Public Health 250a - Lecture 13

Art Reingold: Good morning. Good morning. So, um, a couple of administrative announcements. So first of all I understand that some people would like at least a copy of the presentation on Friday. If you were here on Friday you know that Len Syme doesn't need a Power Point in order to talk intelligently unlike some faculty. There is no Power Point presentation. As far as I know the audio should be available. If he spoke into the microphone in theory that was captured and should be posted on bspace or wherever it's posted. That should be there. Secondly in terms of the request for the derivation of the formula of attributable risk that's going to be discussed in section this week and the entire derivation will be posted on bspace. Just to point out that's one difference between 250 A and 250 B. In 250 B I actually derive all the formulas and equations. Here we state then and don't derive them. For those interested you'll see the full derivation. Despite my failure to initially remember it the last slide I showed on Wednesday with population attributable risks and odds ratios was in fact for triggers for heart attack for myocardial infarction. Several of you e-mailed to me. It's interesting to look at that particular graph and see the many, many things that can potentially set off a heart attack. Some have a high odds ratio but low attributable risk because they are uncommon exposures. Others have a lower odds ratio but in fact a higher attributable risk because they are quite common exposures. I think it nicely illustrates the relationship between those things. One last administrative thing. Because I need to be in Argentina on Friday of this week professor Bates has agreed to do the two presentations on experimental studies with individual randomization. So we slightly changed things. Michael will be presenting today and Wednesday. So they come in the intelligent sequence and then on Friday Lisa Barcellos will be talking about genetic factors in disease. So the basically there's a switch between what's on the schedule for Wednesday and for Friday. And then next Monday I'll pick up the discussion on randomized studies in which we randomize groups of individuals rather than randomize individuals. So any questions about the schedule? Okay. Michael. Michael Bates: Thank you, Art. So, as Art said I'll be talking about randomized trials with individual interventions and this is basically the list of topics that I'm going to be covering. I've got two hours I guess. Today and Wednesday. So I haven't split it into two separate distinct talks. I basically have one talk. I'll finish at some point today and do the rest of it on Wednesday basically. These are the things I'm basically going to be covering. The general features of experimental studies. And I'm going to talk some detail about parallel study design which is really the main type of design, randomization, blinding, also known as masking. Efficacy and effectiveness, data analysis and some alternative study designs which I probably won't get to until Wednesday. Some ethical issues and talk about early termination of studies. That's the list. So, when I teach the summer epidemiology class I like to constantly remind the class of this hierarchy. At least my hierarchy of study designs maybe not everybody in epidemiology would completely agree with it. There are some areas here which, you know, you could swap some of these around possibly. But basically it's a hierarchy starting down at the bottom, I say at least informative. I could replace that with hypothesis generating. And moving up through this list here to the top where we have analytic study designs. Have you talked about the difference between descriptive and analytic studies? Good. These are more hypothesis test. And today we're going to be talking about experimental studies. The other day I talked about ecological studies which are more towards the descriptive study design. This is more a continuum it's not like there's a clear cut point where descriptive studies change over to experimental, change over to analytic studies. It's more of a gradation. But today we're going to be talking about experimental studies often regarded as the gold standard of epidemiology studies. When they are properly conducted and they have a good enough sample size they have a very high degree of validity. In other words they are free of bias. I know you haven't talked about bias or confounding, but you will be. This will be clearer. Unfortunately I'm going to have to introduce some of these terms like bias and confounding today because it's unavoidable when talking about experimental studies. The thing about epidemiology you can't learn it in a completely linear way. Once you go to the end of the course you'll have to cycle through the course notes a few times and things that didn't perhaps make complete sense the first go around will make a lot more sense when you revisit them. And you can also think of experimental studies in humans to some extent the human analog of say toxicology studies. I came from a background in toxicology involving rats and mice but I found that humans, human studies were more interesting that's why I switched to epidemiology. Basically experimental studies in humans can be thought a bit like toxicology studies in animals in terms of the overall study design. So we can, there's a major split if we look at the range of epidemiology study designs as I set out in the hierarchy. There's really a very big divide here between experimental studies which you're going to be talking about today and specifically individual level studies and observational studies which we're not dealing with today but you will cover in some detail. The thing about observational studies they observe people and place. They record data on their exposures and health outcomes. There's no interference with these people. We try not to interfere and see what happens with them in their natural living circumstances. The