RESEARCH DESIGNS AND DIAGNOSANDS

We present a general description of a research design as the specification of a problem and a strategy to answer it. We build on two influential research design frameworks. King, Keohane, and Verba (Reference King, Keohane and Verba1994, 13) enumerate four components of a research design: a theory, a research question, data, and an approach to using the data. Geddes (Reference Geddes2003) articulates the links between theory formation, research question formulation, case selection and coding strategies, and strategies for case comparison and inference. In both cases, the set of components are closely aligned to those in the framework we propose. In our exposition, we also employ elements from Pearl’s (Reference Pearl2009) approach to structural modeling, which provides a syntax for mapping design inputs to design outputs as well as the potential outcomes framework as presented, for example, in Imbens and Rubin (Reference Imbens and Rubin2015), which many social scientists use to clarify their inferential targets. We characterize the design problem at a high level of generality with the central focus being on the relationship between questions and answer strategies. We further situate the framework within existing literature below.

Choice of Diagnosands

What diagnosands should researchers choose? Although researchers commonly focus on statistical power, a larger range of diagnosands can be examined and may provide more informative diagnoses of design quality. We list and describe some of these in Table 1, indicating for each the design information that is required in order to calculate them.

TABLE 1. Examples of Diagnosands and the Elements of the Model (M), Inquiry (I), Data Strategy (D), and Answer Strategy (A) Required in Order for a Design to be Diagnosand-Complete for Each Diagnosand

The set listed here includes many canonical diagnosands used in classical quantitative analyses. Diagnosands can also be defined for design properties that are often discussed informally but rarely subjected to formal investigation. For example one might define an inference as “robust” if the same inference is made under different analysis strategies. One might conclude that an intervention gives “value for money” if estimates are of a certain size and be interested in the probability that a researcher in correct in concluding that an intervention provides value for money.

We believe there is not yet a consensus around diagnosands for qualitative designs. However, in certain treatments clear analogues of diagnosands exist, such as sampling bias or estimation bias (e.g., Herron and Quinn Reference Herron and Quinn2016). There are indeed notions of power, coverage, and consistency for QCA researchers (e.g., Baumgartner and Thiem Reference Baumgartner and Thiem2017; Rohlfing Reference Rohlfing2018) and concerns around correct identification of causes of effects, or of causal pathways, for scholars using process-tracing (e.g., Bennett Reference Bennett, Bennett and Checkel2015; Fairfield and Charman Reference Fairfield and Charman2017; Humphreys and Jacobs Reference Humphreys and Jacobs2015; Mahoney Reference Mahoney2012).

Though many of these diagnosands are familiar to scholars using frequentist approaches, analogous diagnosands can be used to assess Bayesian estimation strategies (see Rubin Reference Rubin1984), and as we illustrate below, some diagnosands are unique to Bayesian answer strategies.

Given that there are many possible diagnosands, the overall evaluation of a design is both multi-dimensional and qualitative. For some diagnosands, quality thresholds have been established through common practice, such as the standard power target of 0.80. Some researchers are unsatisfied unless the “bias” diagnosand is exactly zero. Yet for most diagnosands, we only have a sense of better and worse, and improving one can mean hurting another, as in the classic bias-variance tradeoff. Our goal is not to dichotomize designs into high and low quality, but instead to facilitate the assessment of design quality on dimensions important to researchers.

EXISTING APPROACHES TO LEARNING ABOUT RESEARCH DESIGNS

Much quantitative research design advice focuses on one aspect of design at a time, rather than on the ways in which multiple components of a research design relate to each other. Statistics articles and textbooks tend to focus on a specific class of estimators (Angrist and Pischke Reference Angrist and Pischke2008; Imbens and Rubin Reference Imbens and Rubin2015; Rosenbaum Reference Rosenbaum2002), set of estimands (Heckman, Urzua, and Vytlacil Reference Heckman, Urzua and Vytlacil2006; Imai, King, and Stuart Reference Imai, King and Stuart2008; Deaton Reference Deaton2010; Imbens Reference Imbens2010), data collection strategies (Lohr Reference Lohr2010), or ways of thinking about data-generation models (Gelman and Hill Reference Gelman and Hill2006; Pearl Reference Pearl2009). In Shadish, Cook, and Campbell (Reference Shadish, Cook and Campbell2002, 156), for example, the “elements of a design” consist of “assignment, measurement, comparison groups and treatments,” a definition that does not include questions of interest or estimation strategies. In some instances, quantitative researchers do present multiple elements of research design. Gerber and Green (Reference Gerber and Green2012), for example, examine data-generating models, estimands, assignment and sampling strategies, and estimators for use in experimental causal inference; and Shadish, Cook, and Campbell (Reference Shadish, Cook and Campbell2002) and Dunning (Reference Dunning2012) similarly describe the various aspects of designing quasi-experimental research and exploiting natural experiments.

