Interventional Studies Study Documents

PRINCIPLE OF EPIDEMIOLOGY INTERVENTIONAL STUDIES Hierarchy of Study Types Strength of evidence for causality between a risk factor and outcome Basic Trial Design Comparing Cohort Studies with Randomized Trials Interventional Study Observational Study Study group Study group Random Allocation No Allocation Group A Group B Group A Group B matching 5  can match only on variables that we know about  we can measure   we cannot match on many variables that may affect prognosis Genetics  immune status  other variables we may not even be aware of   if we match on a particular characteristic, we cannot analyze its association with the outcome because the two groups will already be identical. What distinguishes observational studies from experiments?  Ability to control for confounding Confounder Predictor Outcome can we measured all of the potential confounders?  In a prospective cohort study you can (maybe) measure all potential known confounders, but…  You can’t control for unmeasured confounders  Known  Unknown Allocating Subjects Using Randomization 9   randomization is the best approach in the design of a trial The critical element of randomization is the unpredictability of the next assignment Steps in a randomized controlled trial 1. 2. 3. Select participants Measure baseline variables Randomize   Eliminates baseline confounding Types (simple, stratified, block) Steps in a randomized controlled trial 4. Blinding the intervention  5. 6. As important as randomization Follow subjects Measure outcome   Clinically important measures Adverse events Randomized trials can be used to 12     evaluate new treatments assess new programs for screening and early detection compare different approaches to prevention evaluate new ways of organizing and delivering health services Aim 13     different therapies May compare more than two groups a new treatment compared with no treatment a new treatment compared with currently recommended regimen Selection of Subjects 14   The criteria for determining who will or will not be included in the study must be set with great precision and in writing before the study is begun. no element of subjective decision-making on the part of the investigator 15 Allocating Subjects to Treatment Groups Without Randomization   STUDIES WITHOUT COMPARISON STUDIES WITH COMPARISON  Historical Controls  Simultaneous Nonrandomized Controls STUDIES WITHOUT COMPARISON 16   case study or case series No causal inference Historical Controls 17   We could use a comparison group from the past we go back to the records of patients with the same disease who were treated before the new therapy became available problems with historical controls 18    we may set up a very meticulous system for data collection from the patients currently being treated, not their historical counterparts not comparable in kind and quality secular changes: Possible changes over calendar time (e.g., ancillary supportive therapy, living conditions, nutrition, and lifestyles Good to use 19  when a disease is uniformly fatal and a new drug becomes available, a decline in case-fatality that parallels use of the drug would strongly support the conclusion that the new drug is having an effect. Simultaneous Nonrandomized Controls 20  assign patients non randomly  by  the day of the month admitted The assignment system is predictable How is randomization accomplished? 21   computer programs manual randomization  table of random numbers  Other methods  If we randomize properly, we achieve nonpredictability of the next assignment How to implement? 22  Maintain concealment:  Prepare opaque envelopes, predetermined programs, …  Randomization performed by a separate member of research result of randomization 23     if the study is large enough and there are enough participants, we hope that randomization will increase the comparability in regard to all factors that may affect prognosis. Randomization is not a guarantee of comparability because chance may play a role if the groups are large enough and the randomization procedure is free of bias, they will tend to be similar. No guarantee for an equal number of participants in each group but with large numbers, on average the two groups will generally be comparable. 24 Hierarchy of Study Types Descriptive •Case report •Case series •Survey Analytic Observational •Cross sectional •Ecologic •Case-control •Cohort studies Strength of evidence for causality between a risk factor and outcome Experimental •Randomized controlled trials •Field Trials •Community Trials Remember 26  Randomization will make the groups comparable in terms of variables that we  recognize and can measure  may not recognize  may not be able to test now  may not be able to measure with today’s technologies  randomization cannot always guarantee comparability of the groups being studied the Main Purpose of Randomization 27     to prevent any potential biases on the part of the investigators from influencing the assignment of participants to different groups. all decisions on treatment assignment are removed from the control of the investigators. It is crucial to protect the study from any biases that might be introduced consciously or subconsciously by the investigator into the assignment process. To whatever extent it contributes to comparability, this contribution applies both to variables we can measure and to variables that we cannot measure and may not even be aware of Stratified Randomization 28    Used when we are concerned about comparability of the groups in terms of one or a few important characteristics that we strongly think may influence results Stratified Randomization can be very helpful in increasing the likelihood of comparability of the study groups we first stratify (stratum = layer) our study population by each variable that we consider important and then randomize participants to treatment groups within each stratum. 29 Data Collection on Subjects 30   Baseline characteristics TREATMENT  ASSIGNED  RECEIVED  Outcome  comparable outcome measurements in all study groups  desired effect  side effects  explicitly stated criteria for all outcomes to be measured in a study MASKING (BLINDING) 31  we want the subjects not to know which group they are assigned to  subjective  measure (e.g. self-reported severity of pain) If the patient knows that he or she is receiving a new therapy, enthusiasm and certain psychological factors on the part of the patient may operate to elicit a positive response even if the therapy itself had no positive biologic or clinical effect. Placebo for masking 32        Placebo is an inert substance that looks, tastes, and smells like the active agent use of a placebo does not automatically guarantee that the patients are masked (blinded) Some participants may try to determine whether they are taking the placebo or active drug. Use of a placebo is also important for studying the rates of side effects and reactions. the placebo plays a major role in identifying both the real benefits and its side effects In addition to blinding the subjects, we also want to mask (or blind) the observers or data collectors in regard to which group a patient is in. The masking of both participants and study personnel is called double blinding Crossover 33   planned crossover unplanned crossover. planned crossover 34         a new treatment is being compared with current treatment Subjects are randomized to new treatment or current treatment After being observed for a certain period of time on one therapy and after any changes are measured the patients are switched to the other therapy Both groups are then again observed for a certain period of time Changes in group 1 patients while they are on the new treatment can be compared with changes in these patients while they are on the current treatment Changes in group 2 patients while they are on the new treatment can also be compared with changes in these patients while they are on the current treatment each patient can serve as his or her own control This type of design is very attractive and useful with considerations:    No carryover. the observations under second therapy will be valid only if there is no residual carryover from first therapy There must be enough of a “washout period” to be sure none of first therapy remains before starting the second the planned crossover design is clearly not possible if the new therapy is surgical or if the new therapy cures the disease. 35 unplanned crossover 36 Analysis 37   according to the original assignment (called an intention to treat analysis) according to the treatment that the patients actually receive (as treated analysis) Factorial Design 38 Noncompliance 39  Patients may agree to be randomized, but following randomization they may not comply with the assigned treatment.    Whenever possible, checks on potential noncompliance are built into the study.    Overt: people may overtly articulate their refusal to comply or may stop participating in the study. These noncompliers are called dropouts covert: people may just stop taking the agent assigned without admitting this to the investigator or the study staff. E.g. urine tests for the agent being tested or for one of its metabolites. drop-ins. Patients in one group may inadvertently take the agent assigned to the other group People who do not comply or who do not participate in studies differ from those who do comply and who do participate  selection bias