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Reading Notes- Chapter 8

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York University
PSYC 2030
Krista Phillips

Chapter 8: Nonrandomized Research and Causal Reasoning How is Causal Reasoning Attempted in the Absence of Randomization?  Randomized controlled experiments are not always possible  Prospective data – (prospective = of or in the future), collecting data by following your reaction forward in time (i.e. Dog bite, you get tetnis shot, request to have it in same arm as dog bite so you can have use of other arm, doctor needs to separate possible reactions from tetnis shot so does it in good arm, wouldn’t be able to tell if swelling is from dog bite or from reaction to medicine) – this is example of simplest single-case experiment  Prospective data often used in longitudinal research, defining characteristic of which is that individuals are observed and measured repeatedly through time.  Framingham Heart Study (longitudinal observational investigating that was started by the U.S Public Health Service in the 1940s.  Retrospective data – data that are collected back in time (i.e. fast food data chart, shows what many people ate – past tense, and which of them got food poisoning)  If epidemiologist worked with this data, all you’d have to go with is the covariation between the food they ate (X) and whether or not they got food poisoning (Y) and temporal precedence (i.e. Retrospective information on what each person said they had eaten.)  Challenge would then be to try to emulate the casual reasoning of Mill’s Methods in order to arrive at causal hypotheses that are as sound as possible within the limitations of the retrospective database  Could look at the possibilities of certain things in table getting people sick, but some people ate it that got sick, others that did not get sick ate it too… could have been different dressing on each salad? Different carton of milk for each milkshake, etc.? What’s more intriguing though is that everyone who reported eating a rare hamburger got sick; no one did not get sick that ate one.  Consider how bacteria may not have been killed in a rare hamburger – this seems to be the surface cause  What if owner tells us that someone working in the kitchen was sick that same day and suppose the food handler touched some but not all of the foods that same day  Eventually food handler can be ruled out, we know he touched more foods than only what was listed and not everyone got sick, or maybe they did but did not report, but still.  Only the rare hamburger was absent in every case that did not involve food poisoning, so on the basis of the available retrospective data, we suspect that the rare hamburger was the necessary and sufficient condition (X) that brought about food poisoning (Y).  Perhaps there are other variables between X and Y but there is not enough information to explore that possibility How Is the Third Variable Problem Relevant?  Causality implies correlation, as causality entails the covariation of the presumed cause (X) and the presumed effect (Y). Finding that relationship, that they covary, does not explain why they’re related  Besides variation and temporal precedence (that X precedes Y), another requirement of casual inference is the exclusion of plausible rival explanations of the covarying relationship between X and Y.  Third-variable problem – concept of a rival explanation – third variable that is correlated with both X and Y could cause X and Y to covary o I.e. Paulos’s example of high correlation between sizes of children’s feet and their spelling abilities. However, as children grow their spelling abilities would often tend to get better and their feet get bigger – third variable responsible: age o Age is correlated with both X and Y and can account for the correlation between them.  Supposed there’s an outbreak of health related symptoms in people – time is of the essence. We discover most of those people with symptoms were ill prior to the symptoms and were prescribed a new drug. We suspect that the new drug’s side effects are causing the new symptoms  Randomized research: could take a sample of asymptomatic people, give half a placebo, half the new drug – cannot do this, cannot ethically expose people to a potentially harmful drug  Nonrandomized research: could track down people who were diagnose with the original illness and separate from that group the patients who were prescribed the new drug  We then compare the two groups  If only those given the new drug experience those new strange symptoms, the new drug would seem to be more seriously implicated as the causal agent  However, it’s causal role is not yet fully established because patients given the new drug may differ on some unknown variable, a third variable, from those not given the drug  As we would think of rival hypotheses in randomized experiments (threats to internal validity), we think it is plausible that not the new drug but an unknown correlate of being given the new drug might be the causal variable  Suppose we find not all patients who took the new drug were given the same dosage levels – correlate dosage level with outcome variable?  If patients on larger dosages suffer more severely with the strange new medical symptoms, would this evidence clearly implicate the drug more strongly as the cause of those symptoms? – same answer as above, still cannot be sure of causal role, those given higher dose may have been more severely ill initially  We wonder whether the severity of the illness for which the different dosages of the drug were prescribed, rather than the drug itself – could be third variable  To establish temporal precedence, we need to show that taking new drug preceded the strange new medical symptoms  Unless medical records go back far enough, might not be able to prove that the symptoms did not occur until after the drug was taken  Covariation assumption requires us to show that the new drug is related to the strange new medical symptoms, even if we can though, it might be argued that in order to be susceptible to the drug a patient already had to be in a given state of distress  According to this argument, it was not the new drug, or maybe not only the new drug, that was related to strange symptoms  If patients who were in state of distress were only ones given new drug, it is possible that the state of the patients’ distress determined the particular group in which they found themselves  Might still be convinced by strong circumstantial, though inconclusive, correlation evidence  If patients who had been taking the new drug were more likely to display the strange new medical symptoms, if those taking more of the new drug displayed more of the strange symptoms, and if those taking it over a longer period of time also displayed more of the strange symptoms, we would be reluctant to conclude that the new drug was not the cause of the symptoms.  Even if we were unwilling to state that the new drug was definitely at the root of the strange symptoms, at least on the basis of the type of correlational evidence outlined above, it might be prudent to act as though it were  On this basis we might think about designing a randomized experiment using an animal model (primates for example), to simulate the strange medical symptoms, because we now have a causal model with which to work – failure to produce symptoms in primate would not rule out the causal relationship in human patients What Is Meant By Sub classification on Propensity Scores?  