experimental studies as I'll describe we do interfere with the people in terms of their exposures. The main defining feature of experimental studies is the allocation of treatment. That is really the big thing that distinguishes experimental studies from observational studies. Usually the allocation is randomized. There may be a few instances, for example, phase one studies in the hierarchy of clinical trials where randomization may not take place. We'll talk about what randomization means and how to go about it. Basically the people are randomized to groups for different treatments allocated. The participants are followed over time and the health outcomes they experience monitored. They go under different names. And they use quite a bit of terminology to describe the studies such as intervention studies. And as I'm going to explain they can be used for treatment purposes or for prevention purposes, but they may have completely different names. So treatment studies may be called randomized controlled trials, clinical trials, therapeutic trials, maybe some other trials as well. In prevention settings they may be called field trials or community intervention trials. I think you're going to be talking about community trails next Monday. We'll stick to the studies which have the individual people as participants today. So as I said, studies may be concerned with either prevention or treatment. So, the prevention, this involves interventions given to people who are basically healthy. They may be higher risk individuals. They may have a particular genetic make up that puts them at higher risk. It's to prevent disease. Trials of vaccines would fall into this category. Another example here does tamoxifen lower the incidence of breast cancer risk in high risk women compared to women not given tamoxifen. I think what the studies have found it's only in a particular genotype, a particular genetic gene make up that they, that tamoxifen is actually protective. And the treatment studies where they're given to people to either try and cure them, your study populations who maybe have the disease and you split them into different groups and you try and see whether it cures them or causes remission or reduces their risk of recurrence or whatever. These are the two basic study types. The first instance that is usually cited of an experimental study by James Lind, a British naval surgeon in the eighteenth century. At the time scurvy, which most of you know was caused by vitamin C deficiency. The British empire more or less stretched around the world. They were out to sea for many years. Anyway, Lind who is a naval surgeon he did this early clinical trial and took 12 men with scurvy and divided them into six groups of two each. And he gave them, administered these treatments. This is supposedly a picture of him treating the sailors. And he found that of the six treatments, it was oranges and lemon which were the only ones that really effective. But as is often the case in public health it took, how long, it took 50 years or so before this was adopted. In those days there were many instances of this where early public health discoveries are not adopted for maybe a century or so later, 50 to a hundred years later. Eventually the British sailors were given lemon juice or lime juice, which is why British sometimes referred to as limeys. They gave them the lemon or lime juice. So, okay. We're going to be talking about individual persons today. Not the community interventions. Preventive only. You don't treat communities for disease generally. You give community interventions for prevention. Individual person interventions can be therapeutic or preventive. This is an example with women with stage one breast cancer survive with lumpectomy as long as women who are given lumpectomy plus radiation. This is an example of a study with individual people treatment study. So, there's a key ethical requirement in terms of being able to carry out an experimental study. Treatment can only be given in an experimental study if it has potential benefits. That can be curative or preventive. It must have potential benefits. This has major limitations on in terms of what exposures or what treatments we can give people. What would be an example of something we couldn't test in an experimental study? Clearly obvious. Many things. Anthrax, smoking, any of these things. This is in some senses a problem that makes it more difficult for people who are mainly in observational epidemiology such as myself to actually conclusively determine cause and effect. With experimental studies if they are properly conducted with a large sample size then you can fairly clearly identify causal relations but with observational studies we can't. There are many things we can only investigate in observational studies. This is the primary requirement. It has to have either, have some sort of potential benefit. We'll come back to this probably on Wednesday in terms of when the issue of equipoise, which we'll discuss. Okay. So, this is the general schema for the conduct of experimental studies. So you start by having some sort of hypothesis. Some sort of purpose of your study. Design the study and obtain funding. And then you have to get as with all epidemiologic studies, you need IRB approval. Berkeley has its own IRB which we on this campus would apply to. And I'll talk about that more on Wednesday. And then you need to have some study participants selection and recruitment procedures based on certain eligibility criteria for the study participants and then you need to get informed consent. And that point the eligible and willing participants are randomly allocated to one or more study treatment or intervention groups if you like to call it that. You basically follow them for some period of time and then to investigate whatever the particular study outcome is that you are investigating, whether it be cure or remission or first occurrence or disease in prevention studies and so on. And then