[MUSIC] Hello everyone, this is Lea Drye and I will be picking up with the lecture on Trial Design. Before we discuss trial design, I thought I'd introduce some terminology that you're likely to hear about phases of clinical trials. So the phases of clinical trials refers to the sequence of trials that are necessary to bring a treatment into use. The terms originally came from drug development, but had been extrapolated to other types of trials. Phase one trials are the first stage in testing a new intervention in humans. They're usually small with only 10 to 30 people, and they might include healthy volunteers or those with disease. The goal of phase one trials is to identify a tolerable dose, and also to provide information on drug metabolism and excretion and really gather information on toxicities. Phase one studies are frequently not controlled. So we are not going to discuss designs for phase one studies in this class. Phase two studies are slightly larger, they usually have 30 to 100 people. And in phase two we start to collect preliminary information on efficacy, but we continue to collect information on side effects and safety. Phase two trials are sometimes controlled and sometimes uncontrolled. Phase three trials are the final approval stage for drug trials. They usually involve a 100 or more people, and the goal is to assess both efficacy and safety. Phase three trials are controlled and almost always randomized. Phase one and two are usually considered the learning phases of clinical trials, and phase three is considered the demonstration phase. You sometimes hear of phase four studies. And these are studies of a drug or device after market approval. The objective of phase four studies is to see how an intervention works in the real world, and to examine long term safety. Phase four studies are frequently observational, but sometimes they are control trials. In this lecture we are going to focus on these types of clinical trial designs, parallel designs, crossover designs, group allocation, factorial, large simple, equivalency, non-inferiority and adaptive designs. I have arranged these designs into four groups of design types that we're going to cover. These are not mutually exclusive or exhaustive design types. A specific trial may fall into one of these types or more of these types. And there are other possible trial designs that we will not discuss in this lecture. First in section A, we are going to talk about the comparison structure of a trial and the comparison structure describes the different ways that we compare an experimental group to a control group in the trial. The general types of comparison structures are parallel, crossover and group allocation. We'll start first with the parallel design. This is the design that we usually think of when we think of a clinical trial. In a parallel design, we are assigning patients and administering treatment, so the experimental and control groups in parallel. In other words, we are assigning people to both groups, over the same period of time, as opposed to collecting data on the experimental groups only, and comparing that data to historical controls, or as opposed to assigning treatment A and then assigning treatment B in series. And each person in a parallel design is designed to only one treatment group. The process by which we allocate people to a specific treatment group is usually by randomization. We use randomization to allocate patients because it removes bias in the allocation process which is called selection bias. Randomization also has the advantage of producing comparable groups with respect to known and unknown factors on average. Our statistical comparison for the parallel design, is the comparison of a summary of the outcome measures between the treatment groups. On this slide I'm going to show you a graphic depicting a parallel design. In the top box we start with the defined population or the group of people who are eligible for our trial. Then through an allocation process, usually randomization, we decide who is assigned to which treatment group. As shown here we are deciding who will be assigned to receive the new treatment versus who will be assigned to receive the current treatment. In the bottom row of boxes, we see that we will observe after some period of time, who among those assigned to new treatment has improved and who has not improved, and who among those assigned to current treatment has improved and who has not improved. We use this observation to make our comparison of efficacy and safety among the treatment groups. An example of a clinical trial with a parallel design is the National Emphysema Treatment Trial or NETT. NETT was a phase three trial conducted in the late 1990s and early 2000s. NETT enrolled about 12 hundred people with severe emphysema. If you read the NETT design papers that are referenced here at the bottom of the slide, you'll notice that NETT was originally designed to be more than twice as large, but the sample size was recalculated based on higher than expected mortality rate, and a lower than expected rate of drop ins and drop outs. The participants were randomly allocated to one of two treatment groups. The experimental treatment was a lung volume reduction surgery in addition to standard medical therapy. In lung volume reduction surgery, the most severely damaged lung tissue is removed so that the remaining lung tissue and the surrounding muscles are able to work more efficiently. Lung volume reduction surgery was not a new technique when that began, it was actually developed in the 1950s but originally the surgery had a large mortality rate and it was not much pursued as a surgical