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Saving Private Ryan Cultural Analysis

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Tech Broiler 1, articles. Linux and Open Source 5, articles. In practice, researchers often carry out a statistical test for balance after randomization but before analysis, presumably with the aim of taking some appropriate action if balance fails. The first table of the paper typically presents the sample means of observable covariates for the control and treatment groups, together with their differences, and tests for whether or not they are significantly different from zero, either variable by variable, or jointly. These tests are appropriate for unbiasedness if we are concerned that the random number generator might have failed, or if we are worried that the randomization is undermined by non-blinded subjects who systematically undermine the allocation.

Therefore, if the test turns out to be significant it is, by definition, a false positive. Of course, it is always good practice to look for imbalances between observed covariates in any single trial using some more appropriate distance measure, for example the normalized difference in means Imbens and Wooldridge , equation 3. Whether such imbalances should be seen as undermining the estimate of the ATE depends on our priors about which covariates are likely to be important, and how important, which is not coincidentally the same thought experiment that is routinely undertaken in observational studies when we worry about confounding. One procedure to improve balance is to adapt the design before randomization, for example, by stratification.

It has the further advantage that it allows for the exploration of different ATEs in different strata which can be useful in adapting or transporting the results to other locations see Section 2. Stratification is not possible if there are too many covariates, or if each has many values, so that there are more cells than can be filled given the sample size. With five covariates, and ten values on each, and no priors to limit the structure, we would have , possible strata.

Filling these is well beyond the sample sizes in most trials. An alternative that works more generally is to re-randomize. If the randomization gives an obvious imbalance on known covariates—treatment plots all on one side of the field, all the treatment clinics in one region, too many rich and too few poor in the control group—we try again, and keep trying until we get a balance measured as a small enough distance between the means of the observed covariates in the two groups. An alternative, widely adapted in practice, is to adjust for covariates by running a regression or covariance analysis, with the outcome on the left-hand side and the treatment dummy and the covariates as explanatory variables, including possible interactions between covariates and treatment dummies.

Freedman shows that the adjusted estimate of the ATE is biased in finite samples, with the bias depending on the correlation between the squared treatment effect and the covariates. Accepting some bias in exchange for greater precision will often make sense, though it certainly undermines any gold standard argument that relies on unbiasedness without consideration of precision.

The tension between randomization and precision that goes back to Fisher, Gosset, and Savage has been reopened in recent papers by Kasy , Banerjee et al. BCS and Banerjee et al. BCMS The trade-off between bias and precision can be formalized in several ways, for example by specifying a loss or utility function that depends on how a user is affected by deviations of the estimate of the ATE from the truth and then choosing an estimator or an experimental design that minimizes expected loss or maximizes expected utility. Of course, this requires serious and perhaps difficult thought about the mechanisms underlying the ATE, which randomization avoids.

BCMS provide a proof of a Bayesian no-randomization theorem, and BCS provide an illustration of a school administrator who has long believed that school outcomes are determined, not by school quality, but by parental background, and who can learn the most by placing deprived children in supposed high-quality schools and privileged children in supposed low-quality schools, which is the kind of study setting to which case study methodology is well attuned. As BCS note, this allocation would not persuade those with different priors, and they propose randomization as a means of satisfying skeptical observers. As this example shows, it is not always necessary to encode prior information into a set of formal prior probabilities, though thought about what we are trying to learn is always required.

Several points are important. First, the anti-randomization theorem is not a justification of any non-randomized design, for example, one that allows selection on unobservables, but only of the optimal design that is most informative. According to Chalmers and Bothwell and Podolsky , the development of randomization in medicine originated with Bradford-Hill, who used randomization in the first RCT in medicine—the streptomycin trial—because it prevented doctors selecting patients on the basis of perceived need or against perceived need, leaning over backward as it were , an argument recently echoed by Worrall Randomization serves this purpose, but so do other non-discretionary schemes; what is required is that hidden information should not be allowed to affect the allocation as would happen, for example, if subjects could choose their own assignments.

This opens up all sorts of methods of inference that are long familiar but that are excluded by pure randomization. For example, what philosophers call the hypothetico-deductive method works by using theory to make a prediction that can be taken to the data for potential falsification as in the school example above. This is the way that physicists learn, as do other researchers when they use theory to derive predictions that can be tested against the data, perhaps in an RCT, but more frequently not.

