a good guide to what we would see in the exposed group without its exposure.

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Comparing heterogeneous exposure groups

Exposed

follow-up

Confounding

53

Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

1,700

8,300

2,500

RR = 0.06 / 0.023 = 2.6

(Not angry)

(Angry)

2,400+2,300

8,134+1,632

100+200�(0.06)

166+68�(0.023)

0.08

0.04

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Comparing heterogeneous exposure groups

Exposed

follow-up

Confounding

54

Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

1,700

8,300

2,500

RR = 0.06 / 0.023 = 2.6

(Not angry)

(Angry)

2,400+2,300

8,134+1,632

100+200�(0.06)

166+68�(0.023)

0.04

0.02

Meanwhile, on the right side of the slide, the people who are not angry and get enough sleep have an incidence proportion of 0.02 (which comes from 166/8,300). The people who are not angry but don’t get enough sleep have an incidence of 0.04 (68/1,700). The overall incidence in those who are not angry, 0.023, is a weighted average of 0.02 and 0.04, but the two incidences are not weighted equally. Fully 83% – which comes from 8,300/(8,300+1,700) – fully 83% of the unexposed group get enough sleep, leaving 17% [1,700/(8,300+1,700)] who do not get enough sleep. So the weighted average is formed by giving the 0.02 a weight of 83% and the 0.04 a weight of 17%:

So the weighted average = 83% x 0.02 + 17% x 0.04 = 0.023

Because its weight is so much greater, the 0.02 “pulls” the average closer to it than does the 0.04.

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Overall proportions are weighted averages

Confounding

55

2,500

Exposed group (Angry people)

4% 5% 6% 7% 8%

2,500

Get enough sleep

Sleep-deprived

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Overall proportions are weighted averages

Confounding

56

8,300

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

1,700

Get enough sleep

Sleep-deprived

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Confounded comparison of weighted averages

Confounding

57

8,300

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

1,700

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

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Comparing within a stratum is valid

Confounding

58

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

1,700

8,300

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Comparing within a stratum is valid

Confounding

59

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

1,700

8,300

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Overall comparisons reflect subgroup sizes

Confounding

60

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

1,700

8,300

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Overall comparisons should use the same weights

Confounding

61

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

2,500

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Unconfounded RRs

Confounding

62

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

2,500

RR=2.0

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Confounded RR

Confounding

63

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

RR=2.6

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RR for confounding

Confounding

64

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

4% 5% 6% 7% 8%

Exposed group (Angry people)

RR=2.6

RR=2.0

RR_{for confounding} = RRcrude / RRunconfounded

1.3 = 2.6 / 2.0

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RR for confounding

Confounding

65

Unexposed group (not angry)

2% 2.3% 2.5% 3% 3.5% 4%

Get enough sleep

Sleep-deprived

2,500

2% 2.5% 3% 3.5% 4%

Exposed group (Angry people)

RR=1.3

RR=1.0

RR_{for confounding} = RRcrude / RRunconfounded

1.3 = 1.3 / 1.0

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Confounding in a case-control study

Exposed

follow-up

Confounding

66

Exposed

Diseased

Not

Diseased

Unexposed

Diseased

Not

Diseased

2,500

8,300

100+200

166+68

2,500

(Not angry)

(Angry)

2,400+2,300

8,134+1,632

1,700

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Exposure odds in case group

Exposed

follow-up

Confounding

67

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100+200

166+68

2,500

(Not angry)

(Angry)

1,700

Odds in cases = 300 / 234 = 1.28

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Exposure odds in controls

Exposed

follow-up

Confounding

68

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100+200

166+68

2,500

(Not angry)

(Angry)

1,700

Odds in study base = 5,000 / 10,000 = 0.50

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Exposure odds ratio in case-cohort study

Exposed

follow-up

Confounding

69

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100+200

166+68

2,500

(Not angry)

(Angry)

1,700

OR = 1.28 / 0.50 = 2.6

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Exposure odds in cases without the potential confounder

Exposed

follow-up

Confounding

70

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100

166

(Not angry)

(Angry)

Odds in cases = 100 / 166 = 0.60

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Exposure odds in controls without the potential confounder

Exposed

follow-up

Confounding

71

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100

166

(Not angry)

(Angry)

Odds in study base = 2,500 / 8,300 = 0.30

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Odds ratio in people without the potential confounder

Exposed

follow-up

Confounding

72

Exposed

Diseased

Unexposed

Diseased

2,500

8,300

100

166

(Not angry)

(Angry)

Odds = 0.60 / 0.30 = 2.0

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Exposure odds in cases with the potential confounder

follow-up

Confounding

73

Exposed

Diseased

Unexposed

Diseased

1,700

200

68

2,500

(Not angry)

(Angry)

Odds = 200 / 68 = 2.94

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Exposure odds in controls with the potential confounder

Exposed

follow-up

Confounding

74

Exposed

Diseased

Unexposed

Diseased

1,700

200

68

2,500

(Not angry)

(Angry)

Odds = 2,500 / 1,700 = 1.47

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Odds ratio in persons with the potential confounder

Exposed

follow-up

Confounding

75

Exposed

Diseased

Unexposed

Diseased

1,700

200

68

2,500

(Not angry)

(Angry)

OR = 2.94 / 1.47 = 2.0

And the odds ratio would be 2, the unconfounded value.

