Hello, I'm Ned Colange. Welcome to this section of the 2023 ACPM review course. I am going to present the session on epidemiology. The objective of this session is to review the major terms, definitions, and concepts of epidemiology. Here's our agenda for this time period. This is the introduction, so we'll be done with that quickly, and then just go over what we hope to get through in this time slot. I'll start with talking about the measures of disease frequency, then move on to descriptive epidemiology, and measures of excess risk. We're going to spend some time on discussing study design, broken up into descriptive studies, case control studies, cohort studies, and then the intervention studies, clinical trials, and quasi-experiments. We're going to move on to talk about epidemiologic evidence and causal inference, and then confounding and effect modification. We're going to spend some time on disease screening, and finish up the lecture with a discussion of the terminology around infectious disease epidemiology. So let's go ahead and get started with measures of disease frequency. Epidemiology started with counting, and counting the number of deaths, or counting the number of people with a disease. So, counts is a very important measure of disease frequency, but it's missing something. So if I told you there are about 30 infant deaths in Wyoming a year, and 300 infant deaths in Colorado a year, I wouldn't want you to conclude that the death rate is higher in Colorado, and what you're missing is the denominator that gave rise to that numerator. So the denominator allows you to account for the denominator, or size of the population. And when we talk about a rate, we then imply a period of time. So it ends up that the population of Colorado is about 10 times that of Wyoming, although the states are about the same geographical space. But that denominator, and then the conversion to rates, allow us to make more fair comparisons from one area to another, or one population to another. The next term I'd like to introduce is cumulative incidence. And most often when you hear the term incidence, we're actually talking about cumulative incidence. So we commonly use it as synonymous. Cumulative incidence, or incidence, is the number of new cases of a disease occurring in a specified time period, divided by the number of people initially at risk. And you see I've highlighted the word new. So that means we're not looking at existing cases. When we're talking about incidence, we only want to know the new cases that arose in that time period. This is a very useful and commonly used measure. It's synonymous with attack rate, which is kind of a short-term incidence, often used in infectious disease epidemiology. It's also used as the risk of disease. So if the cumulative incidence of heart disease in a certain age group of population is one in 1,000, that means the probability or the risk of getting the disease in that population is also one in 1,000. So as you heard me say, it also is synonymous with the probability of getting the disease. Incidence density is another measure of incidence. It starts with the same numerator, which is the number of new cases of a disease occurring in a specified time period. But now the denominator is the total amount of person time at risk that was contributed during the time period. So person time is this concept of, if I'm in the denominator for a year, I have now contributed one person year to the denominator. Incidence density estimates the rate of occurrence of disease per unit of time relative to the size of the population at risk. And it accounts for what we say is reality, the reality of in and out migration, censoring, death, et cetera. So in other words, individuals can move in and out of the denominator, but they're still looked like contributing to the numerator if it occurs while they're in the denominator during that time period. What this does is yield a more precise instantaneous risk estimate. And when you divide two incidence densities, you get a more precise relative risk calculation. We don't use incidence density much in usual discussions around disease frequency because that person years denominator is confusing, a little harder to understand. And actually it's really its utility in calculating relative risks with greater precision that incidence density comes into its own. Now I'd like to move to a different term, which is prevalence. And now we're going to talk about the number of existing cases of a disease at a specific time. Here the denominator is the size of the base population at that time. Prevalence provides us with a snapshot view of disease frequency in a population at a single point in time. And it's very important for planning and allocation of resources. So for example, if you're thinking about type two diabetes, this gives you the amount of type two diabetes in a population that you need to think about what healthcare resources, including primary care, specialty care, medications, lab testing, hospitalizations, et cetera, that that size of a population of people with that condition are going to need. There are two flavors of prevalence. One is a point prevalence, and it refers to the prevalence at a single point in time. So for example, if we were all in a room together with say 200 other board eligible students, and I just asked, how many here are currently suffering from the symptoms of upper respiratory tract infection? Let's say maybe three or four people hold up their hands. That gives me a point prevalence of three or four per 200. So that's a single point in time. If instead I ask the question, how many of you have had URI symptoms over the past 12 months? I would get a lot more people holding up their hands, maybe even half. And so that becomes a period prevalence, the prevalence measured for a specific time period. In that example, a one year time period. So we're going to move on from kind of measures of frequency of disease in a population to other useful measures that we use commonly in epidemiology. We're going to start with mortality. So the total mortality is going to be the number of people dying in a specified time period divided by the average number of people alive during that time period. So that ends up measuring, with the denominator being all the people alive, just how many people died. Mortality is a useful number comparing, say, state to state or nation to nation, kind of think about the impact of disease and other factors that influence how long people live. We could change the numerator to dying of a disease in the same time period, like lung cancer, and then this overall mortality becomes a disease-specific mortality. Let's move on to case fatality, and I'm going to pause for just a moment to say we're now going to change the nature of the denominator. It's really important because before, remember, the entire population has been in the denominator. But when we go to case fatality, while the numerator is the number of people who die of a disease, the denominator is now the total number of people who get the disease. So it's no longer that total enumeration of the population. It's a very specific number which changes the nature and the characteristics of this measure. So now we're measuring disease prognosis rather than disease frequency. And usually we talk about case fatality in a specified time interval, such as a one-year case fatality rate or a five-year, etc. Another measure where the denominator changes from everyone in the population is proportional mortality. Let's look at this now. We have the number of deaths due to a disease in a specific time period divided by the total number of deaths in that time period. So now the denominator is deaths. So it's not the whole population. It's not everyone with the disease. You're actually looking at a proportion of the deaths due to a specific condition. This is a useful measure that we use often to talk about the impact of mortality. But note that it can be misleading if mortality rates for other causes are unusually high or unusually low in a group. I'd like to give an example of this last statement. So there was a study in 1960 published looking at Hodgkin's disease in teachers. And the report talked about 2.5% of deaths in teachers were due to Hodgkin's disease, while 1% of deaths in the general population was due to Hodgkin's. And the authors in the study concluded that teachers were at 2.5 times higher risk for death from Hodgkin's. Well, that 2.5 times higher risk is really a relative risk for death from Hodgkin's disease. And if you're talking about that comparison of those two numbers, they're not a proportional mortality measure. They're a mortality measure from Hodgkin's. And in order to get there, you actually have to divide the number of deaths from Hodgkin's by the total number of teachers, rather than here, the total number of deaths in teachers. And so the 2.5% of deaths in teachers are due to Hodgkin's is the way you would phrase a proportional mortality. The issue that underlie this misstatement is that teachers were less likely to die of other causes. They were less likely to die of motor vehicle crashes, less likely to die of heart disease, and less likely to die of other causes of cancer. In general, teachers are a fairly healthy population. Because of the lower rate of deaths due to other causes compared to the general population, that percentage of deaths due to Hodgkin's was inflated by the decrease in the deaths from other causes. So the warning here is that when you're given a problem that asks you to talk about risk or relative risks, make sure you have the information available. So I wanted to provide an example that is a question that might be on the exam or some form of it. I've certainly used it in teaching myself. Here's the problem. In Denver, 10% of deaths in white children under 10 are due to leukemia versus 5% of deaths in black children. Which are the following are true? So look at the numbers given you. The 10% of deaths in white children is a proportional mortality number. Therefore, that means 1 out of 10 deaths was due to leukemia versus the higher risk of deaths in black children. The first answer is the relative risk for leukemia in white versus black children is 2.0. Now we're going to talk about relative risks in just a few minutes. What I already told you is a relative risk requires risk in the numerator and the denominator. And you don't have risk, you have proportional mortality. So A is going to be false. Number B, the attributable risk for leukemia in white versus black children is 5 per 100. We're going to go over attributable risk 2, which is the subtraction of the two rates of disease. Again, you don't have a rate of death due to leukemia. You have these proportional mortality numbers. So B would be false. And C is neither the attributable risk nor the relative risk may be determined from the data provided. And that is the correct answer. This slide just kind of goes over that reasoning again and gets to C as the correct answer. So my guidance for you in taking the exam is always look at what you need to compare to come up with the answers provided. And if you don't have that information, it's going to be some form of C that you don't have information you need to do that calculation. Now we're going to move on and talk about how disease rates can be related. The first example is that prevalence, incidence, and specifically incidence density and duration of disease are related. So the formal formula would be prevalence is incidence times the average duration of disease divided by 1 plus incidence times the average duration of disease. Now think about what happens when prevalence is low, that is, less than 10%. Then that incidence times the average duration of disease will be a small number. It's going to make 1 plus that number very close to 1. So therefore we can collapse this more complicated equation to prevalence equals incidence times duration. Now this only holds when the incidence and duration aren't changing over time. So if there's an increase in some risk factor that makes incidence go up, or if we have new treatments that make duration longer, then this doesn't hold as well. However, when they're stable, it helps you predict what a change in one variable will cause in another. So if you're looking at the prevalence and you see it goes up, you know either the incidence has gone up or the duration of the disease has gone up. And the corollary is true as well. If you see prevalence has gone down, either the incidence or the duration has gone down. Mortality, incidence, and case fatality are related as well. Mortality is going to be the incidence times the case fatality, which if you go back to the formula is going to make sense. You just take out the case fatality, it gives you the number of people dying over the total number of people. Now again, this only holds when incidence and case fatality are stable over time. And then finally, survival rate and case fatality are related, and it's a simple relationship. If you don't die, you survive. So if you take one minus the case fatality, you get the survival rate. If the one-year case fatality is 20%, then the one-year survival rate is 80%. I just want to provide a few more useful rates and measures that we use commonly in epidemiology and public health. We're going to start with the birth rate, which is the number of live births in a year, divided by the populations in thousands at mid-year. So birth rate is a useful number in terms of kind of considering the stability of a country or a population. Usually as things like education and economy goes up, socioeconomic status, we see the birth rate start to level out and even go down. The similar is true with the fertility rate. Now you still have the number of live births in the numerator in one year, but now the denominator is only looking at women of the average childbearing age or recognizing that women can get pregnant before 15 and over 44. The way we use this measure, though, is the number of thousands of women aged 15 to 44 years at mid-year. Now this is the most common way of doing fertility rate. I have seen some sources calculate the total fertility rate by adding the births per women for five-year age categories, which can smooth out the number. The other thing I would say is that recognizing that reproductive age can dip down lower and exceed 44, some sources will extend the range to 10 to 49. Next, I'd like to talk about the fetal death rate or the stillbirth rate. Here the numerator is the annual number of fetal deaths, which is defined as a gestational age 20 weeks or greater or a birth weight of 350 grams or greater in the numerator. That's divided by the annual number of fetal deaths plus live births in thousands. Now I've asterisked the number for fetal deaths because there are different definitions depending on where you are. This is the current U.S. definition, the WHO used 22 weeks and 500 grams as a cutoff for a fetal death. Prior to those weeks gestation or the birth rates, these are termed as miscarriages or spontaneous abortions and not fetal deaths. Fetal deaths is an important measure because it's a measure of the prenatal care and kind of maternal nutrition and overall maternal health prior to the pregnancy. Neonatal death rate is the annual number of deaths in the first 28 days of life divided by the annual number of live births. Now you're thinking about a broader group of metrics. So you have kind of maternal health, you have prenatal care, you have interpartum care, and you have neonatal care for the first 28 days, all summed up in a single metric. Perinatal death rate is trying to narrow this to the annual fetal deaths plus deaths in the first seven days of life divided by the annual number of fetal deaths plus live births. And again, that fetal death definition can change depending on where you are. But this is now saying, okay, I'm not going to look at all of the maternal health issues, but I am going to try to pinpoint this, what I want to say, perinatal time period to capture kind of obstetrical care and neonatal care. And finally, the infant death rate is the annual number of deaths in the first year of life divided by the annual number of live births. The infant death rate is the one you'll see most commonly because it's easiest to measure. It is measured in almost all nations, and it can be used to compare nations to one another. I would point out that it includes a lot. Now you're talking about maternal health, prenatal care, perinatal and obstetrical care, neonatal care, and then child care, and nutrition, and a lot of other issues that come in. But it's often compared because of its utility and ease in comparisons across nations and across states. Finally, I want to talk about a measure that's different from the others we've talked about and go over the years of potential life lost. This is a measure of premature mortality, and it's gonna take into account not only the cause of death, but the age at which the death occurred. The idea behind the years of potential life loss is to give more weight to deaths earlier in life compared with later deaths. And the concept really came out of the care for pediatric patients over time, and the kind of feeling that a death of a child should carry more weight than the death of an older person. Now, I have to admit that's a value judgment, especially as I've joined the ranks of the older people. And I hope you understand the concept behind it, trying to say, it's not just that you died, it's the age at which you died at that is an important public health issue. I wanted to go over a little bit about how it's calculated. You stratify deaths usually into 10-year age intervals. So let's say I have a disease like cystic fibrosis, where at least in the past, usually affected individuals didn't live past 30. So I could take the deaths and I could look at these 10-year age groups and say, boy, for the zero to 10-year olds, I had two, in the 11 to 20-year olds, I had nine, and the 21 to 30-year olds, I had four. So those are the deaths I have. Then I want to calculate the number of years lost between age 75 and the midpoint of that interval that I just calculated. So the concept is 75 is around the average age of death in the US, and the midpoint, if you're in that zero to 10-year age group, is five years. So conceptually, those two children on average lost about 70 years of potential life. Of the 11 to 20-year olds, those nine children lost on average about 60 years of potential life. And in the 21 to 30-year old age group, each one of those lost an average 50 years of potential life. Now what you do is you take the number of deaths and just multiply it by the number of years lost in that interval. So for 75, I'm sorry, for the zero to 10-year age group, you have 140 years of potential life lost. For the 11 to 20, 540 years of potential life lost, and 50, I'm sorry, the 21 to 30-year olds, an average total of 200 years of life lost. To get the total years of potential life lost, you just add up those numbers. So here are the total years of potential life loss will be 840 years. So again, this is a way of thinking about premature mortality, and when the deaths actually occurred, not just that they occurred. And it changes the epidemiology of mortality as we talk about it. So for every year except two in the United States, the leading cause of years of potential life lost have been injuries, either intentional or unintentional injuries. And that's true up to, it's always the leading, I'm sorry, injuries are the leading cause of death for all individuals up to about age 44. And compared to all ages, it's the leading cause of years of potential life lost. Now, if I was gonna ask you, what happened in those other two years? And I'll just pause and say, what do you think caused the years where there was a higher YPLL due to something other than injuries? If it doesn't come to you instantly, I would say, the years were 81 and 82. And so the answer is, it was HIV AIDS disease that caused a large increase in the number of deaths to young men. So that kind of gives you a feeling about how years of potential life lost work and how they're impacted by mortality trends in the population. I did wanna talk a little bit about something called lifetime risk. You'll often see people talk about lifetime risks as a way of talking about the importance of a different, I'm sorry, of a specific condition. So lifetime risk, I'm sorry, life expectancy is the average age of death given a live birth. And you gain additional life expectancy as you get older and don't die. So how you get age-specific life expectancy is to actually do survival analysis using a life table, which we're not gonna cover in this lecture. And I'm not certainly cover it much in the class because I don't think very many people do life table analyses, but instead hope someone else has done it for you. So my warning is be careful of cumulative lifetime risk estimates that don't give you the life expectancy on which they're based because that cumulative lifetime risk is very dependent on that age. So for example, if I was gonna talk about breast cancer, I'd say, you know, what percentage of deaths in women in the US do you believe come from breast cancer? And some of you might say one in eight, but that's actually the incidence, the cumulative lifetime incidence of breast cancer mortality. The real mortality for any cohort of women is about 3%. So about 3% of women in any age cohort die from breast cancer. That one in eight is that cumulative lifetime risk. Now, I wanna talk a little bit about where that came from. So before we started mammography, we would measure life expectancy. At the time, it wasn't 79 or 