As Lakatos among others has stressed, some of the most fruitful research advances are generated by the puzzles that result when the data fail to match such theoretical predictions. In economics, good examples include the equity premium puzzle, various purchasing power parity puzzles, the Feldstein-Horioka puzzle, the consumption smoothness puzzle, the puzzle of why in India, where malnourishment is widespread, rapid income growth has been accompanied by s fall in calories consumed, and many others. Third, randomization, by ignoring prior information from theory and from covariates, is wasteful and even unethical when it unnecessarily exposes people, or unnecessarily many people, to possible harm in a risky experiment. Worrall documents the extreme case of ECMO Extracorporeal Membrane Oxygenation , a new treatment for newborns with persistent pulmonary hypertension that was developed in the s by intelligent and directed trial and error within a well-understood theory of the disease and a good understanding of how the oxygenator should work.

In early experimentation by the inventors, mortality was reduced from 80 to 20 percent. One baby received conventional therapy and died, 11 received ECMO and lived. Even so, a standard randomized controlled trial was thought necessary. With a stopping rule of four deaths, four more babies out of ten died in the control group and none of the nine who received ECMO. Fourth, the non-random methods use prior information, which is why they do better than randomization.

If prior information is not widely accepted, or is seen as non-credible by those we are seeking to persuade, we will generate more credible estimates if we do not use those priors. Indeed, this is why BCS recommend randomized designs, including in medicine and in development economics. They develop a theory of an investigator who is facing an adversarial audience who will challenge any prior information and can even potentially veto results based on it think of administrative agencies such as the FDA or journal referees.

The experimenter trades off his or her own desire for precision and preventing possible harm to subjects , which would require prior information, against the wishes of the audience, who wants nothing to do with those priors. Even then, the approval of the audience is only ex ante ; once the fully randomized experiment has been done, nothing stops critics arguing that, in fact, the randomization did not offer a fair test because important other causes were not balanced.

Among doctors who use RCTs, and especially meta-analysis, such arguments are appropriately common see Kramer We return to this topic in Section 2. Today, when the public has come to question expert prior knowledge, RCTs will flourish. In cases where there is good reason to doubt the good faith of experimenters, randomization will indeed be an appropriate response. But we believe such a simplistic approach is destructive for scientific endeavor which is not the purpose of the FDA and should be resisted as a general prescription in scientific research. Previous knowledge needs to be built on and incorporated into new knowledge, not discarded. The systematic refusal to use prior knowledge and the associated preference for RCTs are recipes for preventing cumulative scientific progress.

In the end, it is also self-defeating. To quote Rodrik D. Modern work calculates standard errors allowing for the possibility that residual variances may be different in the treatment and control groups, usually by clustering the standard errors, which is equivalent to the familiar two sample standard error in the case with no covariates. Statistical inference is done with t -values in the usual way. Unfortunately, these procedures do not always give the right standard errors and, to reiterate, the value of randomization is that it permits inference about estimates of ATEs, not that it guarantees the quality of these estimates, so credible standard errors are essential in any argument for RCTs. In many observational studies, researchers are prepared to make more assumptions on functional forms or on distributions, and for that price we are able to identify other quantities of interest.

Without these assumptions, inferences must be based on the difference in the two means, a statistic that is sometimes ill-behaved, as we discuss below. This ill-behavior has nothing to do with RCTs, per se, but within RCTs, and their minimal assumptions, we cannot easily switch from the mean to some other quantity of interest. By tabulating all possible combinations of treatments and controls in our trial sample, and the ATE associated with each, we can calculate the exact distribution of the estimated ATE under the null. This allows us to calculate the probability of calculating an estimate as large as our actual estimate when the treatment has no effect. This randomization test requires a finite sample, but it will work for any sample size see Imbens and Wooldridge for an excellent account of the procedure.

Randomization inference can be used to test the null hypotheses that all of the treatment effects are zero, as in the above example, but it cannot be used to test the hypothesis that the average treatment effect is zero, which will often be of interest. In agricultural trials, and in medicine, the stronger sharp hypothesis that the treatment has no effect whatever is often of interest. In many public health applications, we are content with improving average health, and in economic applications that involve money, such as welfare experiments or cost-benefit analyses, we are interested in whether the net effect of the treatment is positive or negative, and in these cases, randomization inference cannot be used. None of which argues against its wider use in social sciences when appropriate.

