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12 confounding
- 1. 4/5/2011 Confounding 1 Confounding 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/
- 2. “Brain Cramps” "interesting" comments by well-known people (Received from Natasha Jamison, EPID160 graduate)
- 3. 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.
- 4. Equal opportunity employer “We don't necessarily discriminate. We simply exclude certain types of people.” – Colonel Gerald Wellman, ROTC Instructor.
- 5. Quite a high risk, I’d say “If we don't succeed, we run the risk of failure.” – President Bill Clinton
- 6. 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
- 7. Confounding 7 We are here • [Now leaving] Sources of error Confounding • [Now entering] Data analysis and interpretation Causal inference
- 8. Confounding 8 Setting the scene “The data speak for themselves.” versus “Our data say nothing at all.” (Epidemiology guru Sander Greenland, Congress of Epidemiology 2001, Toronto)
- 9. Confounding 9 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
- 10. Confounding 10 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?
- 11. Confounding 11 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
- 12. Confounding 12 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
- 13. Confounding 13 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
- 14. Confounding 14 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
- 16. Confounding 16 People with an exposure
- 17. Confounding 17 Same people without the exposure
- 18. Confounding 18 With the exposure O O O O
- 19. Confounding 19 Without the exposure O O
- 20. Confounding 20 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”.
- 21. Confounding 21 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
- 22. Confounding 22 “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.
- 23. Confounding 23 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”.
- 24. Confounding 24 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”
- 25. Confounding 25 Why worry about confounding? • Does air pollution cause bronchitis ?
- 26. Confounding 26 Why worry about confounding? • Does air pollution cause bronchitis ? Breathe polluted air Develop bronchitis Have choices and power ?
- 27. Confounding 27 Why worry about confounding? • Does air pollution cause bronchitis ? • Do seatbelts reduce crash injuries? ? Wear seatbelts Risk averse ↓Injured in a crash
- 28. Confounding 28 Why worry about confounding? • Does air pollution cause bronchitis ? • Do seatbelts reduce crash injuries? • Do STD’s increase HIV transmission? STD Risky sex HIV ?
- 29. Confounding 29 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?
- 30. Confounding 30 Three questions 1. What comparison should we make according to the counterfactual model? 2. What comparison will we make instead (i.e., what substitute population will we use for the comparison)? 3. How likely is this substitute population to show us what will happen in the exposed population without its exposure F
- 31. Confounding 31 Learning objectives 1. Understand (basic) confounding 2. Recognize potential confounding and actual confounding 3. Know how to control confounding 4. Follow discussions about confounding
- 32. Confounding 32 Learning objectives - 2 5. Define and explain: – confounding – potential confounder – actual confounder – control of confounding
- 33. Confounding 33 Conventional perspective Confounding: “mixing of effects” > Some other risk factor may be responsible for at least some of the association under investigation.
- 34. Confounding 34 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(-), . . .
- 35. Confounding 35 Example of confounding in a cohort Baseline_____________________ Diseased Not diseased follow-up
- 36. Confounding 36 Cohort study – known risk factor Risk factor absent_____________________ Risk factor present
- 37. Confounding 37 Cohort study – known risk factor Risk factor absent_____________________ Risk factor present Diseased Not diseased - - - - - - - - - - - - follow-up - - - - - - - - - - - -
- 38. Confounding 38 Cohort study for a new exposure follow-up Exposed follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased (Angry) (Not angry)
- 39. Confounding 39 Confounding in a cohort ExposedExposed 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)
- 40. Confounding 40 Confounding in a cohort ExposedExposed Unexposed Substitute population will not show us what would happen in the exposed population without its exposure (Angry) (Not angry)
- 41. Confounding 41 Confounding in a cohort Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased (Angry) (Not angry)
- 42. Confounding 42 Cohort members without the potential confounder Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased (Not angry) (Angry)
- 43. Confounding 43 Cohort members with the potential confounder Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased (Not angry)(Angry)
- 44. Confounding 44 Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 8,300 100 2,400 166 8,134 Cohort members without the potential confounder (Not angry) (Angry)
- 45. Confounding 45 Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 8,300 100 (0.04=4%) 2,400 166 (0.02=2%) Cohort members without the potential confounder (Not angry) (Angry) 8,134