basically the statistical analysis relative at least to observational studies is relatively straightforward in terms of comparing one group, the rates of the outcome in one group with another. So the question of number of participants. So, this involves power and sample size calculations. You are not covering in this course, but if you go into 250 B or do some of the statistics classes you will definitely do this. So basically we have to determine the study size. This is determined up front. It's based on a number of assumptions, particularly in terms of the number of disease cases that are likely to occur. And the implications of these sample size calculations are the prevention studies usually have much larger sample sizes than therapeutic studies because in therapeutic studies we are starting off with people with the disease and you are looking for some appreciable benefit in terms of reduction in terms of cure. Whereas with prevention studies we maybe have to have a very large population because the rate of the disease may not be very high, but you may, you want to detect a difference between the two groups. Maybe one getting a vaccine and another one getting a placebo. You may need a large population size, maybe tens of thousands in order to confidently detect a difference in the incidence of disease between the two groups. Now, this is the general schema for randomized trials. So, you have some reference population which is a population that you are wanting to be able to make some sort of inferences for. From this reference population you take an experimental population. Some of these people may be unwilling to participate. You have some number of non-participants. Then you have some willing people. And some treatment allocation into two groups a treatment group and a comparison group. It's fairly straightforward. Um, and this basically just summarizes the groups. The reference population, the general group which results of a trial are intended to be applicable. That may be a large population or a somewhat smaller population. Um, and then you have your experimental population. People who are considered for the enrollment in a trial. And then you have your actual study participants. And those study participants are, well I should say first we have some selection criteria which we use to take people from the reference population to determine our experimental population from which the study participants derive. Study participants are the ones actually willing to participate. And you have a number of exclusion and inclusion criteria for study participation. And sometimes this is a compromise between those who are, the population more suitable for research and those best for generalization. And so, for example, in prevention trials you might if you are wanting to, for example, see whether a particular treatment is effective in reducing the rate of lung cancer you might just say focus on smokers because they are more likely to have the lung cancer. Rather than take a general population sample. And you may disease to exclude people who are likely to be lost to follow up. The follow up people from the beginning of treatment to the end of the trial. You may make some decisions to exclude some of these people who may not be likely to be reliable. They may not be compliant. They may be planning to leave the area and so on. These are the individual decisions made in the study design. Clinical trials have various phases of testing. These are basically the phasing. There's preclinical testing likely to involve studies in chemistry and cell cultures and animals. Before you get to the stage of actually being ready to treat human beings. And then we have these sequential phases. First screening for safety, establishing the testing protocol and final testing. I'll give you more detail on these. The phase one studies involve a relatively small number of usually healthy people and small amounts of the drug are administered just to determine its safety and also to see how it is metabolized, how rapidly it's excreted. Whether or not the metabolic parameters in humans are similar to what are being observed in animals. They are very different than the animal models may not really be predicting what might happen in the human situation. That's phase one. If a new treatment survives phase one, then you may move onto phase two. Which is testing for safety and efficacy in a larger population. And you may look at different dose levels. And this is to help with the designing of the larger trial. If you move into phase three. So, the larger trial, phase three is involves much larger study population. It could be thousands of people. And usually you're testing in comparison with the current standard therapy or if there's no current standard therapy you may be testing against the placebo. And this is the last phase required before in this country at least the FDA will approve a treatment for wider use. But that's not the end of the story. The phase four studies which are various follow up studies that you may explore different patient outcomes, different patient populations looking for side effects, all that sort of thing. So this is general post-marketing surveillance. So these are the main studies. In each one of these there are a multitude of different study designs and things that can take place. >>>: It says a small number of healthy people and sometimes advanced disease cases what does that mean? Michael Bates: Yes, for example if the drug was intended to treat a serious cancer. And it may be that you disease not to. And some of these cancer treatment drugs can have very serious side effects. They are very potent chemicals. So you may just use people who are at a very advanced stage. Particularly if there's no other treatment available. It would depend on the nature of the situation. But certainly some of these cancer therapeutic agents they are highly cytotoxic. You may not want to give them in small doses to healthy people. Whereas a blood