80, which is a woman's life expectancy today. It was less, it was around 74 to 75. And so the way they calculated, they said, what is the woman's chance of dying from breast cancer given a life expectancy of 74 years? And when they first measured it, it was one in 11. And then Nancy Reagan got breast cancer. And this test, which we already knew, we already had RCT evidence that it saved lives, it was just not used. And the use of mammography was somewhere around 10 to 12% in the US. When Nancy Reagan got breast cancer, it jumped up precipitously. And what happens when you start screening a previously unscreened population is you start detecting what we call prevalence cancers, cancers that were already there but had not yet been detected because they hadn't been screened for. So we added in all those prevalent cancers with all the incidence cancers, and that number went from one in 11 to one in eight. And the American Cancer Society seized on that one in eight number and used it to publicize the importance of breast cancer screening. Now, the other thing that happens when you start screening and you maintain a higher level is you do something we call you clear out the prevalence pool. And so all those prevalent cancers were detected and the rate returned to where it was prior to the increase in mammography use, which was one in 11. The American Cancer Society decided that telling women that the risk went down was not a good message. And might actually work against the concept of trying to promote mammography. So what did they do? They just pushed up the life expectancy age range over which they're calculating the lifetime risk. And they continued to do that. So for today, when they say one in eight women in the US will die of breast cancer, they mean one in eight women who live to age 90 will die of breast cancer. And so the number has been manipulated for the purpose of advocacy. And I just want to point this out when you look at lifetime risk estimates. It's an important question to ask. It's interesting to me though, that half of the women in the US, more than half, will never reach that number or would never be protected from that number because they will die before they reach age 90. All right, now we're gonna turn to a new topic, descriptive epidemiology. So we talked a lot about rates and measures and the ways that we talk about epidemiology. These are all used in descriptive epidemiology. And I want to talk about why these are useful. They can be used to provide clues to etiology. And once we know what causes a disease, that can help us think about prevention. Descriptive epidemiology can help us target screening efforts. Because as we talk about later in this talk, if you screen a higher risk population, the overall testing characteristics improve. You can use descriptive epidemiology to aid in diagnosis, to aid in the planning of health services, and to provide baseline data so that we know what's happening with disease trends over time. So when we think about descriptive epidemiology, we have to think about these proportions and these rates. And you want to think about where does the numerator come from and where does the denominator come from? So numerator data for descriptive epi can come from vital records. And that's probably, I mean, most of you, sorry, many of you in your careers will at some point use birth or death certificates to look at numerator data for both of those conditions. So when you're talking about mortality, or we're talking about birth metrics, those come from vital records data. You can also get numerator data from disease reports. So all 50 states have reportable disease statutes that say we have to report things like measles or other infectious disease, diseases, sexually transmitted diseases, HIV infections, et cetera. So those are very common and can give us numerators. Remember that COVID-19 was a reportable disease. And so we got a lot of our numerator data from that process to try to think about the rates of disease for COVID. There are also things like cancer or tumor registries in states that allow you to develop cancer numerators for the data as well. And finally, we are seeing more and more development of chronic disease registries, especially as we've tapped into the electronic medical record, which is the next source of numerated data. So medical records and now the EMRs are a rich source of things like what people are visiting the doctors for, what medications they're getting and what chronic diseases they may have. And finally, if we don't have a metric or a way of measuring things, we often use surveys. And there are a number of nationally run surveys that develop numerator data that we can then use with the survey sample to develop descriptive statistics. Now, there are problems with numerator data and these can kind of range from problems we may have in identifying the case, but also problems in what is a case. So one of the things that CDC does the very beginning of any investigation is they spend a lot of time on how are we gonna define a case? You could see this happen with long COVID where CDC went through a long painstaking process in defining what a case of long COVID was. And then there were grants given to other groups like the National Academies of Medicine in order for them to come up with definitions as well. If those case definitions are different, you can start having problems with numerator data. Plus you need a way to say, how am I gonna detect a case? So how am I gonna know when I have a case of long COVID if I'm not identifying it in a surveillance or structured way? Denominator data seems more straightforward to me, almost always comes from census or vital statistics records. Now, the census is great. I think many of us have lived through more than one. We know that they become a mixture of samples and enumeration. Whereas when they started, they were complete enumerations. There are weighted samples, there are errors, it can be associated with the weighted samples. The census is only done every 10 years. Although there is a major mid-decade update that's based both on ongoing measurement and modeling. And then every state does an every year update trying to take into account births, deaths, immigration and emigration. So that's a very common source of data. A common source of denominator data. Another source though is to say, where did I get my numerator data from? So if I got it from the medical record, did I get it from a health plan like Kaiser Permanente or Geisinger or Lovelace or Intermountain Health so that I can develop a denominator based on who's enrolled in those health plans. And then the numerator can then come from the electronic medical record. I could also get industry or union records and alumni roster. So I don't know how many of you taking the course are Harvard alums, but they do an annual survey of all their alumni and they have a high response rate. So the Harvard alumni survey is a great example of denominator and numerator data from a very specific survey source. So now that we know where the data come from, let's talk a little bit about frameworks for reporting descriptive data. And it's kind of the who, what, when, where, how or why for measures of disease frequency. So what kinds of people get the disease? So we think about characteristics such as age and age is complex in things like immunity to infectious diseases, where infants might be, for example, or children under one more susceptible to enteroviruses and have more severe illness. Whereas if you survive to adulthood, you've seen a lot of enteroviruses. And so you probably aren't gonna get very ill when you're exposed to a new one. Flip side, infants' immune systems are faster at, or young children, at faster are responding to a new antigen. And so they might fare better with something like, something novel and new like West Nile virus, where the children tended to have not a severe disease, but because the adults had never seen anything like it and their immune systems were not as nimble, older people had more disease. Age also has a role in slowly developing diseases because you may need a latent period, a long latency period, in order to see the onset of disease. And there are also environmental exposures that may vary by age in terms of occupation, in terms of risk-taking behavior for younger people. And so age has a big impact. There are other things like sex. There are anatomical and physiologic differences between the sexes. We know these affect susceptibility, especially if you can't get the disease because you don't have the target organ. But we also know there are many differences in lifestyles, environmental exposures, education, temperament. And so these sex differences can impact who gets the disease in major ways. Race ethnicity is also an area where we see variation, but here it's really disproportional impact, mainly associated with discrimination and systemic racism. There really are very few genetic differences in susceptibility. And instead we see these associations going along with education, socioeconomic status, behaviors, and then chronic stress and allostatic load. We talked a little bit about socioeconomic status as well. Here you can impact nutritional factors, lifestyle, access to healthy lifestyles, and adequacy of medical care. Clearly our occupation can impact who gets kind of what kinds of diseases, and it occurs in different ways. And so there are certain well-paid medical subspecialties where suicide rates are high among otherwise affluent people with high education and high socioeconomic status. But occupation can also be a direct risk in terms of I'm a line worker for the power company or other more risky combinations, occupations. Marital status is interesting in that people who get married tend to live longer than people who don't. And how that has to do with stress and other harder to measure factors is complex and not always known. However, we do know that when a spouse dies, the life expectancy of the remaining spouse shortens considerably. And then there can be other factors associated with what kinds of who gets the disease that might be important for some diseases and not for others. There are also issues about where is the disease common or rare? And what are the characteristics of those places? So this is like physical environment issues, even things that are hardwired or less hardwired into the environment, such as extreme temperatures on either side. So people who live in Arizona, in Phoenix, and Tucson are more likely to suffer heat-related illnesses than people who live in Northern or Northern climes where the heat is not quite as excessive. There are also man-made exposures that may vary by place. And these are usually toxins that we create. We used to see when asbestos was a major component of brake pads that mountain towns that were at the bottom of mountain passes had higher rates of lung cancer. And eventually the conclusion was it's from people using their brakes to slow down coming down the mountain pass, creating asbestos fibers that then settled in the communities on either side. There are also man-made exposures like PFAS, peri and perifloral alkyl substances that are related to a number of cancers and other conditions and people who live along waterways or drink from groundwater that is contaminated by industrial cleanup for PFAS can have different diseases or higher rates of disease caused by those environmental exposures. So then we think about time, and how does the frequency of a disease change over time? And what are the historical factors that appear to correlate those changes? So we have short-term trends, like disease outbreaks, so we're still watching, hopefully, the tail of COVID-19 continue to go down. We do know that there's an increase in the variant of the Omicron strain that we're starting to see now. There's good news is it doesn't seem to be more aggressive or more infectious than Omicron, but we are starting to see a little uptake in diseases again, and those are short-term trends. But then there are secular long-term trends. So an example of long-term trends might be deaths of despair, kind of suicides and substance abuse-related deaths that we know are related to things like social isolation and depression and kind of a loss of belonging and connectivity. So we're seeing those increase right now, which are impacting life expectancies in the country, and that's this kind of a more secular long-term trend. And then we can have cyclical variations, like flu season, which comes every year, goes up and comes down. In Colorado, we're starting to see an increase in the presence of West Nile virus in mosquito populations, and we expect that's going to give us an increase in West Nile cases in humans later this fall. When you start talking about time, it's a good time to talk about what the cohort effect is. The cohort effect is when age and time interact to produce this effect, which is a point in time cross-sectional observation that reflects variation in disease rates based on the year of birth, and then the variation in disease rate within each cohort by age. There's a time to think about cohort effect. So most diseases tend to increase in terms of mortality or incidence as we age. Cancer is a great example. Heart disease is another. Whenever you see an unexpected decline in older age groups, you should start asking yourself could it be a cohort effect? So here's an example where we can look at lung cancer mortality and age. And as I said, we actually expect lung cancer mortality and rates, because of the nature of cancer in general, that these would continue to increase as age increase. This is an actual curve, and it is caused and known to be caused and observed because of the cohort effect. So if you look at this, we have different ages now. The age is across the bottom, and each age is associated with an age cohort. So the people who are age 90 in this example were born in 1910. The 80-year-olds born in 1920, the 70-year-olds 1930, and then the 60-year-olds in 1940. And these lung cancer rates, you see how they all increase with age, but they reach different heights. And this is the impact of smoking. So where smoking was not very prevalent and almost not seen at all in women in the 1910s, it steadily increased due to advertising and increasing social acceptance of smoking. And then it peaked during the World War, Second World War. Cigarettes were actually distributed to soldiers. It was a very effective combat tool or drug. You could use and smoke a cigarette in a short period of time. If you were nervous or agitated, it could calm you down. If you were tired, it could stimulate you and get you active again. So it was like the perfect drug in the Second World War. And it wasn't until the 1950s that we started associating and made the connection definitively between cigarette smoking and lung cancer, and we started to see the rates drop off. So that's a cohort effect, and that's how it occurs and what it looks like. We're going to move into a new topic now, which is going to be measures of excess risk. So we have a need to identify individuals at increased risk for disease, and it pervades all aspects of clinical medicine. We start asking ourselves, like, who is at risk for disease and who should be target for primary and secondary screen, secondary procedures associated in the prevention world? It can also help us talk about diagnosis. So given the characteristics of, and therefore, constellation of risks for a given individual presenting with a certain symptom complex, what is the most likely diagnosis? So if I was talking or describing a 57-year-old man in the emergency department, known smoker, hypertensive, high cholesterol, who comes in saying, I feel pressure in my chest, short of breath, and my arms and fingers are tingling, you would most likely come up with the diagnosis or the expectation that you're looking at a man with acute coronary syndrome, a patient. On the other hand, if a 20-year-old man or woman came in to the emergency department, very agitated, complaining of chest pressure, shortness of breath, and tingling of their hands and fingers, you might more likely say, I think this is hyperventilation syndrome and an anxiety attack. So knowing that the risks associated with heart disease versus the characteristics of some people unlikely to have heart disease can kind of lead you into diagnosis. Management is important. So once the patient is known to have a given condition, for what is he or she at further risk for? So knowing that you have one thing that I know increases your risk for something else, what should I look for? So ulcerative colitis, I'm worried about colon cancer, so you have one condition and that puts you at a higher risk. Also, what characteristics put an individual or an adverse reaction to potential therapeutic interventions? So you might look at CYP450 analyses, which is a genetic test that might tell you someone who could be a fast or a slow metabolizer of warfarin, and then you might want to adjust your dose of warfarin for anticoagulation depending on their metabolism rate as projected by their genetic testing. It ends up that we can do computation of all the measures of excess risk looking at a basic two-by-two table, where on one side is the risk factor, either present or absence, and on the other axis is disease, present or absent. So we're going to use this ABCD two-by-two table in our computations for excess risk. And we're going to start with the relative risk and odds ratio. The relative risk is also called the risk ratio or rate ratio, and it's the ratio of the incidence of a condition in a group of individuals with a specific characteristic, which we often call a risk factor, to the incidence of the group of individuals without that risk factor. Incidence in formula form, incidence in the exposed, over incidence on the unexposed. And if you can refer back to the two-by-two table, it's going to be A over A plus B, which is the ones with the disease and everyone who's exposed, divided by C. Those are the ones with the disease and the unexposed over all the unexposed. So that's the calculation for relative risk. The odds ratio is something that can estimate the relative risk, and we use the odds ratio very often in case-control studies. In fact, it is the metric that we can use in case-control studies. We'll talk about case-control studies, but briefly, these are individuals with the disease compared to individuals without the disease, and we look at the presence or absence of a risk factor. The other thing I will tell you is an odds ratio is what is calculated by the modeling technique called logistic regression. So regardless of study design, you can still use logistic regression, and it's going to create odds ratios. So what is odds? So we're going to go back a little and just talk about what an odds is. It's a transformation of the probability, such that odds is a probability over 1 minus the probability. And as silly as it seems, or as simple as it seems, I give you the back calculation as well, because if you are ever given an odds, you can also calculate back to the probability, which is 1, odds over 1 plus odds. So you think about odds like a coin flip, the probability of any one face coming up is 0.5 divided by 1 minus 0.5, where the odds is 1. We often say 1 to 1. If you'll think about rolling a die, a single die, then the odds of any one face coming up is 1, I'm sorry, is 1 out of 6 divided by 1 plus 1 out of 6. And so you can get from probability to odds and odds to probability. So the probability would be 1 divided by 6. Note that in the computation of a relative risk, so we're going to talk about why the odds ratio approximates the relative risk. When you're computing the relative risk, if the disease is rare, then A, which is the number of people with the disease, is going to be small compared to B, the number of people without the disease, because we just said it was rare. Similarly, C will be small compared to D. And so if we say, well, if A is small compared to B, then I can approximate A plus B with just B. And I can approximate C plus D as just D. And so we divide A over B by C over D, which collapses to AD over BC, where we call this the cross product of the 2 by 2 table. And that's the odds ratio. And this is why it approximates the relative risk. So let's talk about other measures of excess risk. So I love the risk ratio. It's easy to interpret—let me go back just for a minute—risk ratios are easy to talk about. They come out as numbers like 2, which is a twofold increased risk. You can have a relative risk of 1.2, which is a 20% increased risk. And the way we think is particularly suitable to those kind of comparisons. And so the relative risk is most very commonly used, very easy to interpret. And we use it all the time in talking to the general public, to reporters, and reporting it, honestly, in epidemiology magazines, right? But the attributable risk has more information. It's also called the risk difference or rate difference. And it's the difference between the incidence of those with the disease and those with the risk factor versus those without. Now it accounts for the baseline incidence of disease and gives the absolute amount of excess risk that an individual has due to the risk factor. It does require prospective study. You can't get it from a case control study. And you need a prospective study to produce incidence rates. And it's honestly more difficult to interpret. So now if my incidence in the exposed is 5 per 1,000 and my incidence in the unexposed is 4 per 1,000, I end up in a 1 per 1,000 attributable risk. And honestly, those of us with 10 fingers don't do well with thousands. It's hard to conceive of 1,000. We don't automatically think in thousands where we do in terms of tens. So it ends up being a harder to interpret term. On the other hand, it includes that basic risk. So if I was going to say that, you know, if you get hepatitis B, you have about an eightfold increased risk of getting liver cancer. That eightfold relative risk, it's really high. Get your attention. Send you out to get your hepatitis B series right away. If I pitched it to you differently, though, and said, you know, the underlying risk of liver cancer is 1 in 2 million. So now your risk reduction brings you down to 1 in 250,000, which is still, I mean, that's the excess risk. That's the eightfold increased risk if the underlying risk is 1 in 2 million. 