- 46. Confounding 46 Exposed follow-up follow-up 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 Cohort members without the potential confounder (Not angry) (Angry) 8,134
- 47. Confounding 47 Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 1,700 200 2,300 68 2,500 1,632 Cohort members with the potential confounder (Not angry)(Angry)
- 48. Confounding 48 Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 1,700 200 (0.08=8%) 2,300 68 (0.04=4%) 2,500 1,632 Cohort members with the potential confounder (Not angry)(Angry)
- 49. Confounding 49 Exposed follow-up follow-up 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 Cohort members with the potential confounder (Not angry)(Angry) 1,632
- 50. Confounding 50 The entire cohort Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 1,7008,300 100+200 2,400+2,300 166+68 2,500 8,134+1,632 (Not angry) (Angry)
- 51. Confounding 51 The entire cohort Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 1,7008,300 100+200 (0.06) 166+68 (0.023) 2,500 (Not angry) (Angry) 2,400+2,300 8,134+1,632
- 52. Confounding 52 The entire cohort - RR for exposure Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 1,7008,300 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)
- 53. Confounding 53 Comparing heterogeneous exposure groups Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 1,7008,300 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) 0.080.04
- 54. Confounding 54 Comparing heterogeneous exposure groups Exposed follow-up follow-up Exposed Diseased Not Diseased Unexposed Diseased Not Diseased 2,500 1,7008,300 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) 0.040.02
- 55. Confounding 55 Overall proportions are weighted averages 2,500 Exposed group (Angry people) 4% 5% 6% 7% 8% 2,500 Get enough sleep Sleep-deprived
- 56. Confounding 56 Overall proportions are weighted averages 8,300 Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% 1,700 Get enough sleep Sleep-deprived
- 57. Confounding 57 Confounded comparison of weighted averages 8,300 Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% 1,700 Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people)
- 58. Confounding 58 Comparing within a stratum is valid Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) 1,700 8,300
- 59. Confounding 59 Comparing within a stratum is valid Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) 1,700 8,300
- 60. Confounding 60 Overall comparisons reflect subgroup sizes Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) 1,700 8,300
- 61. Confounding 61 Overall comparisons should use the same weights Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) 2,500 2,500
- 62. Confounding 62 Unconfounded RRs Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) 2,500 2,500 RR=2.0 RR=2.0RR=2.0
- 63. Confounding 63 Confounded RR Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) RR=2.6
- 64. Confounding 64 RR for confounding Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 4% 5% 6% 7% 8% Exposed group (Angry people) RR=2.6 RR=2.0 RRfor confounding = RRcrude / RRunconfounded 1.3 = 2.6 / 2.0
- 65. Confounding 65 RR for confounding Unexposed group (not angry) 2% 2.3% 2.5% 3% 3.5% 4% Get enough sleep Sleep-deprived 2,500 2,500 2% 2.5% 3% 3.5% 4% Exposed group (Angry people) RR=1.3 RR=1.0 RRfor confounding = RRcrude / RRunconfounded 1.3 = 1.3 / 1.0
- 66. Confounding 66 Confounding in a case-control study Exposed follow-up follow-up 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
- 67. Confounding 67 Exposure odds in case group Exposed follow-up follow-up 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
- 68. Confounding 68 Exposure odds in controls Exposed follow-up follow-up 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
- 69. Confounding 69 Exposure odds ratio in case-cohort study Exposed follow-up follow-up 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
- 70. Confounding 70 Exposed follow-up follow-up Exposed Diseased Unexposed Diseased 2,500 8,300 100 166 Exposure odds in cases without the potential confounder (Not angry) (Angry) Odds in cases = 100 / 166 = 0.60
- 71. Confounding 71 Exposed follow-up follow-up Exposed Diseased Unexposed Diseased 2,500 8,300 100 166 Exposure odds in controls without the potential confounder (Not angry) (Angry) Odds in study base = 2,500 / 8,300 = 0.30
- 72. Confounding 72 Exposed follow-up follow-up Exposed Diseased Unexposed Diseased 2,500 8,300 100 166 Odds ratio in people without the potential confounder (Not angry) (Angry) Odds = 0.60 / 0.30 = 2.0
- 73. Confounding 73 follow-up follow-up Exposed Diseased Unexposed Diseased 1,700 200 68 2,500 Exposure odds in cases with the potential confounder (Not angry) (Angry) Odds = 200 / 68 = 2.94
- 74. Confounding 74 Exposed follow-up follow-up Exposed Diseased Unexposed Diseased 1,700 200 68 2,500 Exposure odds in controls with the potential confounder (Not angry) (Angry) Odds = 2,500 / 1,700 = 1.47
- 75. Confounding 75 Exposed follow-up follow-up Exposed Diseased Unexposed Diseased 1,700 200 68 2,500 Odds ratio in persons with the potential confounder (Not angry) (Angry) OR = 2.94 / 1.47 = 2.0
- 76. Confounding 76 Potential confounder Determinant or risk factor for the outcome (or its detection). Must have potential to provide an alternative explanation for observed association.