intervention. At the time of NETT lung volume reduction surgery had been resurrected with new surgical techniques, and was much safer, but the question remained as to whether or not it improved lung function in people with emphysema. The control treatment in NETT was medical therapy only. That is, people were managed by their primary care physicians following the guidelines that were proposed by the American Thoracic Society at the time, which included smoking cessation, oxygen therapy, and other therapies and medications. NETT was an unmasked trial, so there was no sham surgery in the control group. NETT was designed to test superiority, either the surgery group was superior to the control group, or the control group was superior to the surgery group. The primary outcome ws mortality and exercise capacity. And there were numerous secondary outcomes such as quality of life, the rate of symptoms, lung function and mechanics and functional capacity. There was a long period of follow up. Some of the particpants had as much as seven and a half years of follow up. The participants were recruited and followed at 17 centers in the United States, and the trial also had resource centers, such as a coordinating center and a coordinating center was here at Johns Hopkins Bloomberg School of Public Health, and a project office at NHLBI, the national heart, lung and blood institute. Now we will leave the parallel design and move onto another design called a crossover design. In a crossover design the unit that is randomized is the order in which the treatments are received, instead of whether or not the patient receives A or B. So in a crossover design we randomize whether they receive A first and then B or B and then A. And so in this case, randomization promotes balance between the treatment groups and timing of the exposure. The defining feature of our crossover design is that we're testing each treatment in all patients. That means that each patient serves as his or her own control. This is a nice feature because variability is almost always higher between measurements of an outcome taken on different people, than in repeated measurements taken on the same person. If each person serves his or her own control, we are essentially controlling for other person level characteristics that may affect outcome measurement and increase variability. As a result of the reduction in variability, we need fewer patients to test the hypothesis of interest. So the crossover design is more efficient than the comparable parallel design. On this slide, we have a graphical representation of the cross over design. Here group one is represented by a dashed line and group two is represented by a solid line. One the top left, we see the group one receives treatment A first followed by a washout period that is represented here with a line green color. And then group 1 receives treatment B. Group two receives treatment B first, followed by a washout period, and then group two receives treatment A. The crossover design is appealing because of its efficiency, however the design has many disadvantages that really limit its utility. Most importantly, only a specific kind of medical condition and treatment are appropriate for study with a crossover design. None of the treatments in the study can provide a permanent cure. If a treatment has a permanent cure, then we can't cross somebody over to the other treatment, because they've already reached the outcome. So the conditions for which we can use a crossover design are only those that have a chronic level of intensity for which the treatments provide symptomatic relief but not any permanent cure. Another concern with this design is the potential for a treatment in any early period to have effects that carry over to later periods. For instance, if I'm a person randomized to receive treatment A, and then B, I might have some effects from treatment A, that get carried over to the time period when I'm receiving treatment B. The result of this is that we need some period of time between the administrations of the treatments, to allow the effects of the treatments in the earlier periods, to subside before beginning the administration of the later treatments. That period of time is referred to as the washout period. The washout period needs to be long enough to ensure that we have no carryover effects of any of the treatments. So, this implies that the washout period has to be long enough to accommodate the treatment that has the longest potential carryover effect. Another issue that needs to be considered with a crossover is, issue of how we're going to treat people while they're in the washout period. We can actually test to see if there are any period by treatment interactions. That is, does the order of administration affect the efficacy of treatment? Is A more effective when receive second, as opposed to first? So, we are testing for the carryover effect. Test for interaction are not nearly as powerful as tests for main effects. So the test to make sure that there is no carryover effect, is not a very powerful test. Another disadvantage of the crossover design, is that dropouts can be more problematic in this design, because if you lose a participant you lose information from all treatments for that participant. The crossover design also has slightly more complicated analysis requirements than a parallel design, because you have to account for the fact that you have correlated outcomes on the individuals. So all of these limitations mean that crossover designs are feasible for the study of chronic conditions that have a constant level of intensity of the underlying disease. A condition for which