1 in 250,000 is still a really low risk. And so this issue about knowing the denominator and having more information is something you all should keep in mind when you start using relative risk as your major measure of excess risk. There is a way to turn the attributable risk into a easier to interpret number, and it's called the number needed to treat. When you calculate, you can use it to say the number needed to screen, the number needed to treat, or the number needed to harm, just depending on what number you're looking at. You get the NNT by dividing the attributable risk into one, and you end up saying you'd have to treat the number needed to treat people to gain one additional outcome. And so that is a more interpretable way of using the attributable risk in talking about excess risk. It may take a number like 1 in 1,000, and depending on the disease, you divide 1 in 1,000 to 1, and now you get a much lower number of people that you'd need to treat to see the outcome. All right, I want to move on to other measures of excess risk. The attributable risk percent is also called the attributable rate percent, the attributable proportion, or the attributable fraction. It's the proportion of disease among those with the risk factor that is due to the risk factor. It tells you how much disease in the exposed group is due to the exposure. It's calculated with this formula, incidence in the exposed minus incidence in the unexposed divided by the incidence in the exposed multiplied by 100% if you're doing the percent rather than fraction. And here's the A and B table identities as well. So we use attributable risk percent in phrases like 90% of lung, 90, I think it's like 95% of lung cancer in smokers comes from smoking. So that means if you have a smoker with you in front of you with lung cancer, it's very certain that that lung cancer came from smoking and not from other potential causes of lung cancer. The population attributable risk is the rate of disease in the population that's due to the exposure, and it's just a subtraction of the total incidence minus the incidence in the unexposed, and then it again gives you a rate of disease that's now associated with the exposure. More useful, I believe, is the population attributable risk percent. This is also called the population attributable fraction, and it's the proportion of cases of disease in a population, the entire population, due to a given risk factor. It's useful because it's the amount of disease that would be prevented if the risk factor could be eliminated from the population. And we hear numbers like 30% of all cancers could be eliminated if we could eliminate tobacco products from the US population. Here's its calculation, total incidence, subtracting out the incidence in the unexposed over the total incidence, and that gives you the population attributable risk percent. Here is a formula that I say all card-carrying epidemiologists know. It can be calculated from case-control studies using the odds ratio. So in the odds ratio in case-control studies, you have an A, B, C, D in your cell sizes, but if you did one-to-one matching in your case-control settings, you have actually manipulated the underlying prevalence of disease. So you can still get there by taking the odds ratio, subtracting one, and then doing this calculation. So you can still use case-control data to get to this very important policy-relevant number. Well we've kind of gone through the terms of ART and kind of what we talk about in terms of basic epidemiology. So I want to change gears and move on to another domain that's important in our work, which is study design. Really talking about those studies that provide us with the numbers that we use in epidemiology, in public health, and in basic clinical care. So I'm going to start out with talking about bias, and it's interesting when I talk about bias, the first sentence has nothing to do with bias. It says, the goal of science is to be accurate in the discovery, description, and measurement of the truth. This is modified a little from a quote by Michael Rothman, a famous biostatistician, whose book many of you probably use as your biostats textbook. So if that's what the goal of science is, bias is a systematic deviation of study measurement, results, or inferences away from the truth. And then the internal validity of a study is related to the minimization of bias, so that the study result that you find can most confidently be assigned to the factors under study. What are the types of bias that we need to worry about? So I gave this lecture for years, and I just said there's only two. There's information or measurement bias, and there's selection bias. Cochrane is an international collaboration that looks at randomized control trials and have now started looking at other study designs, and they break out these two simple concepts into more specific types of bias. Selection, detection, observation, recall, response, publication, regression to the mean, Hawthorne effect, and treatment selection bias. We're not going to talk about these in the specifics, but recognize that there are other ways of categorizing the two major types of bias. I learned this from a coaching colleague of mine, the CBCs of research evaluation. Whenever you read a paper, you should ask yourself these three questions. Could the findings be due to chance or random error? Now most of the time, this is answered for us, and it's answered for us often in peer review, where the reviewers are looking at things like p-values, and alpha levels, and power, and beta levels. So they're actually doing this for you prior to when they accept and publish the paper. And I'm not saying you should glance over it, because making sure that you're confident that the results aren't due to chance is really important. But then the other two aren't always covered by the researcher, and definitely not always covered by the numbers themselves. Could the findings be due to bias, and could the findings be due to confounding? We're going to spend a lot of time on confounding later. And talk a little bit more just about bias now in terms of study designs. So most epidemiology or biostats textbooks will have some version of what I'm presenting here, which is kind of an overview diagram of research designs. I think about research designs in two major categories. There's a third one that I didn't put here, so maybe I should just bring that up. There's also basic science designs. Basic science is more concerned with like structure, and function, and mechanism. So these are kind of the overview diagrams of more clinically applied research designs. On one side is descriptive, and on the other side is analytic. Descriptive studies are also called hypothesis-generating studies, and they describe something like a case report, or a case series, or how something varies by time and place, like descriptive epidemiology. So many states still publish an annual vital statistics report, which is an example of a descriptive epidemiologic study. So that's on that side. The other side is analytic or hypothesis testing. We're going to spend most of our time here talking about these different designs. We're going to start with observational studies called non-experimental, and you see next slide, and then we'll talk later about intervention studies. And here we're going to talk about randomized controlled trials, also called true experiments, clinical trials, pragmatic trials, and then we're going to cover some of the quasi-experiments. Natural experiments, group randomized trial, quasi-experiments, and regression discontinuity. But you see this next slide. So we can't always do an intervention study. So we've come up with clever ways of trying to get to the same answers that a clinical experiment could get to by using these other study designs. So we have before, after studies, or pre-test, post-test. Correlational studies, also called ecologic studies. Cross-sectional studies called prevalence survey studies. And then, so these, I call these the minor observational studies. And then the major observational studies, case control and cohort studies. TROHOC was coined by a rival college of the college that created the case control study, and they jokingly called it the TROHOC study, which is cohorts spelled backwards. Often you'll see these called retrospective studies. I tried to put in all of the synonyms like case-referent, case-compare, causal-comparative. I think the two most common are case-control and retrospective studies. Then cohort studies are also called follow-up studies, longitudinal studies, incident studies, or prospective studies. And I usually just say cohort studies. And then we have two flavors of cohort studies, one prospective and one retrospective. And then you see their synonyms, concurrent or futuristic cohort studies, or historical or retrospective, prospective cohort studies. So I am in a school, and I came from a school, and I changed the school I'm at now, School of Public Health at University of Colorado, from, sorry, we were originally a retrospective-prospective study school. And it drove me crazy because of this one down here, retrospective-prospective study. That just, you know, made me twitch when I heard it. And so I like better case-control because it's very descriptive and cohort. And then when I say cohort, I can talk about retrospective and prospective cohort studies. So we're going to cover all of these going forward. There is a hierarchy. I tried to outline that with the order in which I put the studies. We start with descriptive studies at the bottom, but then we start to go up in terms of analytic ability to more confidently assign the outcome to the factors under study. So descriptive studies are at the bottom, observational studies are next, and experimental studies have the opportunity to be the most robust. When you talk about study designs, I have to include things we're not going to talk much about, which are called summary or extrapolation studies. Meta-analyses are studies that combine different studies to come up with what I would say is a summary or an average effect size. They become more robust, more important in causation considerations over time because a meta-analysis of several good clinical trials is felt to be superior to a single RCT. Decision analysis takes data from what's known and extrapolates it to what's not known. And so that's just another way of doing modeling that extrapolates information to help make decisions. We're not going to talk about decision analysis either. If you look at descriptive studies, they usually don't have a hypothesis in advance and are satisfied with establishing what we would call non-causal associations. So, you know, the colon cancer rate is higher in El Paso County, which is a county south of Denver County, than it is in Denver County. So, I don't know why, but I can say there's a higher risk associated with living in that other county. Descriptive studies can include case reports and case series. Recognize the New England Medical Journal, that rag of the medical world, has a case report study in every issue, and it's seen as a way to teach around the bedside or teach around the specific case. Recognize that case reports are ends of one. They have useful information for education, and they become less useful for rolling up into making decisions about clinical care based on more than a single person. A case series is just a group of case reports. Recognize that a case series has no denominator, and so it's just a case report with more cases. So, it's very difficult to make decisions based on those two study designs. And then, finally, we have descriptive reports that we talked a little bit about already. Vital statistics reports, hospital discharge data, physician pharmacy profiles are all examples, and we do use these to make decisions. So, vital statistics reports, like death rates, could lead state legislators to say we want to put more money into opioid overdose prevention, or we need to pay more attention to the nutrition of low-income pregnant women. So, we do make decisions based on those. Physician pharmacy profiles really are used even today to think about how to better pay or rate physicians going forward. So, descriptive studies have a real role in decision making, even though we don't often identify the causal association that underlies it. Analytic studies, on the other hand, are going to have the hypothesis specified in advance, and they are usually intended to establish a causal association. And you remember from the outline, we're going to talk specifically a little bit more about causal association later in this session. So, as we start to delve into study design, I wanted to just give a high-level discussion of research study structure. And at the highest level, it's really very simple. There's variation in an exposure, which could be a drug, an environmental exposure, a health habit, a heritable gene. So, there's variation in that exposure that we believe or that we are concerned about it being associated, usually causally, with the variation in an outcome, such as presence or development of disease, morbidity, mortality, quality of life, healthcare utilization, other outcomes you might be interested in. And the simplest format for looking at research structure is, again, the two-by-two table. So, here's that really high-level approach, where you have exposure on one axis, yes or no, and the outcome on the other, simply bad or good. The designs we're going to talk about vary primarily on how cell subjects are obtained. How do you get into the cell that you're in? So, here are the observational studies, before, after, ecologic, and cross-sectional. I call the lesser studies. Then we'll talk about case control, and then we'll talk about cohort and both flavors of cohort studies. So, before-after studies, outcomes for an individual or a population are compared before and after a known exposure or event. So, you had high cholesterol, I gave you garlic tablets, and I measure again, and your cholesterol is lower. That's a before-after individual-level study design. You can do before-after on a population basis. Say, Colorado had no light rail system, and we had a certain level of reported individual exercise and obesity rates. Then we put in a light rail and said, what happened to those measures after that exposure happened? It required little resources. Clearly, light rail takes a lot of resources, but notice that the investigator didn't make that decision. Someone else did that. It happened naturally or by some other process. The garlic tablet doesn't require assigning a blinded control group, developing placebos, and a lot of other things. So, the resources are less. However, you always are uncertain what would have happened without the intervention. So, this issue about what is the trend of cholesterol over time. If I just tell you you had high cholesterol, would you change your diet? You looked up and did more than just take the garlic tablets. So, you just don't always know what would have happened, and that lack of a control group is the Achilles heel of before-after studies. What about ecologic studies? So, here rates of exposure and outcomes for different populations are compared. Probably one of the most famous correlational studies looked at per capita fat intake by country, and then colon cancer mortality rates by country. So, when you looked at those, if you think about the upper left-hand part of the table where there's high colon cancer rates and high fat intake, you had the U.S. And then on the other end, down near the axis, the 00 axis, you had Japan with low colorectal cancer rates and low per capita fat intake. So, the conclusion was how much fat you eat increases your risk of colon cancer. Now, the problem there is we don't actually know that the people eating all the fat are the ones that are getting the colon cancer. So, there's assumptions that are made that may be false, and when they are false, that's an ecologic fallacy. So, one example that's a real-life example is we could look at the use of bicycle helmets and head injuries. And so, I could take Kansas and Colorado, and I could do a survey and say, what is the per capita use of bicycle helmets in Kansas versus Colorado? And then, what is the rate of head injury in Kansas versus Colorado? And when you do that, it looks like bike helmets cause head injuries. However, the people in Colorado—Colorado is a mountainous state—people do crazy things on bicycles, like mountain biking down ski trails that are rocky and sheer and have an element of risk and danger. If you do that without wearing a helmet, you're going to have a much higher risk of a serious head injury. And because more people are there doing more risky behaviors on bicycles, we have a higher risk of overall head injuries for bicycle riders, but it's the riders without the helmets who are getting the injuries. Where in Kansas, pretty flat, lower use of bicycle helmets, but lower risk bicycle trails and bicycle riding. So, those are examples of the inherent Achilles heel of correlational studies and the ecologic fallacy. Finally, there's the cross-sectional study. Individuals and exposures and outcomes are determined at the same point in time for a population. And to really be a cross-sectional study, you need to go into it not knowing the disease status of the people you're asking or you're looking at. So, you say, how many people drink Diet Coke? So, you might do a telephone survey, random digit dialing, and say, do you drink Diet Coke? And number two, do you have heart disease? So, you're doing exposure and the outcome at the same point in time. Now, there's one nice thing is that you get a prevalence of both the outcomes and exposures, but it's very statistically inefficient and you can't establish the temporal relationship between exposure and outcome. So, which came first? And because you lose that temporality, it makes cross-sectional studies not as robust. So, we're going to move on to the observational studies that have more validity, less bias, and provide more robust comparisons and information. So, in a case control study, we take subjects with an outcome and we compare them to those without the outcome and then compare their prior exposure history. What that yields is an increased risk of having an exposure based on the outcome. So, for example, if we do case control studies of smoking and lung cancer, we ask, do you have lung cancer? We ask people who had lung cancer, did you smoke? People who did not have lung cancer, did you smoke? And we find that people with lung cancer have a much higher risk of having the exposure of cigarette smoking. And then our biostatistician colleagues tell us it's an exact corollary that having an increased risk of exposure based on outcome is the same as having an increased risk of outcome based on exposure. So, the other example I gave here is that men with and without prostate cancer are compared to see if they had had a vasectomy. You'd say, well, where would the bias be in that? Well, you want to kind of think through it a little bit. Who does most of the vasectomies in the US? They are urologists. And what else do urologists do? They look hard for prostate cancer. And so, there's a little bit of a diagnostic bias in patients that have established relationship with the urologist that could lead to the finding or the association of a vasectomy with prostate cancer. That's the source of bias in case control studies. Here's a diagram of how case control studies work. We're going to start here today with saying, do you have the disease or do you not have the disease? Then we're going to look into the past and say, did you have the exposure or did you not have the exposure? And the ACBD just tells you where those individuals go in the overall two-by-two table. So, you can fill out your two-by-two table and you can do your calculations of excess risk. There are specific situations where case control studies are favored and in fact are likely to be the best study design. Now, that doesn't mean you can't use case control studies in other settings. It's just this is where you may want to use case control because they're ideal. The first situation is where the disease under study represents a rare outcome event. And sometimes this is the only way to study diseases. So, for example, we know, or most of you would know, that we don't give children with fevers aspirin. And we don't give that to them because of a worry of Reye's syndrome. Reye's syndrome is a still poorly understood condition which can be fatal where a child with usually chickenpox or influenza are the most prominent causative viral infections are given salicylic acid or a salicylate-type compound and they develop Reye's syndrome, which is threatening. Now, when Reye's syndrome was first detected, I'll admit I'm old enough that I was a medical student at the time. The studies that linked it with aspirin use were only cohorts, I'm sorry, case