- 77. Confounding 77 Actual confounder 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
- 78. Confounding 78 Causal models A X B (X confounding) A X B (X intervening)
- 79. Confounding 79 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”.
- 80. Confounding 80 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)
- 81. Confounding 81 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.
- 82. Confounding 82 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
- 83. Confounding 83 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 . . .
- 84. Confounding 84 Confounded confounding! • Does overweight increase CHD risk independently of cholesterol, hypertension, and diabetes?
- 85. Confounding 85 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).
- 86. Confounding 86 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).
- 87. Confounding 87 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.
- 88. Confounding 88 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).
- 89. Confounding 89 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.
- 90. Confounding 90 Keep hope alive! Confounding can be confounding – do not be discouraged if you do not understand it yet.
- 91. Confounding 91 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.
- 92. Confounding 92 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.
- 93. Confounding 93 Dietary advice - conclusion Conclusion: Eat & drink what you like. It appears that speaking English is what kills you. (submitted by Natasha Jamison, EPID160 student)
- 94. 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
Notas do Editor
- Salam malekum, namaste, drasvuitsya, xin chao, huan ying, bienvenidos, karibuni. This lecture is on confounding.
- Our last two modules concerned sources of error – random error and systematic error. We focused on two broad categories of systematic error – selection bias and information bias. We now take up the topic of confounding, the third major category of systematic error. Confounding differs from selection bias and information bias in an important respect: with selection bias and information bias, the data we collect are incorrect. With confounding bias, on the other hand, the data may be correct, but our interpretation of them is faulty. Because it concerns causal interpretations, confounding bridges the topics of sources of error and data interpretation and analysis. So let’s begin with a few thoughts about data analysis.
- When a speaker wishes to emphasize the conclusiveness of a finding, she or he may well declare that, “The data speak for themselves”. But Sander Greenland, a major figure in the development of the modern conceptualization of epidemiology, counters that “Our data say nothing at all.” Data are conceptualized, constructed, collected, organized, and interpreted by people. The story “the data” tell is our story, a story which should be informed by what we find, to be sure, but our story nevertheless.
- As Sander Greenland explains, logically sound inferences involve two ingredients – (1) data and (2) assumptions. Without the latter we can make no inference. So we always need a conceptual model to derive meaning from data. The conceptual model consists of our assumptions about where the data come from, what they reflect, and how they relate to each other.
- 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.
- Or, what about when my partner says I’m grumpy because I get too little sleep? I can try sleeping too little – and ask my partner if I’m irritable. Then I can try sleeping enough – and ask her again. Then try sleeping too little – and ask her again, and continue that process until we’re both convinced.
- 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.
- But though cross-over experiments are a powerful strategy, there are major constraints on our ability to use them in epidemiology. First, of course, the “exposures” we want to study may be harmful or not under our control, in which case intervention research is not an option. Second, the effects of the exposure may not occur quickly or be reversible, in which case it is not practical to change the exposure and expect to see a change in the outcome. Also, the experimental subjects or the environment may have changed over time, so that we can no longer be confident that the only difference between conditions is the presence of the exposure.
- The key attribute of a crossover experiment can be summarized as follows: we can compare what happens to people who are exposed to what happens to the same people when they are not exposed – and we can compare these two conditions (almost) at the same time.
- Let’s consider this point with the example population that I have used in earlier lectures.
- To demonstrate the effect of an exposure, we would like to compare what happens to people with an exposure (shaded pink).
- To what happens to the same people but without the exposure.
- To demonstrate the effect of an exposure, we would like to compare what happens to people with an exposure (shaded pink).
- To what happens to the same people but without the exposure.
- This comparison provides the best evidence that the exposure causes the outcome. The modern formulation of causal inference in epidemiology and of the concept of confounding is based on this, as it is called, “counterfactual model”.