In contrast, a number of qualitative treatments focus on integrating the many stages of a research design, from theory generation, to case selection, measurement, and inference. In an influential book on mixed method research design for comparative politics, for example, Geddes (Reference Geddes2003) articulates the links between theory formation (M), research question formulation (I), case selection and coding strategies (D), and strategies for case comparison and inference (A). King, Keohane, and Verba (Reference King, Keohane and Verba1994) and the ensuing discussion in Brady and Collier (Reference Brady and Collier2010) highlight how alternative qualitative strategies present tradeoffs in terms of diagnosands such as bias and generalizability. However, few of these texts investigate those diagnosands formally in order to measure the size of the tradeoffs between alternative qualitative strategies.^{Footnote 4} Qualitative approaches, including process tracing and qualitative comparative analysis, sometimes appear almost hermetic, complete with specific epistemologies, types of research questions, modes of data gathering, and analysis. Though integrated, these strategies are often not formalized. And if they are, it is seldom in a way that enables comparison with other approaches or quantification of design tradeoffs.

MIDA represents an attempt to thread the needle between these two traditions. Quantifying the strength of designs necessitates a language for formally describing the essential features of a design. The relatively fragmented manner in which the quantitative design is thought of in existing work may produce real research risks for individual research projects. In contrast, the more holistic approaches of some qualitative traditions offer many benefits, but formal design diagnosis can be difficult. Our hope is that MIDA provides a framework for doing both at once.

A useful way to illustrate the fragmented nature of thinking on research design among quantitative scholars is to examine the tools that are actually used to do research design. Perhaps the most prominent of these are “power calculators.” These have an all-design flavor in the sense that they ask whether, given an answer strategy, a data collection strategy is likely to return a statistically significant result. Power calculations like these are done using formulae (e.g., Cohen Reference Cohen1977; Haseman Reference Haseman1978; Lenth Reference Lenth2001; Muller et al. Reference Muller, Lavange, Ramey and Ramey1992; Muller and Peterson Reference Muller and Peterson1984); software tools such as Web applications and general statistical software (e.g., easypower for R and Power and Sample Size for Stata) as well as standalone tools (e.g., Optimal Design, G*Power, nQuery, SPSS Sample Power); and sometimes Monte Carlo simulations.

In most cases these tools, though touching on multiple parts of a design, in fact leave almost no scope to describe what the data generating processes can be, what the questions of interest are, and what types of analyses will be undertaken. We conducted a census of currently available diagnostic tools (mainly power calculators) and assessed their ability to correctly diagnose three variants of a common experimental design, in which assignment probabilities are heterogeneous by block.^{Footnote 5} The first variant simply uses a difference-in-means estimator (DIM), the second conditions on block fixed effects (BFE), and the third includes inverse-probability weighting to account for the heterogeneous assignment probabilities (BFE-IPW).

We found that the vast majority of tools used are unable to correctly characterize the tradeoffs these three variants present. As shown in Table 2, none of the tools was able to diagnose the design while taking account of important features that bias unweighted estimators.^{Footnote 6} In our simulations the result is an overstatement of the power of the difference-in-means.

TABLE 2. Existing Tools Cannot Declare Many Core Elements of Designs and, as a Result, Can Only Calculate Some Diagnosands

Note: Panel (a) indicates the number of tools that allow declaration of a particular feature of the design as part of the diagnosis. In the first row, for example, 0/30 indicates that no tool allows researchers to declare correlated effect and block sizes. Panel (b) indicates the number of tools that can perform a particular diagnosis. Results correspond to design tool census concluded in July 2017 and do not include tools published since then.

Because no tool was able to account for weighting in the estimator, none was able to calculate the power for the IPW-BFE answer strategy. Moreover, no tool sought to calculate the design’s bias, root mean-squared-error, or coverage (which require information on I). The companion software to this article, which was designed based on MIDA, illustrates that power is a misleading indicator of quality in this context. While the IPW-BFE estimator is better powered and less biased than the BFE estimator, its purported efficiency is misleading. IPW-BFE is better powered than DIM and BFE because it produces biased variance estimates that lead to a coverage probability that is too low. In terms of RMSE and the standard deviation of estimates, the IPW-BFE strategy does not outperform the BFE estimator. This exercise should not be taken as proof of the superiority of one strategy over another in general; instead we learn about their relative performance for particular diagnosands for the specific design declared.