control studies because it was so rare, it was the only way to study it. And to this day, all of our recommendations about not using aspirin use in children are based just on case control studies. The same thing is true of the Reye tampon and toxic shock syndrome. For years, it was the only way that we linked up estrogen use with endometrial cancer until we finally had a long enough cohort study to find the same outcome. So it may be the only way to look at a rare outcome event. It's also useful if you wanna look at multiple potential risk factors for a single outcome, and that's related to the next bullet point. We don't know much about the disease, but we have some suspicions and we want hypothesis-generating studies. To kind of look at potential risk factors. So when you have a new disease, case control can help identify multiple potential risk factors to then lead into hypothesis-generating studies. The next bullet point is just pragmatic. If it's expensive to diagnose or detect the outcome in study individuals, notice that if you recruit people because they have the disease, you already have the outcome detected. So that becomes a pragmatic approach. And then there's this issue about long, latent periods between exposures and outcome. So, DES, sorry, diethylsebesterone was a hormone given to pregnant women thought to be at increased risk for premature delivery or miscarriage. And the idea was to try to stabilize the pregnancy. Years later, we started seeing a disease called clear cell adenocarcinoma of the vagina, which was exceedingly rare and not seen a lot. And so case control studies linked that cancer, not to the mom, but to the daughters of the mothers who took DES. And so there's this huge long latent period between when the mom took DES and their children, their daughters, got clear cell adenocarcinoma of the vagina. And so only case control studies were able to find that linkage. And finally, again, returning to practical issues, it ends up that while you still have to spend resources and take time, you can do case control studies quicker and with lower expenses than either cohort studies or clinical trials. What are the steps in a case control study? Define your hypothesis. I really suggest people do this ahead of time and really base it not on a fishing expedition, but on what you want to do. And we'll go through these steps. Select your cases, select your controls, ascertain exposure status, and then you also have to look at the status for important potential confounders. Let me just say one more thing about my hypothesis. So there are these things called fishing expeditions and we see them from time to time. They're usually around a rare disease or something that we're trying to figure out what could be the precursors. And so we take something like childhood leukemia and we ask the parents what the children ate. And this actually was a study design used where the parents were asked 180 different food items, analysis was run, and the only food that came out as potentially associated was the hot dog. Now, I'm not going to provide any exculpatory remarks around the nutritional benefits of eating hot dogs. However, if you think about 180 different food sources and you think about using an alpha level of 0.5 or let's say 0.1, you're going to find at least one association by chance alone. And when they did prospective studies looking at hot dog consumption, the mighty tube steak was exonerated and ballparks around the country sighed a long sigh of relief. Still, I'm not advocating eating hot dogs because there's lots of other reasons to not eat them. But that's an example of a fishing expedition. Does that happen today? Yes. The nurse's health study was looking at heart attacks in women, and they asked the women about 80 different nutritional supplements and found that women who took folate seemed less likely to have heart attacks. And where prospective study designs have not borne out a sufficiently strong effect size to recommend folate supplementation for the prevention of heart disease, there are linkages, of course, to folate supplementation and avoiding neural tube defects in infants and fetuses. So I just want to caution you about not doing fishing expeditions. So now we're going to get cases. And when possible, we want to get cases that are, we call them incident cases or newly arising rather than prevalent or existing cases. The reason is if we oversample cases of long duration, we can bias our results. And instead of describing risk factors, we start describing prognostic or survival factors rather than these etiologic factors. And so while it's an extreme example, if you did a case control study looking at the development of type 1 diabetes and insulin as the exposure, you would find a strong association between insulin use and type 1 diabetes. But the insulin use is a prognostic or survival factor, not an etiologic factor. So that's why you want to get these newly existing cases if you can. Sometimes the disease under study is so rare, you have to use prevalent cases to get enough to study, but just recognize the biases you might be introducing. What about selecting where you get your cases from? It's best if they're the cases that arise in a defined population, either all of the cases or a representative number of cases. If you select cases not arising from a representative of defined population, then you got to make sure they're unselected within the source. Select all the cases or select randomly. This is to avoid issues associated with referral bias. So that if you were looking at, for example, the cases of malignant melanoma and your sources of cases was a university hospital, now called the Anschutz Outpatient Pavilion. But at the time it was, when I grew up, it was university hospital. So university hospitals tend to get referred the sickest and most complex cases. And so those cases are not representative and you want to make sure you recognize that and then don't just pick the worst ones or the best ones. They have to be selected all or randomly. Problems in case selection is when you call them a case, but they're not a case. The other, which can happen, just misclassification. Another common problem though is something called heterogeneous outcomes. And heterogeneous outcomes means what you've detected or called a case, they aren't all the same. And a great example is breast cancer. So we often talk about breast cancer as a single disease, but as you delve into it, it's a set of diseases that are cancers of breast tissue. So it can be postmenopausal. It can be premenopausal. They can be estrogen receptor positive or negative. They can be HER2 positive or negative. And these are all different classifications of disease. And so a given risk factor might be a risk factor for some breast cancers, but not all breast cancers. And so if you start combining the heterogeneous outcomes, you might dilute and actually obscure an underlying finding by just including too many other breast cancers not associated with the exposure you're most interested in. All right, we got our cases picked. We know the problems. What about controls? So the rule of thumb that we talk about is you wanna choose control subjects that if they'd gotten the disease under study, they would have shown up in your case group. So that's how you're making sure, or you could make sure that they're from the same underlying population. So if the cases are all cases from a defined population, like all of the colorectal cancer cases from Colorado, then you wanna select controls from the non-disease members from Colorado. I'll just pause and say, I use Colorado examples because that's where I'm from and where I live. And I can usually say it and picture it as I'm talking. If cases are not from that defined population, then select controls from individuals receiving care from the same source. So back to the malignant melanoma in University Hospital, I would like to go to controls who got care from University Hospital. You can also talk about neighbors or friends or family members. Recognize that you might be getting to something called over-controlling where the behaviors or the risk factors for neighbors, friends, or family members are so like the cases that you can't find a difference. You can't find an association with the risk factors. And then finally, you can select persons who underwent the same case-finding procedure as the cases, but were found to be disease-free. So you might wanna say, well, I'm gonna look at risk factors for ampulla of otter cancers. So I'm gonna take as my cases people who were scoped and had cancers in the ampulla of otter. And as my controls, take all those other people I scoped that didn't happen. The only issue is you have to be very specific about the disease and be careful because we don't do endoscopes on people for no reason. So they got the scope for some reason. And so that could start obscuring other potential risk factors. So for example, let's say that you thought maybe use of coffee drinkers as a control actually did happen with pancreatic cancer. Coffee drinkers were more likely to have, or sorry, people with pancreatic cancer were more likely to be coffee drinkers in a case control study. But what they found is that people who drink coffee have more sour stomach or abdominal complaints and were more likely to be scoped. And so it kind of perturbed the relationship between coffee drinkers and pancreatic cancer. So remember people don't get diagnostic procedures for no reason. Matching controls is another alternative to controlling for confounding factors. And we do matching in the design phase rather than the analysis phase, which we do by adjustment. Here we establish criteria for the selection of controls, which prevents certain extraneous factors from being considered. So most often you might see matching done for age and sex. And the idea is then I don't have to worry about a factor like sex showing up differently in my cases and controls because for every female case, I have a female control. For every old case, I have an old control. The major disadvantage is once you match, you lose the ability to evaluate the relationship between the match variable and the outcome. So if you match on sex, you can no longer talk about the association between sex and the outcome. That's why I'm always a proponent of doing it in the analysis part of the study unless there's really compelling economic reasons to match. So now I have my cases and controls. I wanna look at exposures. So it's almost best if you can to look at existing data sources. So these are sources that like automated medical records or any medical records that actually talked about the exposure so you didn't have to ask the subject, which is the second way we get exposures is to ask subjects through interviews and questionnaires. If a disease is rapidly fatal, you might have to use proxy respondents such as next of kin or household members. But recognize this can be very problematic around some exposures, especially those related to things like previous sexual activity or relationships. Finally, preexisting records are often really nice because vital statistics, laboratory results and medical records often don't know that the person is going to disease to get the disease under study. Just a few comments on exposure ascertainment. You wanna have comparable ascertainment between cases and controls. That is you don't want to look harder in the cases for the exposure for then you do in the controls. An example, a real life example was a study looking at a cigarette smoke and cancer use. The cancer cases came from the cancer ward. The controls came from the orthopedic ward. And one day the PI, the principal investigator followed the study assistant around to watch the interviews. And the assistant went into the ortho ward and would ask a patient, do you smoke cigarettes? And the person would say, no. So they marked no and went on to the next interview. And then in the cancer ward, the assistant would go up to a patient and say, do you smoke cigarettes? And the patient might say no. And the assistant followed up and said, you mean you've never smoked cigarettes? Not even one? So that's called differential exposure ascertainment. And it introduces bias into the study. So watch out for that. Response rates need to be high and similar for cases and controls. So you don't want either your case group or your control group to have a low response rate because it could start to wash out any effect size that you find. And then recognize that there are confounding factors as well, and you want to assess confounding factors. That's how you decrease the impact of confounding on your study results. And when you do that, you have to use the same quality approach to ascertainment of the confounding factors. When we talk about analysis of case control studies, there it's done as we talked about before by estimating the relative risk with the odds ratio and recognizing that for rare outcomes, when the prevalence is less than 10%, the odds ratio will be very close to the relative risk that would have been obtained from a similar cohort study. And I'll just tell you that 10% is actually a pretty good bar to use because as people have done mathematical modeling, that's where you get above 10%, the odds ratio starts to overestimate the underlying risk ratio in ways that might be significant. So as we did before, we want to talk about the sources of bias in case control studies. There's selection bias. Most problematic, sorry, one would be the representativeness of the case group, but maybe most problematic is appropriateness of the control group, especially if the study is not population-based. We'll talk more about that. And then the same called detection bias or unmasking bias when the identification of cases varies with the exposure status. So that's kind of the prostate cancer issue where the identification of patients with prostate cancer is associated with going to the provider who does a vasectomy. And so that's kind of an unmasking bias, detection bias issue. So let me talk about the selection of hospital controls. I was interested in looking at our directions for our lectures. They said, don't use any references that are older than, I can't remember what it is, 10 years or 20 years. So when you get to that part of the analysis study, Dr. Kalanj quoted both a 1960 study and a 1983 study. And I did these studies because they're classic and they exhibit the point so well that I returned to them year after year. So here's a study that looked at hospital versus population controls in evaluating the association between artificial sweeteners and bladder cancer. There was an artificial sweetener at the time called cyclamate, very popular. We like artificial sweeteners because we somehow feel they reduce our risk of obesity and they may be helpful in diabetic patients. They probably don't have the impact on obesity. We would like them to, but they provide some psychological comfort. However, there was one that was associated with bladder cancer. And so someone decided bladder cancer is rare, let's do a case control study. So they started out and they say, well, we're at this hospital, we'll take all the bladder cancer cases as our controls and then everyone else, sorry, as our cases and then everyone else is our hospital controls. And when they ran the study, it got relative risks of 0.8 to 0.9. That was the confidence interval. And you look at those and you say, it's under one, it's an odds ratio. That means the people using the sweeteners actually had a 10 to 20% lower risk of bladder cancer. Well, that's not what they wanted to find. So they did what any good researcher would do. They said, let's pick a different control group. So I'm being a little flippant, but they did. Look for another control group. So they went to the general community surrounding the hospital, asked them about artificial sweetener use, used the same case group and got odds ratios of 1.1 to 1.2, which is a 10 to 20% increased risk. So my question to you is, can you think why we saw that difference? Well, you have to go back to think about who uses artificial sweeteners. So we know that two of the biggest drivers of hospitalizations are diabetes and being overweight. Being overweight leads to heart disease, it's associated with diabetes, it's associated with knee and hip degeneration, therefore orthopedic procedures. Diabetes has an incredible number of downside complications that require hospitalizations. So the hospital population is not totally reflective of the population that gives rise to the hospitalizations. And we know that overweight people and people with diabetes use more artificial sweeteners than the average population. So it ended up that the hospital controls were more likely to use sweeteners than the community controls, and so much so that it completely reversed the splatter cancer risk associated with the sweetener use. So that is the issue around selection bias and the selection of controls. And while, why good case control studies today try to use a number of different control groups to kind of balance out selection bias. There are also sources of information bias in case control studies that can be in misclassification. We talked about heterogeneous outcomes. So misclassification bias is that you thought you were including only one disease entity, but because the disease entity is a mixture of diseases, their heterogeneous outcomes, some associated with these exposure and some not. Then you can have differential reporting of exposure data, and this is where recall bias comes in. So recall bias has to do with people remembering their exposures better once they've been diagnosed with the disease. If any of you have been misfortunate enough to have a friend or a family member with cancer, you will have experienced this kind of recall. We have this feeling that bad things shouldn't happen to good people. So I think of myself as a good person, bad things happen to bad people. So if something bad happens to me, there must be a cause. And people will comb their past looking for what might have caused the cancer that they now have. Did I live too close to high power, high tension power lines? Was I drinking water contaminated with PFOS? When I took organic chemistry in college, did I spend too much time with carbon tetrachloride? So just look back and comb the past to say this is what caused it. That's recall bias. And that differential reporting is a key issue about why survey-dependent case control studies have a particular problem with information bias. The other big source of potential bias is confounding, or what we would call residual confounding. So these are confounding variables that weren't anticipated, were unknown, and weren't measured. The only thing I need to say is in case control studies, most of the time confounders are risk factors for the disease. But in a case control study, if the selection probability is different for cases and controls based on a third factor, it can introduce confounding. So I wanted to give some examples of misclassification and effects on heterogeneous outcomes. So this is talking about thrombotic stroke and oral contraceptive use. So I'm going to give an example where I'm going to say the underlying truth is that you have 200 stroke patients and 200 patients without controls. And half of patients with thrombotic stroke and 10% of those without stroke use oral contraceptives. So that maps out to a 2 by 2 table that looks like this, 100 of each oral contraceptive users in the case group, and 20 versus 180 in the control group. And when you do the odds ratio, you get an odds ratio of 9. So what if we perturb this with heterogeneous outcomes? Let's say when the study was conducted, 20 cases of non-thrombotic stroke, that is hemorrhagic stroke, who had oral contraceptive use the same as controls, 10%, were included as cases. And you could actually see this happening. I mean, before the advent of imaging, it was hard to diagnose between non-thrombotic and thrombotic stroke. And I will tell you today, even with imaging, you still make errors from time to time. So this is something that could happen. So remember I said these 20 cases had the same OC use because the OC use was not associated with non-thrombotic stroke. So I would take two people from the control group and put them over in the case group. I would take 18 people from the control group and put those in the non-OC case group, and I'm going to dilute that odds ratio by the inclusion of non-related causes. So that's the bias associated with heterogeneous outcomes. What about misclassification? So what if there are 20 cases of thrombotic stroke that were undetected? What if the neurologic defect was so small and the patient's ability to overcome it was it just never got diagnosed? This is another thing that happens from time to time. But now these thrombotic stroke patients had the same OC use as the detected cases. They were just misclassified. So now I'm taking 10 cases from each of the OC groups and adding them to the control groups, and here again you see bias towards the null hypothesis. Misclassification is different than heterogeneous outcomes. Heterogeneous outcomes will always drive—sorry, the inclusion, heterogeneous outcomes not related to the exposure—will always drive the odds ratio towards the null. But misclassification works differently, and so it depends on who gets added to what cell. And you can actually do this on your own by setting up the two-by-two table and just saying, what happens if I take people from B and put them into A, and then do your AB times BC, and you can generate this table. But for those of you who would like it spelled out, this