- There is an obvious problem with that comparison – we cannot do it. We cannot observe both conditions in the same people at the same time (which is why the model is called “counterfactual”). The solution to this problem is to observe a “substitute population”, a population whose experience will represent that of the exposed population without the exposure.
- So the “counterfactual model” for causal inference says that in order to infer that a factor causes an outcome in a population, we must compare the experience of the population when it is exposed to a factor with the experience of the same population at the same time but without the exposure. Since the counterfactual comparison is not possible, we use a “substitute population” that we hope will provide the comparison we need.
- Confounding is defined as a situation where the substitute population is not equivalent to the counterfactual condition we seek. So confounding arises when the distribution of outcomes expected for the substitute population differs from the distribution of outcomes expected in the exposed population without the exposure.
- Confounding, then, is a problem of comparison. We compare the exposed population to a substitute population. Confounding occurs if the substitute population does not show the “outcome in the exposed population without the exposure”.
- 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?
- If disadvantaged people do have a higher risk of developing bronchitis, then we would expect to find an association between air pollution and risk of bronchitis even if air pollution had no effect at all.
- Or take the question, “do seatbelts reduce crash injuries?” The counterfactual model says that we should compare injury rates among people wearing seatbelts to injury rates for the same people at the same time but not wearing seatbelts. Instead we compare injury rates for people who are wearing seatbelts to people who are not wearing seatbelts. But might people who wear seatbelts have other characteristics that affect injury rates? For example, do these people drive safer cars? Are they less likely to drive after drinking alcohol? Are they more likely to obey speed limits?
- Do bacterial sexually transmitted diseases increase risk of HIV transmission? There is a great deal of evidence that they do, but one of the problems in studying this relation epidemiologically is that people acquire STDs the same way that they acquire HIV – through unprotected sexual intercourse with an infected partner. So if we do find greater HIV seroprevalence in people with STDs than in people without STDs, is the reason that the STD increased susceptibility to the HIV virus or was the person simply more likely to have come in contact with an infected person?
- Another question where concern for confounding is prominent is whether teen cigarette smoking leads to use of other illicit drugs. You may have heard the expression that tobacco is a “gateway drug” that leads to use of substances such as marijuana and cocaine. Indeed, young people who take up marijuana and cocaine are very likely to have smoked cigarettes. Did the cigarette smoking increase their chances of trying other drugs? Or were there other factors (e.g., sensation-seeking, peer influences, media use, lack of social support, negative emotions) that led them both to try smoking and to take up marijuana and cocaine?
- For each of these proposed causal relations, we should ask 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? For each of these causal relations, the obvious choice for the substitute population is likely to differ importantly from the “exposed population without the exposure”, so that confounding will hamper our attempts to infer a causal relation.
- So that’s the philosophical background. What are our learning objectives for confounding: First, we want to: Understand confounding in a basic sense – many of us are still trying to develop a complete understanding. Recognize and distinguish between potential confounding and actual confounding. Know how to control confounding in an epidemiologic study. Be able to follow discussions and arguments about confounding. And finally (on the next slide)
- 5. Be able to define and explain the terms used in the preceding learning objectives: confounding, potential confounder, actual confounder, and control of confounding.
- Although the counterfactual framework just presented is the most useful for analyzing what is going on in a complex situation, the traditional perspective is useful for developing an intuitive grasp. Confounding has been defined as a “mixing of effects”. The premise is that we are evaluating whether a possible risk factor (sometimes called a “putative risk factor”) is actually associated with increased risk of some outcome. The question arises whether some other risk factor may in fact be responsible for at least some of an association we observe between the putative risk factor and the outcome. It is also possible that the effects of some other risk factor may obscure an association that truly exists between the putative risk factor and the outcome.
- 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.
- Let’s use a diagram to illustrate the arithmetic of confounding. Suppose that we are interested in whether an exposure – for example, frequent anger – increases risk of a disease outcome – for example, memory impairment. Suppose also that it is already known that regularly getting inadequate sleep leads to memory impairment. We are going to create an example to illustrate how an effect of inadequate sleep could exaggerate the apparent effect of frequent anger. This slide shows a cohort of people at baseline, a follow-up interval, the subset that develops memory impairment (the “disease”), and the subset that does not.