Last chapter, alluded to family of nonrandomized designs called nonequivalent-group designs.  They traditionally take form of between-subjects designs in which the sampling units (subjects, groups), are allocated to the experimental and control groups by means other than randomization and are also observed or tested before and after the experimental intervention  Imagine we want to investigate a new therapy for treating hyperactive children  If it were a randomized experiment, we would use an unbiased procedure to assign the hyperactive children to the experimental treatment and control group  Supposed circumstances beyond our control dictate that we must use two intact groups of children: one group at School A and the other at School B  We could flip a coin to decide which school will be experimental group, but we are unable to allocate children within each school to the two groups  Assuming they were observed and measured both at the beginning and the end of the study the nonrandomized design can be diagrammed as follows: School A NR O X O School B NR O O  X= treatment or intervention, O= observation or measurement, and NR = nonrandomized allocation of sampling units to conditions  One potentially significant problem: children in school A may be different from those in School B in a basic way that systematically biases the results when we compare one intact group (from school A) with another intact group (from school B)  The general nature of this problem was recognized by Iowa State University statistician. E.F. Lindquist who called it “Type G Error” (group error)  It means that relevant extraneous factors exist that are characteristic of the group from School A but uncharacteristic of the group from School B.  Group from School A might have been assigned to better teachers, or the home lives of most of the group from one school might be more supportive than those from the other school and so on  Much less has been written about these nonequivalent groups designs by the Campbell group of methodologists and we will described an innovative statistical way of improving this situation when sample sizes are large enough and there are relevant subgroups that are also well stocked with sampling units  This procedure of sub classification on propensity scores, reduces all of the variable on which the treated and untreated sampling units differ to a single composite variable  This composite variable called propensity score, is a summary statistic of all the differences on all variables on which the treated and untreated units differ  The procedure requires a computer program and the technical details are beyond the scope of this book  I.e. Example table, it shows that in the states, death of non smokers is equivalent to death of smokers, which would suggest that smoking is not detrimental to health – which we know is untrue  Part B of the table shows substantial discrepancies in the average age of each subpopulation – because age and mortality are correlated, age in this example is a confounding variable  We would need to adjust for the average differences in age before reaching any conclusions about death rates of nonsmokers (N), cigarette smokers (C), and cigar and pipe smokers (CP)  An adjustment for age would subdivide each subpopulation into age categories of roughly equal size  Next step would compare the death rates within the age categories  Final step would be adjusting the death rates by averaging over the age-group-specific comparisons in order to get overall estimates of the death rates  Part C of this table shows the final results of this sub classification-on-propensity scores analysis.  In this case, the adjusted death rates were based on dividing the subpopulations into nine or more subcategories of roughly equal size  Now we see very clearly that the death rate was actually consistently highest among the cigarette smokers and lowest in the nonsmoking U.S. database and lowest in the cigar and pipe smoking Canadian and United Kingdom database.  Although the procedure required a technically complex analysis, its beauty was that it corrected for the statistical artifacts in the original nonequivalent groups Box 8.1 Wit-List Controls  If researcher cannot use random assignment in case due to concerns about depriving the control group of the experimental treatment, the researcher might propose a randomized design with a wait-list control group.  Such a design can also have other benefits.  Here is an example of a wait-list control group: Group 1 R O X O O Group 2 R O O X O  R= random allocation of participants to groups or treatment conditions, O= observation or measurement, and X= treatment or intervention  Those participants assigned to group 1 receive experimental treatment (X) at beginning of study, and assuming the treatment is found to be beneficial, those assigned to group 3, the control condition, are later given an opportunity to receive the treatment once the beneficial result is observed  If we measure group 1 after the treatment and again after group 2 receives it, and we compare the results with those in group 2, a further benefit of the design is that we have information about the immediate and delayed effect of the treatments as well as a replication of the immediate effect What Are Time-Series Designs and “Found Experiments”?  In time-series designs, the defining characteristic is the study of variation across some dimension over time  When effects of some intervention or treatment are inferred from a comparison of the outcome measure obtained at different time intervals before and after the interventions the data structure is called an interrupted time-series design  The term time series means there is a data point for each point in time, and an interrupted time series means there is a dividing lines at the beginning of the intervention (a line analogous to the start of treatment)  Ex. Gottman described how certain cycles of social behavior might be studied in the context of a time series design  He mentioned earlier work by Kendon showing that when two people converse there are cycles of gazing and averting gazing at one another as a function of who is speaking  The person who begins speaking has a tendency to look away from the listener and then increase eye-to-eye contact toward the end of the speech, which is an implicit signal for the listening to begin looking away and speaking  This cycle, Gottman thought, is suggestive of cycles of sine and cosine waves  Another ex of cycles is regular repetitions of brain waves when people are awake, drowsy, or in different stages of sleep  Statistical analysis of time-series designs has its own terminology and can be quite complex  Simplified application that was inspired by work of sociologist David P. Phillips  He referred to his studies as “found experiments” because they were essentially found or discovered in naturally occurring situations  In one set of studies, Phillips explored the clustering of imitative suicides after a series of televised news stories and televised movies about suicide  The variations in the results were difficult to explain  Ex. NYC study found that teenage suicides had increased after three televised fictional films about suicide but a follow-up study done in California and Pennsylvania did not find an increase in teenage suicides after the same three films were televise  In another study, conducted in Austria, Phillips and carstensen reported evidence of what appeared to be copycat imitations of suicides in news stories  In Vienna, A
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