is what that exercise would do, that if you misclassify exposed cases as control, you're going to underestimate. But if you misclassify exposed controls as cases, you will overestimate, or actually the better way to say is drive the odds ratio farther away from the null. There are things that inhibit us finding associations in case control studies. If there's one more than one causal pathway, you can have cases that don't have the exposure. You can have that pesky person who smokes but doesn't get lung cancer because there are other… I'm sorry, I said you can have those people who have lung cancer but don't smoke because you can get there by radon. Or there may be other factors in the causal pathway that are absent, so non-cases can have the exposure. Sometimes there's insufficient variation in the exposure. So if you're looking at cancer rates in returning soldiers from the Second World War, you might have a hard time finding an association with at least heart disease, if not lung cancer, because so many people smoked. And then in these multifactorial diseases, there can be too much founding from other factors. So we're going to leave cohort studies in the past and move on with—I'm sorry, case control in the past—and move on with cohort studies. In cohort studies, subjects with and without the exposure are followed, and their outcomes are compared. Exposed and unexposed subjects can come from the same group, geographically and temporally, or from different groups, and it can be done prospectively or retrospectively. In the latter, you have to be able to assemble the study group based on the exposure status, independent of the outcome status. Diagrammatically, it looks a little like this. So here's today, where I'm looking at exposed versus non-exposed people. And I then follow them forward into the future and measure the disease status. So in this case, where I go from today to the future, that's a prospective study. And if I go from today to look at the past, it's retrospective. As I'm looking at the slide, I'm sorry, these arrows should be moved up so that the arrow moving this direction goes from today to the future, and this arrow goes to the past. I want to make a very important observation on this slide. You can always come up with the right study design, common question, in board exams by saying, how was the study group assembled? If the study groups are assembled on the basis of their outcome, it has to be a case control study. You're starting over here and looking backwards to exposure status. If the study groups are assembled by their exposure status, it has to be a cohort study, because you're starting over here and moving forward. Your question should be, or might be, what about this pesky retrospective one, where I'm starting out today and I'm looking forward? The key is in a retrospective cohort study, you are still assembling your study group based on who's exposed and who's not exposed. You're just measuring it in the past, and then you're coming forward and measuring the outcomes today. Cohort studies are favored when the risk factor is a rare event. So for example, thankfully, Hiroshima, Nagasaki, Athremo Island, Chernobyl, all represent rare massive radiation exposures, but they did present us with the opportunity to look at the multiple potential outcomes of those single exposures. In fact, most of what we take for radiology and radiation exposure risk today comes from extrapolating backwards from Hiroshima and Nagasaki. You have to do cohort study if you want incidence rates, because remember in case control studies, if you do half cases and half controls, then you have set the incidence rate at 50%, and then you must use cohort studies where limitations like ethics, it's not ethical to make people smoke cigarettes, make other designs unfeasible. Again the steps in the cohort study, define your hypothesis, select your study populations, include subjects not at risk, we'll talk about that, ascertain exposure, including confounders, and monitor for and ascertain outcomes. Your study population can be a group with some commonality, either geographic or temporal. So you're a group with a special exposure. So for example, you're listening to a four-hour lecture on epidemiology. In past years, I mean by prior COVID, we did these sessions all in person. We held them in a central location, and students traveled for and stayed in the hotel and got pretty much the same content. I say pretty much the same content, because this is clearly less interactive. And I like to think I'm better in person than statically on a screen, but only people who've seen both would be able to make an objective decision. However, those are two different special groups. And so which group takes more away from the board review exam? That would be a researchable study with a cohort design, where I'm selecting groups based on that temporal and geographic commonality. Could be a population for which there are special data resources available, or any other available identifiable population. When you're thinking about comparison groups, you should say if not for the presence or absence of the exposure, the groups would look like two random samples from the same universe. The comparison group can be an internal group from the cohort without the exposure, or varying levels of the exposure. And that kind of internal groups is probably one of the most common designs that we see in cohort studies moving forward. Oh, let me just say why. Because if you have an overall cohort with an internal group that is somehow different, because of some different exposure, then there are other factors that might be confounders that are shared by the unexposed group. So let's say, for example, we wanted to look at the impact of this lecture on your, again, test performance. Some of you will drink coffee while you listen to this. Some of you will need to drink coffee while you watch this. Others of you may not be coffee drinkers, or may choose to imbibe something different. And we could take the coffee drinkers as an exposed group internal to that cohort, and then see who tended to get more out of the course on the basis of exposure. Excluding subjects not at risk means you have to get rid of those who already have the disease or can't get the disease in order to prevent significant bias in the results. The first study that looked at estrogen use and endometrial cancer showed that estrogen use protected against endometrial cancer. Any of you who are students of epidemiology know we use estrogen use and endometrial cancer as a common example. And so how could they have found that? Well, who gave postmenopausal estrogen? OBGYNs. What else do OBGYNs do? They do hysterectomies. And in the first study, they didn't exclude patients with hysterectomies. Therefore, the patients who could not get the disease were also included, and they found no relationship. You should exclude folks at recruitment if follow-up information is expensive or difficult to collect. You can do it at analysis if it's easy to get the follow-up data. All right, now I need to ascertain the exposure. So recognize that now you're the researcher. You're not doing case control or you're at the mercy of whoever collected the data that you're using to begin with if you're using secondary data and you can't collect and go back and collect all the information on confounders. Now it's your job to anticipate the confounders and collect that information. You can get that information from subjects, through surveys or examinations. You can get them from available records, or you can do other things like environmental exposures. This group of factory workers were exposed to asbestos, and these weren't. Ascertainment of outcome, you can get these from vital records, so you can actually see did the people die by going to the National Death Registry, supplying two of three pieces of information. You have to have at least two of three, the name, the birth date, Social Security number, any two supplied to the National Death Index plus a certain amount of money will get you whether or not they have a death certificate registered. You can also look at other records like hospital discharge data, medical records or disease registries, or you can just ask your study cohort with follow-up surveys or exams. However, if possible, you'd like the observers not to know the exposure status when they're ascertaining outcomes, again, to keep that observation bias. Keep your observers from looking for the outcome differently when they know the exposure. Now when you get to analysis, excess risk, you have all of the things, all of the measures you have are available to you. You have the relative risk, attributable risk, population attributable risk percent because you have the underlying incidence rates in both the exposed and the unexposed groups. Of course, there are sources of bias. Selection bias can occur in the formulation of the exposure groups. Those choosing to be exposed may be very different than those who don't. There may be, like for example, differences in those who drink coffee to watch these lectures versus those who don't drink coffee. There also may be other factors related to the outcome that determine why one group is exposed and the other wasn't. And those factors are, again, kind of rolled up into bias and a residual confounding. But another source is completeness of follow-up. So that's a major source of potential bias, especially if you lose more of one group than another, like you lose more of the exposed group than the unexposed group. You can actually get to a point where you lose enough to follow up that it invalidates your results. You can have ascertainment bias if determining the outcome doesn't include blinding, the exposure status, and then again, we talked about confounding. Mentioning retrospective cohort studies briefly, this is a study in which the cohort is assembled retrospectively. Exposure data for the cohort are determined retrospectively and the outcome is determined today. If you do this right, it can have the same level of rigor as a prospective cohort study, but you have to be able to assemble a cohort based on some common past experience and on the availability of the necessary exposure data collected without bias on all members of the cohort. So for example, for years, Denver Health had an obstetrics registry where they collected information on all the mothers born at Denver Health. And then they wanted to do a study of OB ultrasound. And so they said, well, we can look back 10 years and not only say whether or not you had an ultrasound, but did you have other obstetrical risk factors and why did you have the ultrasound? And then they went out and tried to find those kids today or when they did the study and then asked whether they were having trouble at school, whether parents had noticed any problems, if they had any health impacts. So that's a real life example of a retrospective cohort. They could be faster and cheaper, but loss to follow up usually is a formidable problem. So in the study I just mentioned, 22% of the original cohort could be found, which means they couldn't find 80 or 78%. And so in essence, even though that study stood for years, as the only study of the safety of obstetrical ultrasound, it was fatally flawed. It had no business presenting the conclusions it had. And I think today it would be unlikely to be published. That's just another problem. Usually have smaller sample sizes. You have a bigger chance of misclassifying the exposure outcome and you may not have exposure status for all the confounders you need to account for. There's a kind of a separate special kind of study called a nested study. I'll mention here at the end of observational studies. Sometimes cohort studies provide the opportunity to do these things called nested case control studies. Once you have enough outcome endpoints accrued, you can then compare disease individuals with those free of disease and the exposure status can be determined retrospectively. So this was done in the Framingham cohort when they were wondering about the association of serum vitamin A levels and prostate cancer. So they assembled the Framingham cohort just to look at cardiovascular disease. But when they had enough prostate cancer cases, they were able to assemble a case control study where they went back to the frozen serum samples, defrosted them and measured serum vitamin A at the inception of the study and were able to do a nested case control study. Our kind of last area for study design is intervention studies. We'll spend the most time on randomized control trials, the gold standard for study design, talk about why that is. And then we'll talk about pragmatic trials a little bit, natural experiments, randomized trials and then four types of quasi-experimental designs. All of these are kinds of intervention studies. RCTs are essentially the same as a cohort study but now the investigator decides who gets the exposure using random assignment. It's the strongest study design of all because it maximizes internal validity. But notice this caveat, at the expense of external validity. We'll talk a little bit more about that. How does it do this? It maximizes internal validity by promoting the equal distribution of potential confounders into exposed and unexposed groups. So that's underlying secret of the RCT, not secret but a game changer that makes it the gold standard. Steps are a little bit different to find the hypothesis. This time they're really pretty narrow because you don't want a lot of hypotheses because that increases the cost and the sample size. You select your study subjects and do pre-measurement and pre-assessment and informed consent. Then you randomly allocate subjects to intervention groups. You want to blind the subjects when you can and the investigators when you can and then follow them and ascertain all relevant outcomes, monitoring for adverse effects and stopping rules. So let's dive into this. Study subjects acquire informed consent with strict inclusion and exclusion criteria. So inclusion criteria says, what keeps you from even coming in the door? You're only included if you have this set of characteristics. Exclusion criteria is now that you're in the door because you have this other thing I don't want you. So I'm gonna talk a little bit about the Diabetes Prevention Project, which is our CTI participated in, where inclusion criteria was anyone who came in with a blood, sorry, a spot blood glucose level over 120. So that got you in the door, but then you could be excluded for lots of reasons. You couldn't do exercise. You were allergic to the study medications. You couldn't complete the pre-randomization activities that showed you'd be a good candidate. So those are all exclusion criteria. These pre-randomization visits are used to help ensure successful participation, but they have a problem in that they make the study population non-representative. So in the Diabetes Prevention Program, to get into the study, you had to do a finger prick. So that part was easy, but then you had to agree to a three-hour oral glucose tolerance test, where we gave you a 90 milligram load, maybe it's 129, think about it. No, 90 milligram load of the most sickingly sweet fluid a human ever ingests. We do draw blood before we give it to you, and then one, two, and three hours afterwards. So that, you had to sign up for that. And if you showed impaired glucose tolerance test, you then got to move on to a second three-hour oral glucose tolerance test, repeated in the exact same way. If you were twice impaired glucose tolerance by two tests, we then gave you some pills in two bottles. And we said, we need you to take these pills. We counted them before you went. And so we asked you to bring them back in two weeks, and we counted them again to see if you were successful in taking the number of pills you should have taken. You had to do tricks like randomly assign the numbers so they don't just dump them out. Okay, so you had to do that. And then you had to keep a food frequency diary, and you had to do that for two weeks, marking down how often you ate everything every day. And you had to bring that back, and you had to be able to do that. And then you had to be willing to be randomized to placebo, where we said you probably ought to get more exercise and eat less, that was it. Or intensive lifestyle intervention, diet and exercise counseling, and skill building. Or we're going to give you metformin, a drug. Interestingly to me at the time, and it might be different today, everyone wanted intensive lifestyle intervention, but they had to be willing to be in any of the groups. So then I usually pause here if I'm in a group and say, how many people would do this? And it always makes me laugh, because if it's medical students, someone will raise their hand and say, how much do you get paid? But if they're public health people, I usually don't get any hands up. So then I say, so clearly the DPP isn't representative of public health professionals. Or actually it's representative of people willing to jump through all those hoops, which can make the population less representative. Okay, so then you randomly assign them. It's best to do it totally randomly, but you can use block randomization. So if there's important confounders like sex, you can use block randomization to wait until you randomize women and men as separate blocks to assure that you have equal number of men and women in both groups. You can use quasi-random techniques like every other person, every other chart, but you have to look at that as a way that they would not produce any sources of bias. And when you get to that point, you might as well just randomize. Blinding is the next issue. Subjects should be blinded with placebos, for example, to what study group they are in whenever possible to guard against placebo effects and something we call crossover. So I know what group I'm in, I'm gonna go out and get in the other group without telling you. There's something called allocation concealment here, where it's important for the patient and for the provider to not know what group the patient is assigned to until it's too late to change what group they're in so that you can't perturb the study because you have a personal belief in the outcome. Allocation concealment issues and crossover were a problem with the original mammography study, the New York HIP study, where when they went back, they found that providers enrolling women would differentially offer mammography to patients based on personal characteristics or relationships. And so allocation concealment is meant to keep that from happening. Outcome assessment, you must blind those ascertaining the outcomes to the study subject group whenever possible to guard against investigator bias. So if I blinded the patients to study group and the observers, the outcome observers or investigators, that's a double-blind trial. And the idea is to not let the feelings of the investigator have them look more carefully for an outcome in one group versus another. Then there's this phrase, consider all relevant outcomes. This is the issue around, you want to not just win the battle, you want to win the war. So there are a group of medications, flecainide and echinide, that were used to prevent ventricular tachycardia. Ventricular tachycardia is a ventricle-based rhythm that is high-risk and pre-fatal. And they found that these drugs could actually take people at risk for V-fib and prevent them from progressing to V-fib in randomized controlled trials in the hospital, usually with electro-stimulation studies. So they sent the patients out with these drugs and post-marketing found that for whatever reason, people on these drugs had sudden cardiac death more frequently than those people at risk who were not taking the drugs. And had they not looked at sudden cardio, in fact, they didn't when the drugs were approved, without that post-marketing, they wouldn't have picked up those all relevant outcomes and those drugs are not used today. Another example was in the original use of gemfibrozole and cholestyramine to reduce cholesterol in the LRC study, randomized controlled trials. They found that the people treated with those drugs had a higher mortality rate than those not treated with drugs in an RCT trial. And yeah, I will say that when they looked into it later, it was there were more homicide deaths, suicide deaths associated with the drug use and the endocrinologist said that's a serious finding. And I remember an endocrinologist telling me, he said, they can't think of how this drug could increase the risk of homicide. And a woman in the group held up her hand and said, you've never lived with a man trying to decrease his fat intake. But that's just another example where we don't use those drugs again, because we don't really have the evidence that all mortality, cause mortality is reduced. Safety monitoring for adverse effects is to try to make sure that you aren't causing more harm with the drug. So that gets back to the echinide and thucanide examples. There's a separate committee, separate from the investigators who look at every adverse effect. And when they reach a certain level of concern, they can actually stop the study for safety issues. And so that's what happened in the study looking at type control for type two diabetics. They actually found that the type two diabetics who were having their A1Cs and blood glucoses carefully controlled at a higher mortality rate. And so they ended the study. Stopping rules for me is a controversial issue. This is a point at which results become statistically significant. And the thought is ethically the trial should be ended and everyone should be provided