Our case-control study has provided a faithful “window” into the cohort. When we controlled for the potential confounder by examining people without and with that risk factor separately, we observed the effect of the exposure. When we ignored the potential confounder, then the odds ratio we saw reflected the combination of the effect of the exposure (anger) plus the greater prevalence of the potential confounder (sleep deprivation) in exposed persons.

Many introductory textbooks present tests for confounding in terms of whether the potential confounder is associated with the exposure and the disease. But this test can be confusing when one tries to apply it in the case-control setting. The mechanism that underlies confounding is an association between the risk factor and the exposure of interest in the underlying cohort. The case-control design provides a window into that cohort, rather than access to the entire cohort. In a case-control study we appear to be comparing the cases to the controls, so it might seem that the prevalence of the risk factor should be the same in cases and controls. But that perspective arises from the traditional (and in this case misleading) understanding of the case-control study design.

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Potential confounder

Confounding

76

Determinant or risk factor for the outcome (or its detection).

Must have potential to provide an alternative explanation for observed association.

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Actual confounder

Confounding

77

The potential confounder becomes an actual confounder when one exposure group has more of it than the other, so it’s not fair to compare them

So a potential confounder is a disease determinant or risk factor. When does it become an actual confounder?

A potential confounder becomes an actual confounder – in other words, it can lead us to misinterpret our findings – when one exposure group has proportionately more of the potential confounder than does the other exposure group, so that the comparison is actually distorted.

If two groups have different proportions of a potential confounder, then it’s not “fair” to compare them, just as it’s not fair to compare a basketball team with mostly tall players to a team with mostly short players. When the exposed and unexposed have different proportions of a disease determinant, the unexposed group is not an appropriate substitute population for the counterfactual comparison with the exposed group.

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Causal models

A

X B

(X confounding)

A X B

(X intervening)

Confounding

78

In the beginning of this lecture, I quoted Sander Greenland’s declaration that the data say nothing. Causal inference requires data and assumptions. Without assumptions there is no inference. So far in this lecture we have been considering data (i.e., associations) but not assumptions. Now we need the assumptions.

The interpretation of a situation as one of confounding depends upon our conceptual model for the phenomenon under study. The slide shows two different causal models involving factor A, disease B, and factor X. In the upper diagram, X causes A, and X causes B. A and B are associated, but their association is due to the effect of X on both of them. If we are studying factor A to see if it is an (independent) risk factor for disease B, then we had better control for factor X as a potential confounder, since X is a cause of disease B and is likely to be more prevalent among people with factor A.

However, if our causal model is represented by the lower diagram, then we would not regard X as a potential confounder of the association between A and B. In the lower model, X is an intervening or mediating variable. So it does not make sense to control for X and declare that “the association between A and B is due to confounding by X.” X is not an alternative explanation for the association between A and B. X is simply the mechanism. So decisions about confounding depend crucially on the causal model that we bring to the data analysis and interpretation.

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What is a confounder - 2?

A confounder is:

1. “associated with the exposure and the disease” – it causes “guilt by association”.

2. capable of being an “alternate explanation”, i.e., the “real culprit”.

Confounding

79

One way to get an intuitive feel for confounding – and a way to avoid losing sight of the forest (the meaning) for the trees (the data) – is to think of confounding as a process of “guilt by association”. Suppose we find an association between an exposure and a disease. If the association is due entirely to some other factor, a confounder, then the exposure has been incriminated solely due to its association with the confounder.

In order to find the exposure “innocent”, though, the confounder must be capable of serving as an alternate explanation for the association between exposure and disease. The confounder must be the “real culprit”.

Suppose that Mike’s neighbor has a bookstore. One day Mike and Sam go into the bookstore, and while Mike is talking to the storeowner Sam takes a book without paying for it. When the storeowner realizes that the book has been taken, he calls the police and tells them that Mike was involved.