pressure medication you might be happy to use relatively healthy people. Okay. So, let me talk first about the parallel design trials. These are the most common. This is the most common study design. And basically you take your eligible and willing participants and you randomize them into two or more treatment groups. Usually two but sometimes more than that. But each person, each individual person only receives one treatment. And then the comparison group either gets the current standard treatment torr they get a placebo. We'll come back to placebos. The groups are followed in a very consistent way and their outcomes are measured. So, um, we, I mentioned randomization before. So randomization is carried out at the stage of having recruited eligible and willing participants. And the contingent of the randomization is to achieve baseline comparability between the various groups. This has great benefits. Particularly in terms of equalizing the various groups. Any factors that could otherwise influence the outcome. I'm particularly talking about confounding factors. I know you haven't yet talked about confounding in this class. When you come to it, it will be much clearer. Randomization is an excellent way of eliminating confounding. The good thing about it. Often we know about particular confounding factors in our observational studies we take them into account when we carry out the data analysis in the cohort case studies. We can only take them into account if we know what they are. We can adjust for them in the multi-variate models. The great thing about randomization we don't have to know what the confounding factors are. There's always the possibility in an observational study there are unknown confounding factors which are completely influencing our results. But the great thing about randomization we simply if every person has an equal chance of getting into any of the groups then we equalize those both known and unknown factors between the groups and so they cannot influence the study outcome. If the randomization has taken place properly. Then when he can say the groups should be essentially identical except for the intervention. And the other thing is that it eliminates any sort of conscious or unconscious selection bias by either the physician or the patient. So physicians may -- they have patients and they may be more inclined to give one drug to people who have a more serious condition and another one to people that have a less serious condition. This eliminates if it's done properly it eliminates the selection bias and prevents the patient for opting for either one drug or the other or the treatment or the placebo. Of course most patients naturally do not want to be part of the placebo group. They hope they are not part of the placebo group. That's a chance they take. If they had any idea which group was which almost all of them would opt for the treatment group. Now randomization even when carried out properly, if you are only randomizing a small group, then you may not really, you may not achieve this ideal situation of having the groups identical. We'll talk about this, we'll talk about baseline comparability. So, there is a problem if you have very small groups. We have some other methods I'll talk about such as blocked randomization and stratified randomization which can help with that. The key thing is you have a very large population and you properly randomize your chances of having the groups being essentially identical is very high. If you have a small group then it decreases and is a problem. >>>: I just had a quick question. When someone says they are now doing experimental cancer treatment or experimental chemo, they are not necessarily getting the experimental chemo. They could be in the control. Michael Bates: They are in the trial. Yeah. They are in the trial. There may be two drugs being compared. >>>: Or they may be getting nothing. Michael Bates: They may be getting a placebo. Yeah. It's a possibility. >>>: Can you use a placebo. Michael Bates: We'll come back to placebos. But it would affect the statistical power. The optimal statistical power is the ability of a study given a design features including the sample size in order to detect a real effect is one is actually there. And if you have unequal group sizes, it's regarded as unbalanced and it reduces your chances of detecting an effect, a difference between the two groups. This applies to any study design you talk about including case control studies. The optimal study design is equal number of cases and controls. Sometimes in these situations you have to increase the controls to the cases because you have a limited number of cases. But in an experimental study I can't really see if you have two groups one is placebo and one is an experiment I can't see any reason to decrease the number of controls. Can you? Could you think of a reason, Art? Art Reingold: No. Michael Bates: I don't think there would be any reason. Optimally equal size. Um, so, the thing about, let's talk about confounding a little even though you haven't studied this in any formal sense. A normal clinical practice physicians they may, for example, give an antibody, say a particular antibiotic to people who have certain, may have the more severe cases. Somebody with a more milder form of condition they may give another antibiotic. So that's typical clinical practice. And the problem is if you were just to carry out an observational study and you took people who are, who received say treatment A and compared them with people who received treatment B in the normal course of clinical practice, this can lead to the two treatment groups appearing to be differently effective. It could have simply been because the tendency of the physicians to allocate treatment A to one category, say the more severely effected patients and treatment be to the less severely effected patients. So treatment A because it's given to the more severely effected patients may seem less effective. But