In cases where randomization inference cannot be used, we must construct tests for the differences in two means. Standard procedures will often work well, but there are two potential pitfalls. The second problem, which is much harder to address, occurs when the distribution of treatment effects is not symmetric Bahadur and Savage Neither pitfall is specific to RCTs, but RCTs force us to work with means in estimating treatment effects and, with only a few exceptions in the literature, social scientists who use RCTs appear to be unaware of the difficulties. In the simple case of comparing two means in an RCT, inference is usually based on the two—sample t —statistic which is computed by dividing the ATE by the estimated standard error whose square is given by.

In extreme cases, when one of the variances is zero, the t —statistic has effective degrees of freedom half of that of the nominal degrees of freedom, so that the test-statistic has thicker tails than allowed for, and there will be too many rejections when the null is true. Young argues that this problem is worse when the trial results are analyzed by regressing outcomes not only on the treatment dummy but also on additional covariates and when using clustered or robust standard errors. When the design matrix is such that the maximal influence is large, which is likely if the distribution of the covariates is skewed so that for some observations outcomes have large influence on their own predicted values, there is a reduction in the effective degrees of freedom for the t —value s of the average treatment effect s leading to spurious findings of significance.

In 30 to 40 percent of the estimated treatment effects in individual equations with coefficients that are reported as significant, he cannot reject the null of no effect for any observation; the fraction of spuriously significant results increases further when he simultaneously tests for all results in each paper. These spurious findings come in part from issues of multiple-hypothesis testing, both within regressions with several treatments and across regressions. Within regressions, treatments are largely orthogonal, but authors tend to emphasize significant t —values even when the corresponding F -tests are insignificant. At the same time, the pervasiveness of observations with high influence generates spurious significance on its own.

These issues are now being taken more seriously, at least in economics. Yet it remains the case that many of the results reported in the literature are spuriously significant. Spurious significance also arises when the distribution of treatment effects contains outliers or, more generally, is not symmetric. Standard t —tests break down in distributions with enough skewness see Lehmann and Romano , —8. How difficult is it to maintain symmetry? And how badly is inference affected when the distribution of treatment effects is not symmetric? One important example is expenditures on healthcare. Most people have zero expenditure in any given period, but among those who do incur expenditures, a few individuals spend huge amounts that account for a large share of the total.

Indeed, in the famous Rand health experiment see Manning, et al. The authors realize that the comparison of means across treatment arms is fragile, and, although they do not see their problem exactly as described here, they obtain their preferred estimates using an approach that is explicitly designed to model the skewness of expenditures. Another example comes from economics, where many trials have outcomes valued in money. Does an anti-poverty innovation—for example microfinance—increase the incomes of the participants? Income itself is not symmetrically distributed, and this might also be true of the treatment effects if there are a few people who are talented but credit-constrained entrepreneurs and who have treatment effects that are large and positive, while the vast majority of borrowers fritter away their loans, or at best make positive but modest profits.

A recent summary of the literature is consistent with this see Banerjee, Karlan, and Zinman In some cases, it will be appropriate to deal with outliers by trimming, transforming, or eliminating observations that have large effects on the estimates. But if the experiment is a project evaluation designed to estimate the net benefits of a policy, the elimination of genuine outliers, as in the Rand Health Experiment, will vitiate the analysis. It is precisely the outliers that make or break the program. Transformations, such as taking logarithms, may help to produce symmetry, but they change the nature of the question being asked; a cost benefit analysis or healthcare reform costing must be done in dollars, not log dollars.

We consider an example that illustrates what can happen in a realistic but simplified case; the full results are reported in the Appendix. The parent population mean of the treatment effects is zero, but there is a long tail of positive values; we use a left-shifted lognormal distribution. This could be a healthcare expenditure trial or a microfinance trial, where there is a long positive tail of rare individuals who incur very high costs or who can do amazing things with credit while most people cost nothing in the period studied or cannot use the credit effectively. A trial sample of 2 n individuals is randomly drawn from the parent population and is randomly split between n treatments and n controls.

These rejections come from two separate issues, both of which are relevant in practice: a that the ATE in the trial sample differs from the ATE in the parent population of interest, and b that the t —values are not distributed as t in the presence of outliers. The problem cases are when the trial sample happens to contain one or more outliers, something that is always a risk given the long positive tail of the parent distribution. When this happens, everything depends on whether the outlier is among the treatments or the controls; in effect, the outliers become the sample, reducing the effective number of degrees of freedom.