the drug. The problem I have with stopping rules is every time they've been used, they've led to an incomplete outcome. So they were designed during the early 80s when we were looking at HIV drugs, specifically ATZ. And what they found in the MSN community, the AIDS community, is that patients would go, they knew that half of the drugs were placebo in their group. And so they would come and have these kind of parties where everyone would put their drug, study drug, into a bowl and everyone would take out their allotment. And so the investigators found this out and said, well, they understood it because it was a fatal disease. You wanted some chance of hope. So they went to the community and said, we can't, we'll never get approval for the drug. We'll never have treatment protocols. And they made a deal with the affected community saying, as soon as the results become statistically significant, we'll break the blind and give all subjects the study drug. The issue is that it was so early that looking at the long-term efficacy and safety of AZT was never firmly established. It got worse with other drugs, like the use of CIRMs, estrogen receptor modifiers, to prevent breast cancer. So they gave the CIRMs to women at increased risk for breast cancer. And they stopped the study as soon as the risk of stage one cancer was significantly less in the treated group. But it was at the same time where fatal pulmonary embolisms and other thrombogenic outcomes were on the increase. And if you looked at the two graphs, there was a chance they would have crossed had they run the study another year. And it left clinicians with this issue about, yeah, I can give you a drug that may keep you from getting breast cancer, but might kill you with a pulmonary embolism. And it made it very, that's the tamoxifen and raloxifen trials, and makes it difficult to know what to do. The last time, the last one I will mention is the DPP. We stopped the study as soon as both the exercise group and the metformin group has statistically significant decreased risks of developing type two diabetes. But the average amount of time in the study was three years. And so what I know today is that I can get people to take off 5% of their weight, keep it off and not get type two diabetes for three years. But I don't know if I can do it for five years. So in general, I'm not a fan of stopping rules. And I just think we need to be a little bit more strategic about how we apply them. When we talk to analysis, RCTs have to be analyzed using the same called the intent to treat approach. That means subjects must be analyzed with the group they were first randomized to, and then cross over to the other group. Reassigning crossover invalidates the RCT because those that cross over are likely to be quite different from those who don't. You basically then create just another cohort study. The confounding variables must be comparable across groups, even after you do in the analysis. I'm sorry, let me go back to the last point. So when we started looking at medical versus surgical interventions for severe cardiovascular disease, or angina, you were randomized to either drugs or to coronary artery bypass surgery. And there were some subjects that crossed over. And so the surgeon said, well, they have to be in the surgery group because I operated on them. I know I did. And the investigator said, you want them analyzed with the medical group, because they probably only crossed over because they were worse. And then the surgeon said, I got it, okay. So that's the intent to treat approach. Confounding variables have to be compared across groups, usually in table one, because there are things called pairs of randomization. Sometimes RCTs compare continuous variables like blood pressure, like a number. In general, it takes a smaller difference to be statistically significant with continuous variables. And so this is just a warning that you probably would rather like to look at target cutoffs. So do you wanna know the diastolic blood pressure difference between two groups, or do you wanna know how many subjects in each group reach a normotensive treatment target? I think we've talked about all these sources of bias, errors of allocation, ascertainment of outcomes. Loss to follow-up is also a problem in RCTs. And I think we aimed at no more than a 20% loss to follow-up for the DPP and achieved it. Inclusion of all relevant outcomes, that's the win the war, not just the battle. Crossovers are always a problem. There was a study to try to determine whether vitamin C actually prevented the common cold. It was an NIH-sponsored study. They said, we need about 4,000 people to do this study. They said, well, we have 4,000 people who work at NIH. So they did the study there, and they randomized them to placebo versus vitamin C tablets. Now, the people at NIH are smart, and they found out easily that if you bit into your tablet, if it was bitter, it's an acid. It's salicylic acid. And at the time, we made all placebos out of sugar, so they were sweet. So everybody knew what they had. And they found that a substantial number of the people in the control group went out and bought vitamin C. And I remember one of the interview phrases was, they wouldn't be studying it if they didn't think it worked. So totally invalidated the trial, but we still don't know if vitamin C prevents the common cold. There is selection bias, but now it relates to external validity or generalization. So you really need, if you're using the study, to look at the study group and say, does this represent my patient population? And then finally, we talked about errors of randomization and confounding. Here are the issues in RCTs. In general, they're lengthy, they're very expensive. There can be ethical and legal issues, and they can actually arise during the study after randomization. So I think our case definition of diabetes changed because the definition of diabetes changed, fasting blood sugar over 126. Why was it over 126? Because in Europe, that translates to a millimoles number that is not, I'm sorry, that is an even number and not a decimal. So we had to change our case definition. Sometimes things like estrogen replacement can become unethical and raise ethical issues as they did during the women's health trial. Blinding can be difficult, especially if you're doing something to patients like, I don't know, like rectal exams or acupuncture. Crossovers can be common and dropouts and loss of followups, all major potential problems. Remember, we get strong internal validity at the expense of external validity. Power issues become important when the effect sizes are small and too small to reach statistical significance. All that being said, they're the gold standard of research design. I wanna quickly run through the other study designs. I think I'm a little bit behind schedule. It's hard to imagine when I'm just talking to myself, but pragmatic trials. These are designed to test interventions in everyday practice. Does it work in real life? Usually here, the intervention is compared with usual care or other interventions, and there could be a lot of those because usual care can be a wide range of different interventions. But now the outcomes are more diverse and they're patient-centered. So what is important to the patient? And what is the range of outcomes I might look at? Now you get better external validity and generalizability, but recognize this comes at a cost and it's the expense of internal validity because usual care variations may vary by important characteristics of the patients. Sample sizes may need to be huge, especially if there's a lot of usual care interventions. And the statistics can be complex and definitely can keep biostatisticians employed. Most often we see pragmatic studies in the context of phase four studies used in once a drug has been approved for use in the population through safety and efficacy trials. In a natural experiment, the researcher doesn't determine the group receiving the intervention. It just occurs naturally or under control of some other process. These can address problems where RCT interventions are unrealistic as to what can be implemented and sustained in a natural setting. So the example I think I mentioned earlier was light rail. So we can't really randomize cities to put in a light rail system. However, this is a natural experiment that occurred in Colorado where we could have started looking at the impact of standardized mass transit on physical activity and obesity. We can use them for rapid evaluations of innovative, expensive or complex interventions or even policy changes in natural settings. So when they first expanded Medicaid from 125 to 135% of the federal poverty level for pregnant women, Washington State did the expansion, Colorado always lagging behind did not. That was a natural experiment of a policy change which allowed for comparison of birth outcomes associated with that expansion of Medicaid. This has happened recently again in looking at the Affordable Care Act in states that agreed to expand Medicaid to all low income adults. 139% of the federal poverty level comparison of the overall mortality rates of all residents not just of Medicaid patients. They looked at mortality rates in the population dropped in the Medicaid expansion states compared to those states not choosing to expand Medicaid. Another natural experiment. These have worse internal validity because the states could be very different. Cities could be very different and they have limited generalizability again because not all states are the same but there's better generalizability usually than an RCT. We tend to try to improve internal validity with more data points both before and after the intervention as we would do in a time series analysis. Another intervention is a group randomized trial. Now the unit of assignment is a group that we can identify and we randomize the entire group to different exposures even though the unit of observation are the members of the group. Randomization provides the assumption of independence but at the group level, but we have this desire that the sources of bias will be fairly distributed across the study exposures. However, there is variation attributable to the groups themselves. From a statistical standpoint, this increases the standard error of the intervention effect and therefore makes you have to find a larger effect size. This is worse than when the number of groups is small, limiting your degrees of freedom and having more of this problem of interclass correlation which is that members of the group may be more similar to themselves to that class than they are to the comparison groups. Still, group randomized trials are a popular way of doing things when you can't randomize at the individual level. Say a Kaiser Permanente that has multiple outpatient facilities could randomize those facilities in a group randomization strategy and not randomize the individuals. In quasi experiments, the researcher cannot or does not assign interventions randomly but they could have some control over who gets the intervention, when, and when measurement occurs. You want the study design to match the question under study and recognize there are instances where an RCT might not be the best design because you want generalizability or when it's not feasible or appropriate. The concerns with these quasi experimental designs is that there are additional sources not controlled for by random assignment, specifically selection bias. And then this interclass correlation comes up again and it could be responsible for the observed effect unrelated to the intervention. This is a kind of confounding. The classic example is the individual level before and before after study design so that you don't know what would have happened in individuals without the design. So I'm just gonna go through a few of these. This is the non-equivalent control group design. You have study groups assembled not by randomization but they're intended to try to minimize unequal distribution of important confounders. And then you just decide which group gets the intervention. So group A and group B are not defined through randomization. They're just separate groups that hopefully I've measured something around confounders. I give group A the exposure. Notice I have two periods of before and after. So this is basically a before after study design with the addition of a non-equivalent but temporally related control group. It's a pretty common quasi experiment design. Also common is time series design. When you have multiple groups you have a multiple time series design. This is a refinement of the pre-post study design where now you do multiple measurements over time. So you get a sense of whether post-intervention differences can be assigned to the event intervention. So here's a multiple time series design. I have four observations before, four observations only and I can actually develop a trend line for these two observations before after and see whether or not there's a difference in the trend associated with the intervention. And then the control group controls for not having that temporally related intervention. Then finally, regression discontinuity. I mentioned this because it's a very popular design to at least talk about. I haven't seen lots of them executed but it's the kind of time series analysis. Now units are assigned to a condition based on a cutoff score and a measured covariate. For example, for a smoking cessation intervention communities that exceed a certain cutoff for packs of cigarettes sold or sold per capita are given the intervention and communities below that cutoff are the comparison. The treatment effect is measured as the discontinuity between the treatment and control regression lines at the cutoff point. Recognize this isn't a group mean difference which would suffer from regression team. When properly implemented and analyzed and when the underlying relationship is linear you can get an unbiased estimate of treatment effect which is what you get from an RCT. It makes more sense if I diagram it. So here's tobacco sales and here's smoking prevalence. Here's before the intervention. So the control group is the group that's below this cutoff. The intervention group is this group. And then when I re-measure, I redraw the lines and this discontinuity is the unbiased measure of effect. Well, we're done with study designs. Probably makes you all pleased. I'm gonna move on to causal association and confounding screening and a few more topics to kind of round out the last hour and 10 minutes. Causation has its roots in the Koch-Hinley postulates which was really designed for diseases where the cause was both necessary and sufficient. And almost often this is restricted to infectious agents. They're not as appropriate when the disease entities are multifactorial. And one of the things we know about chronic diseases is that they're most likely multifactorial. So diseases not caused by infectious agents usually require considering e-logic factors that are sufficient, but perhaps not necessary or not even sufficient, but contributory. How do we go about determining cause? You can do a randomized controlled trial or you can investigate statistical and temporal associations and then eliminate alternatives through research. Often in epidemiology we're satisfied or we have to be satisfied with this concept of causal association. The causal association was created by Dahl and Hill. It was created around cigarettes and lung cancer. So they had a specific exposure and outcome in mind when they created. They are now referred to in shorthand as the Bradford-Hill criteria, which was Sir Hill's first name was Bradford. So the association should be strong. That really means like a high relative risk, a tight, a high excess risk associated with it. So tobacco, the risks for lung cancer are seven to 12 times that of a non-smoker. Those are big relative risks. The association should be consistent. So you can't really do a study of cigarettes and lung cancer that doesn't show an association. The association should be strongest when you expect it. This is known as dose response or biologic gradient. And we were able to see that heavier smokers had higher risks than lighter smokers for lung cancer. The exposure should precede the outcome. This is one that's even with cigarette smoking, a little bit tougher to nail down exactly. But I think the investigators felt very strongly that given the clinical course of a rapid course of lung cancer in patients proceeding from the kind of small multi-cell tumor level to death was fast enough that they could establish temporality. I would say, I often say that the time to start smoking is when you're diagnosed with lung cancer because then, you know, it's not gonna cause it. Then finally, the association should be biologically plausible, coherent, and includes supportive data from other sources. And so where does the smoke go? It goes into the bronchi. Where does the cancer arise in the bronchi? Is nicotine and, I'm sorry, mainly TARS risk factors for malignant transformation? Absolutely it is. Does carbon monoxide translate to higher risk of heart disease? It absolutely does. And so there are biological plausibility around those characteristics. However, we worry about residual confounding in all causal association issues. Without an RCT, confounding is the element of doubt that we're always left with. Confounding is a distortion of the true relationship between a given exposure and a given outcome, resulting from a mutual relationship with one or more extraneous factors. The effect of the extraneous factors can account for all or just part of the observed relationship between the exposure and an outcome, or it can mask an underlying relationship. So I think this is often, I'm sorry, more words, sorry. It exists when the association between an exposure and an outcome is due in part or all to the mutual association with a third variable. So we know that hot flashes are associated with endometrial cancer, but that is through the mutual association with estrogen use. So we give estrogen for hot flashes and estrogen causes endometrial cancer, so that creates this confounded relationship. I like diagrams. I put the exposure of interest leads to the outcome of interest. The confounding factor leads to the outcome of interest. And then there's an association between the confounding factor and the exposure of interest. This is often a risk factor. This is almost always a risk factor, but this is an association that can be more complex. Sorry, I want to say that this is not a risk factor because you don't want the confounding factor causing the exposure of interest. Then it's in the causal pathway and then it's not a confounder. So here are the criteria for confounding, and you need both. The potential confounder must be associated with the outcome of interest, either being a risk factor or affecting the likelihood of recognizing the outcome. The confounder must be associated with the exposure of interest, but must not be a result of the exposure. So that leads us to when factors are not a confounder. So if my status regarding the confounder is a result of the exposure under study, then the confounder is in the causal pathway, or the confounder is in the causal pathway. It's not a confounder. So that means you don't want to control for the confounder because it's a result of the exposure or it's an intermediary between the exposure and the outcome. It's also not a confounder if your status regarding the confounder is a result of the disease under study. So sorry, back to the diagram. That means I take the outcome and the outcome causes the confounder. So it's not a confounder factor. If the confounder is essentially measuring the same thing as the exposure. This is called multicollinearity or collinearity. And it means these two are so tightly correlated that if I control for the confounder, I'm controlling for the exposure. This happens often in socioeconomic status where you might be looking at something like race and income and those two may be so tightly correlated that if you control for race, you take out the impact of income or if you control for income, you alias the effect of race. So you want to make sure that they're not tightly correlated, then they're not confounders. And then if the association between the confounder and the outcome of interest is thought to be due to chance. So we use a standard of confounding that it has to be statistically significant. Not mentioned on this slide is a mediator. And a mediator is a factor that impacts the degree, I'm sorry, impacts the outcome in such a way that there's part of the outcome that is due to the mediator that sits between exposure and the outcome. Mediator analysis is difficult. Usually don't talk about it. I think if you're worried about mediators on the exam, you might look up the definition, you might look at acyclic grants, directed acyclic grant diagrams that actually talk about mediators and how they might impact the impact on an outcome. But I think if you stick to confounding, you're pretty good for the exam. Now that we've defined it, how do we find it? You can determine if the potential confounder is associated with both the exposure and the outcome. That's an easy way. You just say, is it associated with both? And it's a potential confounder. You do want to rule out not in the causal pathway, not a result of the exposure understudy, not a result of the outcome. The other way you can do it is adjust for the potential confounder in analyzing the data. And if there's a difference between the adjusted and unadjusted estimate, then the potential confounder is a true confounder. I'm going to give