it has been given to more severely affected participants. They may have a lower survival rate. It can completely distort the comparison. And this is referred to as confounding by indication. And in this instance the confounding factor would be the disease severity or some other factor that determined whether people got treatment A or treatment B. So the point of the randomization process is completely avoid this problem of confounding by indication to eliminate the possibility the subject of factors involved with the physician could influence this. Let me talk about some randomization methods. Starting with simple randomization which is the most common one and the most intuitively obvious one. And so, each participant should have the same chance of receiving each possible treatment. And of course by treatment I'm also referring to placebo. That's regarded as a treatment. A couple ways of randomly allocating people to one group or another. Say there's just two groups would be to use a random number table or random number generator on a computer. So basically random number tables you can get books of random numbers. Just 0 to 9, just randomly completely random. You arbitrarily would pick one point in the random number table and then start there. If it's an odd number you would give treatment A. If it's even you might give treatment B. It can be done with a similar thing, a random number generator. This will give you a completely random sequence of patients that wouldn't be influenced by any other characteristics. Completely random. But there are a number of pseudorandom allocations methods that might be used. For example, patients, the first patient might get treatment A. The second patient might get treatment B. And the third treatment A and so on. Or you could based on the day of week of allocation or the month of birth. There are all sorts of way you could potentially do this. The last digit of the hospital record number. But the problem with this is there may be some hidden bias built in there. That is out of the control of the people running the study. For example, the day of the week of allocation. It could be for example that a particular physician might say, suggest that certain patients knowingly have certain characteristics come in on a Tuesday. Tuesday is the day they give treatment B or something like that. You can imagine there are various ways this thing could be manipulated in various ways. So, generally speaking these methods, because of the possibility of some hidden and biassing factor are better to avoid. So what about, and this is a question for you? What about tossing a coin? Let's say, for example, say that a patient comes in, they are eligible and willing. And you decide it would be heads for treatment A and tails would be treatment B. What about coin tossing as a method? How would that be? Would that be a good method? >>>: If I don't get the answer I like I do best two out of three. Michael Bates: You toss the coin again. It's easy to say I made a mistake until you get the right one. The one you want. It's completely able to be manipulated by the people allocating the treatment. So you really don't want to use anything like that. Anything that's manipulable. You really need for the people running the study who are probably not the people allocating the treatment. You'll maybe have treatment centers around the country. So you have to take it completely out of their hands. So you might have say like a series of packets for one set of packets for treatment A and another set for treatment B. They are randomly ordered by the people running the study by say a random number table. Then they are numbered like 1, 2, 3, 4, 5 and so on. And then they go to the physicians who are going to provide the treatment and they just take the next one in order, in sequential order. They don't know what it is. They don't get a chance to manipulate the process. Even if they would have the best of intentions they might think well, I'd rather give them the treatment than the placebo. So, they don't have that option because all they get is, it's taken completely out of their hands and they just take the next packet which is the allocation. Treatment A or treatment B. Now that was a simple randomization. But if you are in a situation where you have a fairly small number of study participants, say you have 30 participants in a study. And, you know, it may be in the early stages or rare disease. You have 30 participants. And if you do some sort of randomized split saying a random number table and then ideally you would like 15 in each group. As I said the maximum study power comes from having equal numbers in each group. By simply taking random numbers you have some chance, 20 percent chance of getting 11 to 19 split or more uneven. 5 to 25 or anything worse than 11 to 19. This is as I said statistically inefficient. So the blocked randomization process is a very good way of ensuring you get treatment groups of equal size, of 15 each. This is the process, it's a little tricky to understand the first time through it. I'll try and take you through it reasonably slowly. You start the process with blocks. Blocks that have a number of patients that is a multiple of the number of treatment groups. For example, in this example we have two treatment groups. Treatment A and treatment B. So two groups. So we need a multiple of two groups. Multiple of two. We'll take the smallest multiple, which is four. Two by two is four. Okay. The next step is to identify all the possible permutations of A and B with equal numbers of As and Bs. So, in other words two As and two Bs. Obviously there are more permutations. We only take these with two As and two Bs. There are six alternatives. There are six possible permutations to arrange A and B in equal numbers. And then you assign the patients as they enter the trial to blocks of four. So the first four patients is a block. And then you use a process to randomly select from the six possible