- Suppose that the known risk factor (inadequate sleep, symbolized by blue font), is present in about a quarter of the population. In the above diagram, the baseline population, at the top, is divided to show that about one-in-four people do not get enough sleep.
- If inadequate sleep increases risk of memory impairment, then during a period of follow-up, a greater proportion of sleepy people will develop memory impairment, so that they will be disproportionately found among those with memory impairment (shown in the lower left-hand box). That means that people who do get enough sleep will be disproportionately found among those without memory impairment (in the box on the lower right).
- 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).
- As we know from the conceptual model of causal inference presented at the beginning of the lecture, the causal comparison we want to make is that between disease incidence in the angry people and disease incidence in the same people if they did not frequently become angry. Since we cannot observe that counterfactual situation, we compare instead to disease incidence in a substitute population. Unexposed members of the cohort serve as the substitute population. But suppose that the exposed (i.e., angry) population has a greater prevalence of people who do not get enough sleep – a very real possibility, since inadequate sleep is likely to make people more prone to anger.
- If sleep time is unevenly distributed between the exposed and unexposed members of the cohort, then the disease incidence in the substitute population – the unexposed – will not give us an accurate indication of what the disease incidence in the exposed population would be without its exposure.
- 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.
- This slide shows the members of the cohort who do not have the known risk factor, inadequate sleep. I will refer to inadequate sleep as a potential confounder, and we will see in a few slides that it is in fact an actual confounder. This slide shows the cohort members who do not have the potential confounder, i.e., the people who get enough sleep.
- … and this slide shows the members of the cohort with the potential confounder. They are sleep-deprived.
- Let’s make up some numbers to illustrate the process more concretely. Here again are the members of the cohort who get enough sleep. We will suppose that 2,500 of them are frequently angry (i.e., exposed, the left side of the slide) and 8,300 are not. Let’s suppose that the incidence of memory impairment among angry people who do get enough sleep is 100/2,500, or 0.04 (i.e., 4%), and the incidence proportion (cumulative incidence) of memory impairment among people who have neither frequent anger nor sleep deprivation is 166/8,300, or 0.02 (in other words, 2%).
- This slide shows the calculated incidence proportions of 0.04 and 0.02 among the cohort members without the potential confounder.
- So the incidence proportion ratio for memory impairment in relation to frequent anger is 0.04 / 0.02 = 2 among people without the potential confounder. In other words, among well-rested people, the risk ratio for memory impairment in relation to frequent anger is 2.0.
- What about the people with the potential confounder, the people who are sleep-deprived? Suppose that 2,500 of them are frequently angry and 1,700 are not. Since we are assuming that sleep-deprivation increases the incidence of memory impairment, let’s suppose that the incidence proportion is 200/2,500, or 0.08, among the sleepy, angry people and 68/1,700, or 0.04, among the sleepy but not angry people.
- This slide shows these calculated incidence proportions of 0.08, or 8% and 0.04, or 4% in the cohort members with the potential confounder (sleep deprivation).
- So the incidence proportion ratio (or, if you prefer, the cumulative incidence ratio) for memory impairment in relation to frequent anger is 0.08 / 0.04 = 2 among the people with the potential confounder, inadequate sleep. Their risk ratio happens to be the same as the risk ratio among people without the potential confounder. Of course, that was not an accident – I made the numbers up.
- 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%.
- The incidence proportions are displayed on this slide, in pink – 0.06 for the angry people, and 0.023 for the people who are not frequently angry.
- 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.
- In this example, both the exposed group and the unexposed group are heterogeneous. That is, they are composed of diverse subgroups defined by the potential confounder, inadequate sleep. The overall incidence proportion in a heterogeneous group is a weighted average of the incidence proportions for each of the subgroups – it this case, the rested and sleep-deprived subgroups. So, for example, the incidence of memory impairment in the angry people who get enough sleep is 100/2,500, or 0.04. The incidence of memory impairment in the angry people who do not get enough sleep is 200/2,500, or 0.08. Since half of the angry people get enough sleep and half do not, the weighted average assigns equal weight to each incidence, giving us an overall incidence among angry people of 0.06.
- 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.