you examples in a minute. How do you account for or control for confounding? You can prevent it in the study design. If you're worried about confounding by sex, you could just study subjects of one sex. You could match in the study design on the basis of their status regarding the confounder. Then you have to use a matched analysis. Or you can do an RCT design and randomly allocate subjects to put confounding into both groups, just recognizing that there's still a chance, occurrence of confounding. But most often we remove the effects of confounding in the analysis. We can do stratum-specific rates. So if we're worried about confounding by gender, by sex, just list the effect of the exposure on the outcome for males and females. You can use rate adjustment. We'll talk a little bit about that. You can use Mantel-Hansel methods to account for the confounder or to adjust for it. Or you could use regression analysis, which is especially attractive if you have several coincident confounders. I think I asked Jill Whalen one year, Dr. Whalen, and she talked about the Mantel-Hansel method in her statistics lecture, and she said she didn't. So I thought I would just share it. Here's the way you do it. It's providing an average weighting of the risk ratio or an odds ratio based on a weighted average of the different levels of the confounder. Since regression is so powerful, we tend not to do Mantel-Hansel so much anymore. I do want to tell you that other than continuous variables, it can be used for multiple levels of different confounders. So it's very flexible, but it can't mix continuous and categorical variables. And it's not as mathematically robust with small numbers as logistic regression. Here's an example. I think this is the same example I'll use in a minute where there's confounding by sex on heart disease. And if you do the cross product, you'll get one answer, but this is the weighted average, 1.27, which averages across the levels of the confounder. Do I think they'll make you do a Mantel-Hansel adjustment on the board exam? No. Couldn't imagine it. However, knowing that it's an available technique that's used for confounding and that it produces a weighted average of the risk ratio, I think it's fair game. Now, confounding would be great and easy, I think, were it not for effect modification. So effect modification occurs when the effect of a risk factor on an outcome is different at different levels of a third factor. And that third factor is known as an effect modifier. It sounds like this third factor thing starts sounding a lot like, is that a confounder? But the definition says nothing about the relationship between the exposure and the effect modifier. It really means that the exposure has different impact at different levels of this third factor. The most common effect modifiers seen are age and sex. For example, the effect of estrogen on heart disease risk is different for men and women. So if you give estrogen to men, you increase their risk of heart disease. And for women, it either stays the same or is not elevated to the same level, or for some women might be protective because that impact is different for different sexes. Sex is an effect modifier for estrogen use. In analysis, it's usually not appropriate to summarize over the strata of an effect modifier, but to report the different strata. So here, you would miss the fact if you kind of summarized over the different impacts on estrogen in men and women, you might get an answer that says there's no effect at all. So I have an example to demonstrate both at the same time. So here's a made-up example with made up numbers looking at high cholesterol in males and females, and heart disease or no heart disease. So CAD is coronary artery heart disease. And so if I split things out and I run the odds ratio at just the cross product for males, I get an odds ratio of 1.7. Then if I do an odds ratio for females, I get an odds ratio of 1.3. So I'd pause at this step and say, is sex an effect modifier for high cholesterol? So the answer is conditional. It's like, maybe. Why would I say maybe? So I would say yes, because 1.3 and 1.7 are different. This says that women with high cholesterol have a 30% increased risk of heart disease, and men have a 70% increased risk of heart disease. That is a difference. So why did I say conditional? So for effect modification, we apply statistical significance and say the difference must be statistically significant. For confounding, we say all it really needs to do is to change the results, modify the results. So it has a different level of use. So when I say, do you see effect modification? You would say yes, if this difference was statistically significant. Now I'm going to ask if there's confounding. So remember I said there's two ways to do it. One is to look at the relationship between the confounder, here sex, and the exposure, here cholesterol, and then the exposure and outcome. We'll do that in the next slide. The other thing you could do is pool the data, ignoring the strata, and see if you get a different answer. So here I've added all these numbers that say I didn't measure sex at all. These are the study numbers I would get. And I get an odds ratio here of 0.96. And you ask yourself the question, is this pool odds ratio a reasonable weighted average of these two separate strata odds ratio? And your answer would be no. It's not even in between them. It's outside of the range. So this combination of separate or strata into a pool of data that gives you a completely different answer is called Simpson's paradox. So you have said yes, there's confounding. I said the other way to do it is here's sex and heart disease. You get an odds ratio of 0.66, which is different from one. So yes, there's an association with heart disease. And then there's sex with cholesterol. Here the odds ratio is 34.5. And again, it's related to both the outcome of interest and the risk factor and meets the criteria for confounding. Rate adjustment is another approach to look at confounding. And it's a technique we use to provide a single number or adjusted rate for each of two or more comparison groups. This single number summarizes the experience of the group but is not influenced by a confounding variable when you make the comparison. That's a lot of words that I think I need more words. It's often used to account for the effect of age. Age adjustment can also be used to adjust for sex, can be used to adjust for any confounder or group of confounders. In rate adjustment, you essentially estimate how the comparison would turn out if the groups had the same distribution of the confounder, or in the most common case, the same age distribution. So you determine age-specific rates. How do you do it? Determine age-specific rates for age intervals in the populations you wish to compare. Then you choose a standard population whose age distribution is known, like the U.S. population. So here's an example. We're going to look at a rate of disease in Colorado and Washington. So I use Washington because that's where I got my MPH. So I spent time in Washington, too. All right, so we're talking about the U.S. population, age 40 to 50 being about 10 million, and age 50 to 60 being about 10 million, and the total population being 20 million. So I take the rate of disease for these 40 to 50 year olds in Colorado and the rate of disease for the 50 to 60 year olds in Colorado. Over here I have the Washington rate of disease for those two age groups. Now I'm going to calculate the expected number of cases that I would have thought I would see in Colorado if Colorado had 10 million 40 to 50 year olds, and how many cases if Colorado had 10 million 50 to 60 year olds. So I just am going to multiply these two numbers to get the expected number of cases, and then I'm going to repeat that for Washington. So I'm going to calculate the number of events expected to occur in each group of the standard population using the age group specific rates from each comparison group. So here we go. 10 million times 1 in 1,000 is 10,000. 10 million times 1.2 in 1,000 is 12,000. So now I have 30,000 and 35,000 both in a total of 20 million, and I can develop the age-adjusted event rate for each comparison group. So I just put the expected events in the standard population using rates from the comparison group divided by the total in the standard population. For Colorado that's 30,000 for 20 million or 1.5 per 1,000, and the age-adjusted rate for Washington is 35,000 in 20 million or 1.75 per 1,000. Now since these are both age-adjusted to the same population, I can now directly compare them and say Washington has a higher rate of disease than Colorado adjusted for age. The advantage of using the U.S. population is I can now compare Colorado and Washington to every other state, and I also can compare Washington, Colorado to the nation as a whole. So it allows me a lot of comparisons that could be meaningful in looking for etiology and things I might want to address, and it takes out one of the biggest drivers for disease rates, which is the age of the population. So you interpret these rates as the expected event rate for each comparison group if they had the same distribution of the standard population. They will vary depending on the age distribution of the standard population used, which is why we usually use like the U.S. population. If all you want to do is compare the event rates in the comparison groups, then it doesn't matter what population you use. You could just divide the two rates. Regardless of the standard population, you'll get an age-adjusted rate, but if you want to use the age-adjusted rates in other comparisons, you want to use something like the U.S. population. So when you look at most vital statistics reports for states, in fact probably all, they all age-standardize to the U.S. population. There is something called indirect adjustment where we determine the age distribution. I'm sorry, where we do it kind of in reverse. We determine the age distribution for the populations we want to compare, and then determine the observed number of events for each population using the age-specific event rates from the standard population. So I'm going to kind of skip through this example. I'll let you read it and go through it on your own if you have interest. Indirect adjustment is less commonly used, and I include it mainly for comparison. So I did do an example where the age, now here's the U.S. death rate that's used and the population from each state that's used to develop the expected number of deaths. Here's the expected number, and now I have an expected number and a total population, and I can calculate a standardized mortality ratio. In this example, I've made a difference so that Colorado's SMR is higher, so they have a higher standardized mortality ratio, and you could divide these two to get a relative risk. Direct adjustment is commonly used to provide descriptive data, and in comparing data from several different studies, where indirect adjustment can be preferable when there's small numbers in each age category, and changes of only one or two people in the numerator will have big changes in age-specific rates. Both numbers give a single number for each study group, and they're both based on artificial numbers based on hypothetic circumstances. And this slide just compares the two, or what do you take from the standard population, what do you get from each study group, and what's the result of the adjustment. So with that quick breeze through, especially of indirect adjustment, let's focus on disease screening. In the textbook, or reference book, called Prevention, John Last's Prevention book first presented the disease prevention spectrum, and I bring that up because really from the impact of cardiology, these terms have changed, but I wanted you to know how we use them in preventive medicine and their original terms. So the disease spectrum starts with no disease, to the biological onset of disease, but before it becomes symptomatic, to the development of symptomatic disease, to the development of disease with complications, and then death. We can intervene along the way with different intervention approaches. So primary prevention is intervening between the no disease and the asymptomatic disease, or the biologic onset of disease. So primary prevention would say we're going to keep the disease from happening at all. It would be things like smoking cessation or prevention to prevent lung cancer. It would be immunization to prevent infectious diseases. And so that's in a person with BRCA1 and 2 mutations, it would be prophylactic surgery to remove either or both the breasts or the uterus or the ovaries to prevent ovarian cancer or breast cancer. So those are primary prevention strategies. Secondary prevention as used originally is the intervention between asymptomatic disease and the development of symptoms. And so secondary is prevention in the original iteration is disease screening. Cardiologists came along and said, now we're going to call you've had a heart attack. So now that's preventing the next heart attack is secondary prevention, which is a misnomer. A heart attack is symptomatic disease intervening between symptomatic disease and disease with complications is tertiary prevention. So this is really what the cardiologist says you had your first heart attack. Now we're now we're going to give you statins. Now we're going to control your blood sugar. Now we're going to do these other interventions and prevent the second heart attack. And I've not been able to convince them to change their terminology, but I wanted you to know how we talk about it. And we're going to call it screening from here. These are the Wilson Young criteria for screening for disease. They still persist today. I think they're still very useful. The disease should be important. Otherwise, why look for early detection? The disease has to have a recognizable pre-symptomatic stage long enough to provide you a window to allow for screening, then diagnosis, and then treatment. And you want to get that all in before the person becomes symptomatic because then why wouldn't you just wait for symptoms? There need to be reliable screening tests for the pre-symptomatic stage and have acceptable sensitivity and specificity as well as acceptable risks for the screened individuals. This next one is really key. Treatment of the disease during the pre-symptomatic stage must result in improvement in outcome, either morbidity and or mortality. Otherwise, all you're doing is diagnosing the disease earlier and not changing the outcome. This is interesting because we often shortcut this very critical issue without which you probably shouldn't screen for disease. I would say you shouldn't. Sufficient resources and access to the resources must exist for diagnosis and treatment of disease in the population of positive screening tests. I used to say, you know, this is the U.S. This is really made for third world countries. But this is a really important bullet point when we start to talk about equity because it's clear that there is not equitable access to the resources responsible for diagnosis and treatment of all of the diseases we might detect through screening. Then finally, this one is a U.S. issue. Benefits of screening for the disease should outweigh the benefits of other programs. And we tend to think if we can figure out a way to pay for it, we're not going to worry about opportunity costs or overall health care costs. This does become important as costs continue to go up even after the Affordable Care Act. So interestingly enough, screening is one of the few areas that belongs to us and that other people forget all the time. So we're going to talk about screening test utilities, talk about screening to a very deep degree. So when we do screen test utilities, we assume there's a truth. Either have the disease or you don't. And then you have the screening test results. And so because no test is perfect, that puts you into one of these four squares. My test is positive and I have the disease. That's a true positive. My test is positive and I don't have the disease. That's a false positive. If I don't have the disease but my test is positive, I'm a false negative. Let me say that in a different way. Let me say it in the correct way. If my test is negative and I have the disease, that's a false negative. If I don't have the disease and my test is negative, I'm a true negative. So this is a very important diagram. I actually sometimes recommend that you get used to drawing it yourself and then drawing out the equations for sensitivity, specificity, and positive and negative predictive value, which we're going to talk about next. Sensitivity describes how often a screening test detects a disease when the disease is actually present. So it's going to be the true positive over all those with the disease. So that's the true positives over the true positives and false negatives, right? All those with the disease are the true positives and the false negatives, and the sensitivity is the true positives over all the positives. Specificity describes how often a screening test detects the absence of disease when it is indeed absence. Or true negatives over the total without the disease. Or true negatives over true negatives plus false positives. So again, here are the people with no disease. So the specificity is true negatives over true negatives plus false positives. Ah, but predictive value is different. Positive predictive value, often sometimes called predictive value positive, describes how often individuals with positive tests actually have the disease. So that's true positives over all positives. Or true positives over true positives plus false positives. So now these are all the people who test positive, and the positive predictive value is the true positive over all the positives. The negative predictive value is going to be the percentage of people who test negative who truly don't have the truly, I'm sorry, the percentage of people who don't have the disease who test negative. So it's going to be the true negatives over all the negatives. Or true negatives plus false negatives. How often individuals with negative tests are actually disease-free. Now I often pause here and say, as a patient, this is what you want to know. You don't really care so much about sensitivity and specificity. You want to know about what your test means. So if my test is positive, what is the chance I actually have the disease? If my test is negative, what is the chance I really don't have the disease? Or the corollary, I could have it and just not know it. Prevalence impacts these conditions in different ways. Sensitivity and specificity belong to the test. They remain the same for the test, regardless of the prevalence of disease in the population. They are characteristics of the test itself. Predictive value depends both on sensitivity both on sensitivity and specificity, but then is also impacted by disease prevalence. So think about this. If you have the test and you apply it to populations with lower disease prevalence, the positive predictive value is going to go down and the negative predictive value is going to increase. So what it means is that if there's less disease out there, a positive test is less likely to be right if sensitivity and specificity stay the same. On the other hand, since there's less disease out there, a negative test is more likely to be negative. So the negative predictive value increases. On the other hand, if the disease prevalence increases, positive predictive value increases and negative predictive value drops. So these are effects that are important to recognize, to understand, to memorize, if you can't understand them, but they should make sense. I'm going to give you an example. Fecal occult blood testing is 92% sensitive and 95% specific. Of course, this is the new FIT tests. They're not really quite this good, but they're getting close. But let's say it was. The prevalence is two per thousand. What's the positive predictive value of a positive test? That is, what percent of positives will have colon cancer? Now in this example, if you can do this example, you can do any problem that you would face in a test, in the board exam. I doubt that they will ask you to do the mathematical calculations at this level, but if you can understand this, you can understand how to do this. So how would I go about talking about this population, two in a thousand, the positive predictive value of a positive test? Well, I just have to assume I test a lot of people. So I put one with a bunch of number or zeros behind it. Say if I have 100,000 adults and the rate going back is two per thousand, 200 of those adults will have cancer, which means 99,800 will not have cancer. Now I have the test results. Remember, it's 92% sensitive, 95% specific. So I know how many of the 200 will test positive. I multiply 200 times 92, and I would expect 184 positives, which means I would expect 16 negatives. These 16 people have cancer, but because the positive, I'm sorry, the sensitivity is only 92%, they're going to test negative and be false negatives. Similarly, I can take the 99,800, multiply them by 0.95, which is the negative, sorry, is the specificity, and get 94,810 true negatives, which means I have 4,990 false positives. Now this is something I want you to pay attention to because when you have a rare disease, I've got to tell you, 95% specificity is really good. But because the disease is rare, you generate a lot of false positives, and you have to do something to these false positives to know that they're not really positive. So this is one of the Achilles heels of screening tests in low-prevalence