you'd expect the intensity to resume, to it's regular level during the washout period between the treatment administrations. So examples of chronic diseases for which this design is used are asthma, hypertension and sometimes arthritis or other pain relief studies. The treatments in a crossover design as I mentioned must have short term effects and relieve only the signs and symptoms of the disease, but they really shouldn't have any permanent effect on the underlying disease process. Crossover designs are also used sometimes when we are in the early phases of studying a drug and we are looking at the metabolic bioavailability or tolerability of a new product. I briefly searched PubMed for some examples of recent clinical trial publications that used crossover design. In this first example, the investigators were comparing an evening dose versus a morning dose of travoprost, in an open-angle glaucoma for 24 hour intraocular pressure control. So the patients were randomized to receive either in the evening dose followed by the morning dose travoprost or vice versa. And they compared their 24 hour intraocular pressure control in the two groups. And in this study we are looking at the outcome of glaucoma, which is a chronic condition. In the second example, the investigators were comparing montelukast versus salmeterol as an adjuvant to inhaled fluticasone for exercise-induced asthma in children. So the investigators were studying add on therapies for children with asthma, which is a chronic condition, and the children were already taking fluticasone so they had a treatment to get them through those wash out periods. In the last example, we have Neuragen PN, which is a topical oil, versus placebo for neuropathic pain. And in this example, the investigators were studying chronic neuropathic pain from peripheral neuropathy, and the participants were randomized to either the neuragen oil, or a placebo oil, and then vice versa, the participants were randomized to receive either the neuragen oil first and then the placebo oil or vice versa, as an agement to their current medication regimen. Before we move on to the next design, I'd like to take the moment to discuss randomization units. The randomization unit is the level of which the randomization is applied. Usually, we're thinking the randomization unit as a person, that's what we have discussed so far, we randomize a person to receive A or B, or in the crossover design, A first and then B. But in reality it's not always the person that is the randomization unit even in a parallel design. For instance, you could randomize eyes within a person to receive A or B. In a group allocation design, the randomization unit is a whole group of individuals, such as a community, or a school, or a clinic. The entire group of individuals is allocated to the same intervention. This type of randomization is also sometimes called cluster randomization. We use cluster randomization when individual randomization is not practically feasible, or when it's taught to be unacceptable. Another complication of using individual randomization in a group setting, is contamination. For example if you're providing a behavioral intervention to several groups of school children, it will be difficult to administer the intervention to one single child in a classroom, without effecting the other children in the same classroom. In that case it might be more reasonable to randomize the entire class or the entire school to the specific intervention. It's also important to recognize that if there's correlation in the responses within a group, and there usually is, this design, the group allocation design, loses some efficiency. In other words, the group allocation design requires more individuals to address a given hypothesis, as compared to a parallel or a crossover design. In this graphic I'm going to depict the group allocation design. In the top of the graph we have groups, and in the group allocation design the groups are frequently paired based on some characteristics of the groups. So at the top we're going to start with paired groups. So we may have a pair of similar villages, or a pair of similar classrooms, and within the pair, one class is randomized to the intervention, and one class is randomized to no intervention. Then across the boxes at the bottom, we follow these groups to see whether or not they improve or not improve, and we compare the rates of improvement across the groups. In this slide I have an example of group allocation. This is a well known example at. Okay, this is a well known example with the students and faculty at John's Hopkins, this is the Sommer vitamin A trial. Alfred Sommer did a trial of vitamin A prophylaxis in an area of the world that had a high prevalence of malnutrition and vitamin A deficiency. The goal of this study was to see if Vitamin A supplements could reduce mortality in children. The population for this trial was preschool children in northern Sumatra in 1982 and 83. The treatments were Vitamin A supplementation during the study, or no supplementation during the study but Vitamin A supplementation after the study. So the control group, received supplementation after the study had been completed. The clusters for this trial were villages, there were 450 villages, and they were selected using a survey sampling method called systematic sampling. And then after the villages were selected, each one was randomly allocated to receive supplementation during or after the study. So that brings us to the end of Section A, when we come back in Section B, we'll be talking about extensions of the parallel design, which are the factorial and the large simple designs.