Is Mike (who is representing the exposure) guilty (in other words, is he a risk factor for the theft)? If Mike had no idea that Sam was going to steal the book – then Mike was not guilty of shoplifting. Sam is the real culprit, and the appearance that Mike is guilty is due to confounding: guilt by association. If instead, Mike agreed to distract the storeowner while Sam stole the book, then Mike is indeed guilty. The observed association is the same, but our interpretation depends on our causal model.

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Control of confounding

Controlling confounding means doing something to make comparison fair:

Exclude people who have the risk factor (“restriction”)
Stratified analysis (adjustment, standardization)
Mathematical modeling (e.g., regression)

Confounding

80

Controlling confounding means doing something to make the comparison of exposed and unexposed a fair one. Apart from complex situations such as overweight and coronary heart disease risk, there are three basic approaches to controlling confounding in observational studies:

1. Exclude people who have the risk factor that we believe may confound; that’s often neither practical nor desirable, but it is effective in controlling confounding;

2. Carry out a stratified analysis, where we examine the association between exposure and outcome separately according to the values of the other risk factors (for example, people who are frequently angry and people who are not frequently angry can be analyzed separately among those who get enough sleep and among those who do not get enough sleep; that’s what we showed in the example that we went through earlier). We may then compute an adjusted or standardized estimate of the association between the exposure and outcome, if we wish to.

3. We can express the relation between all risk factors and disease in a mathematical model, and using that model we can estimate the association between exposure and disease, controlling for the other risk factors.

It is also possible – in a cohort study – to avoid confounding by matching the unexposed group to the exposed group; this is done occasionally.

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Control of confounding –�hard to control unknown risk factors

These methods can control only known potential confounders.
Only random assignment of exposure can control for unknown potential confounders.

Confounding

81

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Limitations in ability to control

Effective control of confounding requires:

Knowing the causal pathways
Knowing all relevant causal factors
Measuring all relevant causal factors – accurately

Confounding

82

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Limitations in ability to control

Effective control of confounding requires assumptions, such as the mathematical form of relationships between covariables and outcome

Large, randomized experiments uniquely powerful for causal inference but . . .

Confounding

83

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Confounded confounding!

Does overweight increase CHD risk independently of cholesterol, hypertension, and diabetes?

Confounding

84

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Confounding – key concepts

1. Interpreting data requires assumptions about causal relations (including what factors are potential confounders, i.e., what factors affect incidence and are not themselves caused by the exposure).

Confounding

85

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Confounding – key concepts

2. If exposed people and unexposed people differ on factors that affect disease incidence, then those factors may confound (distort) the observed relation between exposure and disease (i.e., actual confounding).

Confounding

86

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Confounding – key concepts

3. We can control confounding by study design if we can make the exposed and unexposed groups similar in respect to all disease determinants, though matching or randomized assignment of exposure.

Confounding

87

Third, because confounding requires that a potential confounder must be unequally distributed between the exposed and unexposed groups, we can control confounding in the design of the study if we can make the exposed and unexposed groups similar in respect to all disease determinants. We can sometimes do this by matching unexposed to exposed people on these disease determinants (for example, we choose unexposed people of the same ages as exposed people). Moreover, if we can randomly assign exposure then we can at least on the average ensure that the exposed and unexposed groups are similar at baseline on all potential confounders, even those we do not know of or cannot measure. We can also employ a combination of matching and randomized assignment.

Note, however, that the above comment about matching applies to a cohort study. Matching in a case-control study does not generally prevent confounding. (If you are interested in that topic, I can provide an explanation and example; it is also illustrated in the Evolving Text)

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Confounding – key concepts

4. We can control confounding in the analysis if we can stratify the data by disease determinants that are not themselves caused by the exposure (i.e., not causal intermediates).

Confounding

88

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Confounding – key concepts

5. The best way to understand a case-control study is to analyze it as a window into a cohort and to be aware that many books and teachings still follow the traditional and somewhat misleading perspective.

Confounding

89

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Keep hope alive!

Confounding can be confounding – do not be discouraged if you do not understand it yet.

Confounding

90

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Dietary advice

The Japanese eat very little fat and suffer fewer heart attacks than the British or Americans.

On the other hand, the French eat a lot of fat and also suffer fewer heart attacks than the British or Americans.

Confounding

91

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Dietary advice

The Japanese drink very little red wine and suffer fewer heart attacks than the British or Americans.

On the other hand, Italians drink excessive amounts of red wine and also suffer fewer heart attacks than the British or Americans.

Confounding

92

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Dietary advice - conclusion

Conclusion: Eat & drink what you like. It appears that speaking English is what kills you.

(submitted by Natasha Jamison, EPID160 student)

Confounding

93

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Hmmm.

"Your food stamps will be stopped effective March 1992 because we received notice that you passed away. May God bless you. You may reapply if there is a change in your circumstances.”

– Department of Social Services, Greenville, South Carolina