- Here is a diagram to illustrate the concept that overall incidences are weighted averages. This slide shows the exposed group, which comprises 2,500 angry people who get enough sleep and 2,500 angry people who are sleep-deprived. Imagine that we had a giant ruler, demarcated with incidence proportions, from which we could hang a basket with each subgroup from either end. Then we position a fulcrum under the ruler and see where the ruler balances. When the ruler is balanced, the pivot will be located at the weighted average of the incidence proportions for the two subgroups.
- Among the unexposed, the number of people who get enough sleep is much greater than the number who are sleep-deprived. So the weighted average, the pivot point where the ruler balances, is much closer to the incidence for people who get enough sleep.
- So the reason that the comparison between the angry and not angry people is confounded is that we are comparing weighted averages derived using very different weights.
- If we make the comparison within the subcohort that get enough sleep, then the comparison is valid, and the incidence proportion ratio is 2.0. The levels of the covariable (sleep status) are often referred to as “strata”, so a comparison among people who get enough sleep is a ‘stratum-specific comparison”.
- The comparison within the subcohort that are sleep-deprived is also valid, and the incidence proportion ratio is also 2.0.
- But the comparison of the overall incidence proportions, the crude ones, does not take account of sleep status. These crude incidences reflect both the stratum-specific incidence proportions and also the relative sizes of the two sleep status groups, so this comparison is confounded by the different distributions of sleep status.
- Since the angry people are evenly-divided between those who get enough sleep and those who do not, the counterfactual comparison we would like to have for them would also be evenly divided. The substitute population should therefore have equal weighting for the incidence proportions for the two sleep status groups. This diagram shows such a comparison. The comparison between the overall incidences here is not confounded.
- So the risk ratio, or RR, from comparing the groups that get enough sleep is 2, the RR from comparing the groups that do not get enough sleep is 2, and the RR from comparing the angry people to a valid substitute population is also 2. 2 is the unconfounded RR, the unconfounded risk ratio or incidence proportion ratio.
- But the crude RR, from comparing the overall incidence in the angry group to the overall incidence in the unexposed group, is confounded.
- We can use the unconfounded RR to calculate an “RR for confounding”, by dividing the confounded RR of 2.6 by the unconfounded RR of 2.0. The result, 1.3, tells us that if anger had no influence on memory impairment, we would still observe an RR of 1.3 due to the different sleep status proportions between the angry and not angry people.
- Here is a diagram displaying that situation. Here, anger has no effect. Within each sleep status subgroup, the incidence of memory impairment is the same for the exposed and unexposed. But because of the different distributions of sleep status, the crude incidence in the exposed is 1.3 times that in the unexposed. This RR of 1.3 is entirely due to confounding.
- Although the preceding example used a cohort study, there is no real distinction in the mechanics of confounding between a cohort study and an entire population. But how do things look when we see the population through a different study design, in particular, through a case-control study design?
- A case-control study will estimate the odds ratio between frequent anger and memory impairment by dividing the odds of exposure to anger in cases by the odds of exposure in controls. If the case-control study enrolls all new cases of memory impairment in the cohort or population, then the case group will be the same as in the example we have just considered. In that example, the odds of exposure in cases are: (100 + 200) / (166 + 68) = 300 / 234 = 1.28. These are the odds of exposure in the people who develop memory impairment.
- If we chose our controls as a random sample from the baseline population (in other words a “case-cohort” design), then the expected prevalence of angry people in the control group would be the exposure prevalence in the cohort, which is (2,500 + 2,500) / (2,500 + 2,500 + 8,300 + 1,700) = 5,000/15,000 = 0.33. So the exposure odds in the controls would be 0.33 / 0.67 (which is 1 minus the prevalence) = 0.5.
- The odds ratio would then be 1.28 / 0.50 = 2.6, which, as it should be, is the same as the incidence proportion ratio for the cohort. The case-control study is confounded to the same extent as the cohort study was. We would also see confounding if we conducted a person-time analysis and used density controls. If we used cumulative controls (controls chosen from among the noncases at the end of follow-up, sometimes called “survivor controls”), then the OR would be greater than the RR, but the mathematics of confounding would be similar.
- What if we had restricted the case-control study to the subcohort who get enough sleep? The odds of exposure in the cases would then be 100 / 166 = 0.6.
- The expected odds of exposure in the controls drawn from the baseline subcohort of well-rested people would be 2,500 / 8,300 = 0.3.
- And the odds ratio would be 0.6 over 0.3, or 2 – the unconfounded value.