settings, is that you generate way more false positives than true positives. So 184 out of 184 plus 4,990, or 3.6% of people testing positive, will have the disease. So even with 95% specificity, you get a positive predictive value of 3.6% of people testing, and you have to test all of these people with some additional test to determine that they don't have colon cancer. Look what happens if the prevalence increases. I'm sorry, the negative predictive value is way high, over 99.9%, because the disease is low, the incidence is low, so a negative test is going to be right. But when we increase the prevalence now to 50 per thousand, the positive predictive value is going to rise to 49.2%, and the negative predictive value is going to decrease, although only slightly. So here's the other example. Now I have 50 per thousand, so 5,000 will have cancer, 95,000 will not have cancer. Of these 5,000, 4,600 will test positive, 400 will test negative. Now you see I still, because it's still rare, still have a lot of false positives, and I've got a lot of true negatives, but now my positive predictive value is 4,600 out of 4,600 plus 4,750, or 49.2% positive predictive value. So this is the reason why we screen high-risk groups, is because it improves our positive predictive value. Just some caveats in screening for rare diseases. If the disease is rare in the population, in the population screened, even a test with high sensitivity and specificity will produce many more false positives than true positives. These can result in significant costs, they can translate to health risks, it will provide anxiety, and you have to have further tests to diagnose the disease. Our strategies to improve predictive value include using a test with higher sensitivity and specificity, or targeting screening efforts on high-risk populations. This is another really important summary slide. I think it'd be good for you to understand, just as a public health person, or a preventive medicine person, because they're not always intuitive, but these are all true. So if you increase prevalence, you increase positive predictive value, and you decrease negative predictive value. So we just showed you that. The corollary, if the prevalence goes down, the positive predictive value goes down, and the negative predictive value goes up. Here's the ones that aren't always intuitive. If you increase the specificity, you increase the positive predictive value. And a lot of people say, well, you're getting more true positives. Isn't sensitivity that drives that up? And then I just kind of take you back to the formulas. Remember, positive predictive value is true positives over true positives plus false positives. What determines the false positives? The specificity. And so, because specificity drives this number, specificity has a huge impact on the positive predictive value. So as prevalence goes down, its false positive rate goes up, positive predictive value goes down. And similarly, negative predictive value, where do the false negatives come from? They come from sensitivity. So that gets us back to where we were, where specificity increasing increases the positive predictive value, and sensitivity increasing increases the negative predictive value. All right. Another topic under screening is screening test cutoffs. Often, there are times when it's possible to choose a cutoff for declaring a positive or a negative test. Most often, this occurs when the screening test involves measuring the level of a substance in a body fluid, such as urine and blood, although it can happen with radiologic screenings as well, like mammography. But let's stick with the level approach. In these cases, the choice of a cutoff for a positive test must involve consideration of the effects of trading off false positives or false negatives. We're going to use a PKU example, affects about 1 in 10,000 newborns. The Swedes did a cost benefit analysis decades ago. Here are the results. Here are different cutoffs for phenylalanine levels for newborns. And here are, these are the results for newborns with PKU. And these are the results for normal kids. And so what they do is they kind of increase the cutoff level. And what you see at the lowest cutoff level, there are no false negatives, but there are a lot of false positives, almost a similar amount, the positive predictive value being 57%. As you go up, you notice that your false positives go down a little bit at the next level. And so you improve your positive predictive value as your specificity improves slightly. And then at 0.6, you start to pick up false negatives. Your false positives go way down. Now your positive predictive value is 76%. And then at 0.7, you pick up additional false negatives. But you have very, very few false positives, and therefore a high positive predictive value. But then you come over here and look at the costs, the case per costs. These are in Swedish kronor, they ignore the cost of the test itself, and only the additional costs for diagnosis. So look at this phrase, and the lifetime care of undetected PKU infants. So the driver for this increased cost is the cost of caring for these false negatives. And that's why you see that number doesn't jump here. It actually goes down because you don't have to retest so many kids. But then when you start picking up false negatives, the costs go up, and the Swedes made their cutoff at this level. I like to do this diagrammatically, and this is PKU, but this is the same diagram for any result that looks, screening test that looks at a cutoff. So here's a curve for normal children for serum phenylalanine. Here is the curve for PKU children. So you see the curve is higher. And here's the combined curve if you didn't test at all. Note that no cutoff level will not incur some error. So at this cutoff level, at this cutoff level, you're going to end up with this many false negatives. Kids who have PKU, but you didn't detect. At this cutoff level, you're going to end up with this number of false positives that you're going to have to do additional tests with. So no cutoff separates those. If you choose a lower cutoff point, you're going to raise sensitivity, but it's going to be at the expense of lowering positive predictive value and specificity. And choosing a higher cutoff does the opposite. So we're always trading off false positives against false negatives when we talk about cutoffs. They may not deserve equal consideration. Here, the false negatives had worse, easily worse, worse health consequences and generated more costs. I want to talk a little bit about screening test biases. In the evaluation of a screening procedure program, you have to think about lead time and length time bias. These sources can result in finding improvements in disease mortality, even if early treatment of disease in no way alters the outcome. We'll talk about lead time first. This is also called zero time shift bias. It occurs because screening tests detect illness at earlier points in time. So if you develop a test that diagnoses the disease one year earlier and early treatment had no effect on survival, you and the person would know they had disease for a year longer than those who detected without screening. And if you compare the outcomes, you'll get the erroneous conclusion that the screening program resulted in an improved outcome when all it did was add a year to the length of the time the diagnosis was made. So here's a diagram. So here's the same cancer, no difference associated with screening. But because you detected the disease this time earlier, you add this survival time and attribute it to screening. So that's lead time bias. Length time bias is the second major source of bias. Understanding that most diseases' natural history varies in time span. One cancer can progress quickly through all phases with a short asymptomatic phase, short interval between development of symptomatic disease, and short interval till death. Another cancer of the same organ could have a very long indolent course with long asymptomatic and symptomatic phases. If the prevalence pool or those you're screening is made up of individuals with these differences, a screening test will be more likely to pick up individuals with a longer asymptomatic phase, and those detected by screening, that they're automatically have longer disease, unrelated to whether they were detected by screening. So here's the diagram. You see these blue lines have the longer lines. And so he screened right here, detected all of these blue folks with screening, and you got an 80% cancer survival rate. But the short time, you didn't detect them at all, and you gave you a lower time. If you would have just looked at the non-indolent courses, you would have got a different answer. So that's length time bias, oversampling cases that would have lasted longer anyway. This is a problem with prostate cancer, where most of the disease is indolent and doesn't metastasize and doesn't threaten the man's life. So parallel, and I want to go back to that. It's a little bit more complex. I just want to say in prostate cancer, a lot of the disease is never going to impact a man, and therefore, any analysis of the impact of prostate cancer screening suffers from lead time bias. Sorry, one more time, length time bias. There are methods of looking at multiple screening tests and an overall strategy. It can be done in parallel or done in series. In parallel testing, the overall screening result is positive if any of the tests is positive. So it makes it easier to become a positive and increases sensitivity, but therefore, it's at the expense of specificity. In series testing, the overall screening result is positive only if all the tests are positive, and this increases specificity at the expense of sensitivity. We use parallel testing in series testing in different strategies. So when we did HIV screening initially in the general population, we did ELISA, which is an antibody test, and Western blot, which is a more sensitive test. We did them in series. So if you had an ELISA, you had to do a second ELISA. If you're positive on both, you had a Western blot, and we didn't tell you you were positive unless you were positive on all three tests. So we were maximizing specificity, so we never told a person that they had HIV when they didn't. That was a values decision made by public health. On the other hand, for the blood supply, we applied the tests in series. So if you have two ELISAs and you're positive on either one, you're called a positive, and you're not retested. You don't get to get blood, and you have to have two ELISAs be negative and a negative Western blot before your blood can enter the blood supply. There, we're trying to really pick up sensitivity and valuing that over specificity so that no one who gets a blood transfusion gets HIV. Okay, our last topic is around concepts of infectious disease epidemiology. Someone else is actually going to talk about the frequency occurrence and aspects of certain infectious diseases, and I'm not going to do that. I'm going to try to give you the basic terminology that you need to think about when you're talking about disease epi. So we're going to talk about first types of host-agent interaction in the spectrum of disease. So there's a lot of different ways we can be infected. We can be colonized. The agent infects the host continuously with no overt evidence of disease or infection. This would be your normal gut flora. We all carry around, you know, some number of pounds of E. coli and other little bugs in our guts that keep our stomachs happy and are part of our overall flora that can be an important part of health. They're a colonization. Covert infection is the agent infects the host, but it's time-limited, but you never know you have the infection, and this is the majority of infections overall. So you did get the infection, but you never knew you had it. People who were born prior to the time of widespread use of varicella vaccine, you'll find many of them say, I never had chickenpox, and that when you do serum studies, you find that 94 to 96 percent of adults in the cohorts that were raised up to age nine before the advent of the vaccine actually have antibodies to chickenpox. They would have had a covert infection, and then overt infection is infection with disease, which is the minority of infections. Typical patterns of infections include inapparent infection, frequent and rare clinical disease. Inapparent infection is important in disease transmission and control, and we saw this with COVID, right? We were worried about people infected with COVID who were asymptomatic but still spreading disease. This influences apparent epidemiology. It understates the amount of disease, and since we only look at those we diagnose with symptoms, it overstates severity. Another pattern is clinical diseases frequent, few severe cases. That also is chickenpox, and then infection is usually always fatal, and for a period of time that was HIV. There's a high case fatality rate in different age groups for COVID-19 as well. These are infectious disease terms that it's good to know the definition for in case someone wants to ask you that on a board exam. Infectivity is the ability to involve or multiply in a host, that is to establish an infection. The ID50 is a dose of an agent necessary to infect 50 percent of hosts. So, the lower the ID50, the higher the infectivity. It takes lower numbers to infect more hosts. For example, hepatitis B has a very low ID50, or interestingly HIV has almost an order of magnitude or more ID50 to infect the hosts. Infectiousness is different. It's just the ability to be transmitted to other hosts, and pathogenicity is the ability to cause disease, that is to produce clinical illness in a susceptible adult. Virulence is a higher level of pathogenicity. It's the ability to produce severe clinical illness, including death, and the LD50 is the dose of the agent necessary to kill 50 percent of hosts. Immunogenicity is just the ability to elicit immune response, either cellular, local, or systemic. There are important areas to the natural history of infectious disease. The reservoir is a thing, like person, animal, insect, plant, or soil, in which the agent lives. It depends on for survival and reproduces within for transmission into a susceptible host. A vector is something that allows for the transmission of the agent. Transmission is the action of moving from the reservoir to a susceptible host, and the host is the organism at the receiving end of the transmission. These are the types of transmission, direct, immediate transfer from one host to another, like through air droplets or direct body contact, and control target is a primary host. It used to be that this was not a common source of severe illness, and then COVID-19 changed that, and it really was that kind of air droplets that breathed out and breathed in. I say not that common or severe, but the same method for SARS, the same method for influenza, and the way you control is you restrict the primary host. Indirect transmission is through an intermediate agent, like vector-borne, I'm sorry, vehicle-borne would be fomites and water, like doctors who don't wash their hands or their stethoscopes. Vector-borne can be mechanical or passive, which is disease carried on the legs of flies, or biologic active, such as mosquitoes. The control target here can be the secondary host, the person who gets bit. If you can keep them from getting bit or flies landing on, that's a reasonable target, although we have often worked on the vector itself, especially for mosquitoes. Airborne, aerosolized organisms in mite and dust is another type of transmission, and I think that's the one that is getting confused with air droplets. So here is the actual viron itself, or the bacteria itself that's been aerosolized into dust or mist, which is different from air droplets. These are terms used in transmission. Incubation time is a period between exposure to infection and the onset of symptoms. So, I've been exposed and now I have symptoms is the incubation time. Generation time is the period between infection and maximal communicability, which can be the same as the incubation time. However, there are some diseases where you are maximally communicable the day before you become symptomatic, so it can be different. Herd immunity, I think we know more about now after COVID. Resistance of a population to spread of disease based on the prior immunity of the population. Secondary attack rates measure the rate of spread of disease with an exposed group, the proportion of those exposed that develop infection. So, a high secondary attack rate leads to a high number of secondary cases. What we learned about more of and used more of under COVID was the basic reproduction number, also called the basic reproduction ratio, sometimes the basic reproductive rate, or R0, number of secondary cases per case in a totally susceptible population that depends on duration of the infectious period, probability of infection per contact, and the number of contacts per unit time. Epi curves will continue to increase when the R0 is above one and will decrease when the R0 drops below one. Here are types of infection in a population. Sporadic is occasional cases. Endemic is a usual low level, expected frequency of disease. I was hoping we were coming to endemic level of COVID, but now we may be going up again. Hyperendemic is a gradual increase in the frequency of disease above an endemic level. Epidemic is a sudden increase in the frequency of disease above the endemic level, clearly in excess. And a pandemic is an epidemic occurring across continents. There are different types of outbreaks and epidemics. Common source means it comes from a single or a point source. Examples are food poisoning. There can be ongoing point source like water contamination. The epidemiologic curve is single-humped with a rapid rise and slow return to baseline. The curve for an ongoing source shows a rapid rise to some persistent epidemic level before when the source is eliminated, then it levels off. Here's a point source epidemic curve. Here's an ongoing source epidemic curve. A propagated epidemic is transmission direct or indirect from one host to another. The epidemiologic curve is multi-humped. The first hump is the primary attack for those exposed to the index case. And subsequent peaks represent secondary and beyond attack rates as those in the first peak infect others. So here's a propagated epi curve. And if you look at the peaks, in between those peaks, you have the generation time. So you can actually do an epi curve, pick the generation time, and identify the agent based on their generation time. You can also have a mixed source and propagated epidemic curve. Here people exposed others by getting together them at a festival and created another curve. Types of outbreaks also include vector borne, but now there's a complex curve due to the vector. So when you start spraying for mosquitoes, you impact the epi curve. How do we control infectious disease? Well, we can control the reservoir, which means controlling the animal or human that is the thing that the bug lives in. Depends on for reproduction. You can control the transmission. So we talked about mosquito elimination and that's controlling the vector. You can also wash your hands or do filters or wear masks to try to control the transmission. We reduce host susceptibility. We can do it a couple ways. We can just separate you, that's social distancing, but we can also immunize you. Social distancing is kind of a combination, I would say, of control of transmission and reduction of host susceptibility. And then we can do disease eradication, which we've achieved once that we know of, which is this smallpox, which I hope doesn't come back. It can only come back if supported by human hands. These are some terms used in control of epi disease. Isolation is separation and sequestering of diseases who have known infection or are symptomatic, and you isolate them from susceptible individuals. Quarantine is separation of individuals with exposures to individuals with known infection, but they aren't known to have infection now. So that's a big difference that's important to know. Contact tracing is identifying, locating, and engaging contacts of individuals with known infection to test them, to immunize them, or to quarantine them. And ring vaccination is a term associated with identifying and vaccinating the contacts of individuals with known infection, then identifying and vaccinating the contacts of the vaccinated cohort, which is the second ring, and so on. And that's how we got rid of smallpox. And we have tried to use that for polio and are thwarted by socioeconomic factors in Africa. My last slide is simply a slide on a calculation of vaccine efficacy. I've done this section of the review course for I would say many years, and one year this was on the exam, and a student who had come back for the course for the unfortunate reason of not passing the boards told me that this was on. And so since that time I have included the formula for vaccine efficacy, and I will let you peruse that at your disposal. That brings us to the end of my slide set, the end of my lecture. I hope that you find a way to look through all four hours in a way that's not exhausting and boring, but stimulating and useful to you. And I wish you, each and every one of you, only the best in your exam. Thanks.

epidemiology

disease frequency

descriptive epidemiology

excess risk

study designs

causal inference

confounding

effect modification

disease screening

incidence

prevalence

mortality rates

case fatality rates

Bradford-Hill criteria

infectious disease epidemiology