In extreme cases, one of which is illustrated in Figure A. When the outlier is in the treatment group, the dispersion across outcomes is large, as is the estimated standard error, and so those outcomes rarely reject the null using the standard table of t —values. The over-rejections come from cases when the outlier is in the control group, the outcomes are not so dispersed, and the t —values can be large, negative, and significant. While these cases of bimodal distributions may not be common and depend on the existence of large outliers, they illustrate the process that generates the over-rejections and spurious significance.

Note that there is no remedy through randomization inference here, given that our interest is in the hypothesis that the average treatment effect is zero. Our reading of the literature on RCTs in social and public health policy areas suggests that they are not exempt from these concerns. Many trials are run on sometimes very small samples, they have treatment effects where asymmetry is hard to rule out—especially when the outcomes are in money—and they often give results that are puzzling, or at least not easily interpreted theoretically. In the context of development studies, neither Banerjee and Duflo nor Karlan and Appel , who cite many RCTs, raise concerns about misleading inference, implicitly treating all results as reliable.

Some of these results contradict standard theory. No doubt there are behaviors in the world that are inconsistent with conventional economics, and some can be explained by standard biases in behavioral economics, but it would also be good to be suspicious of the significance tests before accepting that an unexpected finding is well-supported and that theory must be revised. Replication of results in different settings may be helpful, if they are the right kind of places see our discussion in Section 2. This, then, replicates the spurious findings.

It is of great importance to note that randomization, by itself, is not sufficient to guarantee unbiasedness if post-randomization differences are permitted to affect the two groups. The difficulty of controlling for placebo effects can be especially acute in testing medical interventions see Howick , Chapter 7 for a critical review , as is the difficulty in controlling both for placebo effects and the effects of therapist variables in testing psychological therapies. For instance, Pitman, et al. Many social and economic trials, medical trials, and public health trials are not blinded nor sufficiently controlled for other sources of bias, and indeed many cannot be, and a sufficient defense is rarely offered that unbiasedness is not undermined.

Generally, it is recommended to extend blinding beyond participants and investigators to include those who measure outcomes and those who analyze the data, all of whom may be affected by both conscious and unconscious bias. The need for blinding in those who assess outcomes is particularly important in cases where outcomes are not determined by strictly prescribed procedures whose application is transparent and checkable but requires elements of judgment. In many cases it is reasonable to suppose that people choose to participate if it is in their interest to do so. In consequence, those who estimate consciously or unconsciously that their gain is not high enough to offset the perceived drawbacks of compliance with the treatment protocol may avoid it.

This is not to say that one should assume without argument that non-blinding at any point will introduce bias. That is a matter to be assessed case-by-case. But the contrary cannot be automatically assumed. This brings to the fore the trade-off between using an RCT-based estimate that may well be biased, and in ways we do not have good ideas how to deal with, versus one from an observational study where blinding may have been easier, or some of these sources of bias may be missing or where we may have a better understanding of how to correct for them.

For instance, blinding is sometimes automatic in observational studies, e. See for example Horwitz et al. Lack of blinding is not the only source of post-randomization bias. Subsequent treatment decisions can differ, and treatments and controls may be handled in different places, or by differently trained practitioners, or at different times of day, and these differences can bring with them systematic differences in the other causes to which the two groups are exposed. These can, and should, be guarded against. But doing so requires an understanding of what these causally relevant factors might be. What do the arguments of this section mean about the importance of randomization and the interpretation that should be given to an estimated ATE from a randomized trial?

First, we should be sure that an unbiased estimate of an ATE for the trial population is likely to be useful enough to warrant the costs of running the trial. Second, since randomization does not ensure orthogonality, to conclude that an estimate is unbiased, warrant is required that there are no significant post-randomization correlates with the treatment. Third, the inference problems reviewed here cannot just be presumed away. When there is substantial heterogeneity, the ATE in the trial sample can be quite different from the ATE in the population of interest, even if the trial is randomly selected from that population; in practice, the relationship between the trial sample and the population is often obscure see Longford and Nelder Fourth, beyond that, in many case the statistical inference will be fine, but serious attention should be given to the possibility that there are outliers in treatment effects, something that knowledge of the problem can suggest and where inspection of the marginal distributions of treatments and controls may be informative.