- Similarly, if we had restricted the case-control study to the people with sleep deprivation, the odds of exposure in the cases would be 200 / 68 = 2.94.
- The expected odds of exposure in the controls drawn from the baseline cohort would be 2,500 / 1,700 = 1.47
- 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.
- So when do we need to worry? What is a potential confounder? A potential confounder is something that affects the incidence of the disease or other outcome under study. Thus, a potential confounder is a disease determinant, a risk factor. Since epidemiologic studies can count only cases that are detected, a factor that influences the detection of a disease can also confound. A potential confounder must have the potential to provide an alternative explanation for an observed association.
- 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.
- 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.
- 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.
- 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.
- A significant limitation of all of these methods, however, is that they can be used only when we know and can measure the potential confounders. When we do not know the factors to control or cannot measure them, the only strategy available is to randomly assign the exposure, in other words, to conduct a randomized intervention trial. In a randomized trial, the exposed and unexposed groups will be alike (though only on average and at baseline) – they will be alike on all characteristics. So randomization provides the possibility of controlling for unknown potential confounders. This possibility is one of the key strengths of randomization and is a reason that randomized trials have a special significance for causal inference.
- A problem with epidemiologic research – indeed, with all observational research – is that there are many limitations on our ability to control all confounding. Apart from randomized assignment of exposure, effective control of confounding requires knowing the causal pathways, knowing all of the relevant causal factors, and measuring these factors – accurately. Errors in measurement, random ones as well as information bias, reduce the ability to control confounding by those factors.
- In addition to accurate data, control of confounding requires assumptions. Besides a conceptual model that supposes some factors as independent and others as intervening factors, mathematical modeling, such as logistic regression, involves assumptions about the mathematical form of relations between risk factors and disease risk. These assumptions should be tested. Large, randomized experiments are uniquely powerful for controlling confounding and, therefore, for causal inference, but they are very expensive, logistically challenging, require enormous effort, may take a very long time, may raise ethical concerns, and may not work.
- On the other hand, without the benefit of a randomized trial it can be very difficult to figure out what is going from the data. For example, how do we examine the relation of overweight to coronary heart disease (CHD) risk, knowing that cholesterol, hypertension, and diabetes all increase CHD risk but that overweight contributes to these risk factors? If we control for cholesterol, hypertension, and diabetes, we obscure at least some of the effect of overweight. If we do not control for cholesterol, hypertension, and diabetes, then the association between overweight and CHD may be confounded by these risk factors.
- Confounding is a challenging topic, so let’s restate the main points. First, interpreting data requires assumptions about causal relations, including what factors to regard as potential confounders. Potential confounders are factors that affect incidence but are not themselves a consequence of the exposure of interest.
- Second, the potential for confounding does not mean that confounding actually has occurred. That is why we refer to factors that affect disease incidence as potential confounders. For confounding actually to occur, exposed people and unexposed people must differ on the potential confounders. There must be an unfair comparison. Only then can potential confounders actually distort our interpretation of an observed relation between the exposure and disease of interest. So a potential confounder becomes an actual confounder by being differently distributed in the exposed and unexposed groups.
- 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)
- Fourth, we can control confounding in the analysis of the data if we can stratify the data according to categories of disease determinants that are not themselves caused by the exposure (i.e., they are potential confounders, not causal intermediates). Mathematical models, such as logistic regression, Poisson regression, and Cox proportional hazards regression, are sophisticated procedures for accomplishing the same thing.
- Fifth, the best way to understand a case-control study is to regard it as a window into a cohort and then to analyze what is happening in the cohort. It’s helpful to remain aware, though, that many books and teachings still follow the traditional and somewhat misleading perspective that a case-control study is fundamentally a comparison of cases and controls. Obviously we do compare cases and controls in a case-control study, but the fundamental comparison that underlies a case-control study is a comparison of incidence in exposed and unexposed groups in the cohort from which the cases are arising.
- Confounding is a fascinating but complex topic, so do not be discouraged if it takes you more than once to grasp it. It’s taken me over a quarter-century – and I’m still confounded by some aspects of it!
- And for an epilogue, here is an example of how the interpretation of data depends upon our causal model, courtesy of a former EPID160 student. 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.
- 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.
- The conclusion? Eat & drink what you like. It appears that speaking English is what kills you. (submitted by Natasha Jamison, EPID160 student) Vous êtes d’accord? A bientôt.