permutations. Randomly select from these. So say that you randomly selected BAAB and then so patient one gets B. Patients 2 and 3 get A and patient four gets B. And so if you carry this through the whole process then you will end up with an equal number of participants in each group. Does that make sense? So you'll have 15 on treatment A and 15 on treatment B or whatever the numbers happen to be. Is that clear? Feel free to say no because I find when I talk about this usually many people are not quite clear. >>>: So when you say randomly select one permutation for each block, who is doing the selecting? The patient? Michael Bates: No, not the patient. The people running the study. You don't want the patients to control it. The patients, so the patients don't all turn up in one block on one day. So, when you start the study you have to wait some period of time because they get diagnosed. They'll come in in some order and you'll basically allocate them, you will kind of organize beforehand the first block of four gets this. This one is selected for the second block of our and so on. It's all worked out in advance. It makes sure, it's all planned in advance and ordered. So you can order the packets. If you are the principal investigator and the people running the study you can set this all up in advance. So that basically the to go right through study. The 32 participants, it's divisible by four. You can have it arranged. This will insure when you have recruited your 32 participants, 16 will be in treatment A and 16 will be in treatment B. >>>: What if four walk in the door at the same moment? Michael Bates: That would be most unlikely to happen. Think of it as a rare disease. Usually it would be a rare disease when you have this situation. Unless you have a small study budget. It's most unlikely four people would walk through simultaneously. >>>: Or two people. Then there's some selection bias. Michael Bates: In that, I'm sure there's a way of discriminating who came through first and who came through second. It would be an extremely unusual circumstance. The patients usually make an appointment. They come at different times. They are not just walking into the office in a block. >>>: Okay. Michael Bates: There are different times in terms of their diagnosis and so on. I think in practice that would not be an issue. So that's the blocked randomization process. It's useful when you have a relatively small number of participants. >>>: How do you determine the block size? This instance it's two by two. If there were seven groups? Michael Bates: If there were seven groups. The thing is though, if you really only had a small number of participants it's most unlikely you would have seven groups. You would be spreading your participants too thinly. Really if you have a small number of participants it's better just to have say just two groups that you are comparing. Otherwise you have very few in each group and you wouldn't be able to make any useful comparisons between them. >>>: Blocked is only used with small groups. Michael Bates: Small total numbers of participants, yeah. If you have a very large study, you know, many participants, then it's, the unevenness of just by chance of getting a huge number in group A and a very small number in group B is very low. It's easy to show that with a big, a large sample size that you randomize. There may be a few differences between them. But if you have 3000 people say, it's going to be close to 1500 in group A and 1500 in group B. But 30, you could have an imbalance. Any other questions on that? Let's move onto stratified randomization. And it may be that you want to have sort of perhaps a balanced number of males and females, for example, in your trial. But it may be that the disease occurs more commonly in males or in females. In one group or the other. So if you just randomly, you just took random selection of patients then you might get a huge number, or relatively large number of males compared to females. But it may be that you want the study results to be potentially applicable to both males and females. So you may want to have a more balanced group in terms of the same number of males and same number of females. Or this could also be in regard to age groups. So it may be the disease occurs more commonly in elderly people. But it may also occur in younger people. So you may want to make sure you have it balanced and have your study population balanced in terms of the distribution of ages. The first step is really to define the different stratification categories. It could be strata, males and females or it could be different age strata. And then you separately select the desired number of participants from each of those strata. And the that will then give you what you want. And then it may be that you have many people in one strata. For example, the condition may occur more frequently in males. So some males who are eligible may not get to participate. You may wait a longer time to get enough women to participate, for example. >>>: Do you mean you break them up into two groups, males and females. Michael Bates: You could use the blocked randomization. If you can used the blocked randomization on top of the stratified randomization if you have small numbers. But you may not need to use the blocking if the numbers are adequate. You just want to have a balance in terms of the age groups or gender, so on, you could do this. Yes, you can combine the two. And so this is actually, I think I took this out of your book, Aschengrau. This is just a simple example eligible women stratified according to gestational age at entry. So different gestational age. And then they randomized at that point to the treatment or the placebo. This is for ***, maternal *** infant transmission. A simple example. Another method which is used to prevent human factors, subjective factors from impacting the study. I see we've reached 10 o'clock. Maybe this is a good point to stop. And I'll continue on Wednesday. (Applause)