For example, if both are symmetric, it seems unlikely though certainly not impossible that the treatment effects are highly skewed. Measures to deal with Fisher-Behrens should be used and randomization inference considered when appropriate to the hypothesis of interest. All of this can be regarded as recommendations for improvement to current practice, not a challenge to it. More fundamentally, we strongly contest the often-expressed idea that the ATE calculated from an RCT is automatically reliable, that randomization automatically controls for unobservables, or worst of all, that the calculated ATE is true.

If, by chance, it is close to the truth, the truth we are referring to is the truth in the trial sample only. To make any inference beyond that requires arguments of the kind we consider in the next section. We have also argued that, depending on what we are trying to measure and what we want to use that measure for, there is no presumption that an RCT is the best means of estimating it. That too requires an argument, not a presumption. Suppose we have estimated an ATE from a well-conducted RCT on a trial sample, and our standard error gives us reason to believe that the effect did not come about by chance. We thus have good warrant that the treatment causes the effect in our trial sample, up to the limits of statistical inference.

What are such findings good for? The literature discussing RCTs has paid more attention to obtaining results than to considering what can justifiably be done with them. There is insufficient theoretical and empirical work to guide us how and for what purposes to use the findings. What there is tends to focus on the conditions under which the same results hold outside of the original settings or how they might be adapted for use elsewhere, with almost no attention to how they might be used for formulating, testing, understanding, or probing hypotheses beyond the immediate relation between the treatment and the outcome investigated in the study. Yet it cannot be that knowing how to use results is less important than knowing how to demonstrate them.

Any chain of evidence is only as strong as it weakest link, so that a rigorously established effect whose applicability is justified by a loose declaration of simile warrants little. If trials are to be useful, we need paths to their use that are as carefully constructed as are the trials themselves. The invariance assumption is often made in medicine, for example, where it is sometimes plausible that a particular procedure or drug works the same way everywhere, though its effects cannot be the same at all stages of the disease. More generally, Horton gives a strong dissent and Rothwell provides arguments on both sides of the question. We should also note the recent movement to ensure that testing of drugs includes women and minorities because members of those groups suppose that the results of trials on mostly healthy young white males do not apply to them, as well as the increasing call for pragmatic trials, as in Williams et al.

Our approach to the use of RCT results is based on the observation that whether, and in what ways, an RCT result is evidence depends on exactly what the hypothesis is for which the result is supposed to be evidence, and that what kinds of hypotheses these will be depends on the purposes to be served. This should in turn affect the design of the trial itself. This list is hardly exhaustive. We noted in Section 1. For example, at the Federal level in the US, prospective policies are vetted by the non-partisan Congressional Budget Office CBO , which makes its own estimates of budgetary implications.

Ideologues whose programs are scored poorly by the CBO have an incentive to support an RCT, not to convince themselves, but to convince opponents. Once again, RCTs are valuable when your opponents do not share your prior. Suppose a trial has probabilistically established a result in a specific setting. External validity may refer just to the replication of the causal connection or go further and require replication of the magnitude of the ATE.

Either way, the result holds—everywhere, or widely, or in some specific elsewhere—or it does not. This binary concept of external validity is often unhelpful because it asks the results of an RCT to satisfy a condition that is neither necessary nor sufficient for trials to be useful, and so both overstates and understates their value. It directs us toward simple extrapolation —whether the same result holds elsewhere—or simple generalization —it holds universally or at least widely—and away from more complex but equally useful applications of the results. The failure of external validity interpreted as simple generalization or extrapolation says little about the value of the results of the trial. There are several uses of RCTs that do not require applying their results beyond the original context; we discuss these in Section 2.

Beyond that, there are often good reasons to expect that the results from a well-conducted, informative, and potentially useful RCT will not apply elsewhere in any simple way. Without further understanding and analysis, even successful replication tells us little either for or against simple generalization nor does much to support the conclusion that the next will work in the same way. Nor do failures of replication make the original result useless. We often learn much from coming to understand why replication failed and can use that knowledge in looking for how the factors that caused the original result might operate differently in different settings.

Third, and particularly important for scientific progress, the RCT result can be incorporated into a network of evidence and hypotheses that test or explore claims that look very different from the results reported from the RCT. We shall give examples below of valuable uses for RCTs that are not externally valid in the usual sense that their results do not hold elsewhere, whether in a specific target setting or in the more sweeping sense of holding everywhere, or everywhere in some specified domain. It was originally designed to test whether more generous insurance causes people to use more medical care and, if so, by how much. According to Aron-Dine et al. Ironically, they argue that the estimate cannot be replicated in recent studies, and that it is unclear that it is firmly based on the original evidence.

The simple direct exportability of the result was perhaps illusory. At its most ambitious, this aims for universal reach. Simple extrapolation is often used to move RCT results from one setting to another. For example, Improving Student Participation--Which programs most effectively get children into school? What can we conclude from such comparisons? A philanthropic donor interested in education, who assumes that marginal and average effects are the same, might learn that the best place to devote a marginal dollar is in Kenya, where it would be used for deworming. What does J-PAL conclude? Eliminating small costs can have substantial impacts on school participation.

It is certainly true in a logical sense that if a program has achieved a given result, then it can do so. Trials, as is widely noted, often take place in artificial environments which raises well recognized problems for extrapolation. But it gives short shrift to cross-site variation in the size of ATEs, which also play a key part in the calculations of cost effectiveness. The manual briefly notes that diminishing returns or the last-mile problem might be important in theory but argues that the baseline levels of outcomes are likely to be similar in the pilot and replication areas, so that the ATE can be safely assumed to apply as is.

All of this lacks a justification for extrapolating results, some understanding of when results can be extrapolated, when they cannot, or better still, how they should be modified to make them applicable in a new setting. Without well substantiated assumptions to support the projection of results, this is just induction by simple enumeration—swan 1 is white, swan 2 is white, …, so all swans are white; and, as Francis Bacon , 1. The bird infers, on repeated evidence, that when the farmer comes in the morning, he feeds her. The inference serves her well until Christmas morning, when he wrings her neck and serves her for dinner.

Though this chicken did not base her inference on an RCT, had we constructed one for her, we would have obtained the same result that she did. Her problem was not her methodology, but rather that she did not understand the social and economic structure that gave rise to the causal relations that she observed. We shall return to the importance of the underlying structure for understanding what causal pathways are likely and what are unlikely below. Our argument here is that evidence from RCTs is not automatically simply generalizable, and that its superior internal validity, if and when it exists, does not provide it with any unique invariance across context.

That simple extrapolation and simple generalization are far from automatic also tells us why even ideal RCTs of similar interventions give different answers in different settings and the results of large RCTs may differ from the results of meta-analyses on the same treatment as in LeLorier et al. Such differences do not necessarily reflect methodological failings and will hold across perfectly executed RCTs just as they do across observational studies. Our arguments are not meant to suggest that extrapolation or even generalization is never reasonable. For instance, conditional cash transfers have worked for a variety of different outcomes in different places; they are often cited as a leading example of how an evaluation with strong internal validity leads to a rapid spread of the policy.

Think through the causal chain that is required for CCTs to be successful: People must like money, they must like or do not object too much to their children being educated and vaccinated, there must exist schools and clinics that are close enough and well enough staffed to do their job, and the government or agency that is running the scheme must care about the wellbeing of families and their children.

Levy , nor in places where people strongly oppose education or vaccination. So, there are structural reasons why CCT results export where they do. To summarize. Establishing causality does nothing in and of itself to guarantee that the causal relation will hold in some new case, let alone in general. Nor does the ability of an ideal RCT to eliminate bias from selection or from omitted variables mean that the resulting ATE from the trial sample will apply anywhere else.

The issue is worth mentioning only because of the enormous weight that is currently attached to policing the rigor with which causal claims are established by contrast with the rigor devoted to all those further claims—often unstated even—that go into warranting extrapolating or generalizing the relations. What Mackie called INUS causality Insufficient but Non-redundant parts of a condition that is itself Unnecessary but Sufficient for a contribution to the outcome is the kind of causality reflected in equation 1.

A standard example is a house burning down because the television was left on, although televisions do not operate in this way without support factors, such as wiring faults, the presence of tinder, and so on. This becomes clear if we rewrite 1 in the form. These are however just the kind of factors that are likely to be differently distributed in different populations. Both costs and effect sizes can be expected to differ in new settings, just as they have in observed ones, making these predictions difficult.

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