We draw a number of conclusions from this review of tools.

First, researchers are generally not designing studies using the actual strategies that they will use to conduct analysis. From the perspective of the overall designs, the power calculations are providing the wrong answer.

Second, the tools can drive scholars toward relatively narrow design choices. The inputs to most power calculators are data strategy elements like the number of units or clusters. Power calculators do not generally focus on broader aspects of a design, like alternative assignment procedures or the choice of estimator. While researchers may have an awareness that such tradeoffs exist, quantifying the extent of the tradeoff is by no means obvious until the model, inquiry, data strategy, and answer strategy is declared in code.

Third, the tools focus attention on a relatively narrow set of questions for evaluating a design. While understanding power is important for some designs, the range of possible diagnosands of interest is much broader. Quantitative researchers tend to focus on power, when other diagnosands such as bias, coverage, or RMSE may also be important. MIDA makes clear, however, that these features of a design are often linked in ways that current practice obscures.

A second illustration of risks arising from a fragmented conceptualization of research design comes from debates over the disproportionate focus on estimators to the detriment of careful consideration of estimands. Huber (Reference Huber2013), for example, worries that the focus on identification leads researchers away from asking compelling questions. In the extreme, the estimators themselves (and not the researchers) appear to select the estimand of interest. Thus, Deaton (Reference Deaton2010) highlights how instrumental variables approaches identify effects for a subpopulation of compliers. Who the compliers are is jointly determined by the characteristics of the subjects and also by the data strategy. The implied estimand (the Local Average Treatment Effect, sometimes called the Complier Average Causal Effect) may or may not be of theoretical interest. Indeed, as researchers swap one instrument for another, the implied estimand changes. Deaton’s worry is that researchers are getting an answer, but they do not know what the question is.^{Footnote 7} Were the question posed as the average effect of a treatment, then the performance of the instrument would depend on how well the instrumental variables regression estimates that quantity, and not how well they answer the question for a different subpopulation. This is not done in usual practice, however, as estimands are often not included as part of a research design.

To illustrate risks arising from the combination of a fractured approach to design in the formal quantitative literature, and the holistic but often less formal approaches in the qualitative literature, we point to difficulties these approaches have in learning from each other.

Goertz and Mahoney (Reference Goertz and Mahoney2012) tell a tale of two cultures in which qualitative and quantitative researchers differ not just in the analytic tools they use, but in very many ways, including, fundamentally, in their conceptualizations of causation and the kinds of questions they ask. The authors claim (though not all would agree) that qualitative researchers think of causation in terms of necessary and/or sufficient causes, whereas many quantitative researchers focus on potential outcomes, average effects, and structural equations. One might worry that such differences would preclude design declaration within a common framework, but they need not, at least for qualitative scholars that consider causes in counterfactual terms.^{Footnote 8}

For example, a representation of a causal process in terms of causal configurations might take the form: Y = AB + C, meaning that the presence of A and B or the presence of C is sufficient to produce Y. This configuration statement maps directly into a potential outcomes function (or structural equation) of the form Y(A, B, C) = max(AB, C). Given this, the marginal effect of one variable, conditional on others, can be translated to the conditions in which the variable is difference-making in the sense of altering relevant INUS^{Footnote 9} conditions: E(Y(A = 1|B, C) − Y(A = 0|B, C)) = E(B = 1, C = 0).^{Footnote 10} Describing these differences in notation as differences in notions of causality suggests that there is limited scope for considering designs that mix approaches, and that there is little that practitioners of one approach can say to practitioners of another approach. In contrast, clarification that the difference is one regarding the inquiry—i.e., which combinations of variables guarantee a given outcome and not the average marginal effect of a variable across conditions—opens up the possibility to assess how quantitative estimation strategies fare when applied to estimating this estimand.

A second point of difference is nicely summarized by Goertz and Mahoney (Reference Goertz and Mahoney2012, 230): “qualitative analysts adopt a ‘causes-of-effects’ approach to explanation [… whereas] statistical researchers follow the ‘effects-of-causes’ approach employed in experimental research.” We agree with this association, though from a MIDA perspective we see such distinctions as differences in estimands and not as differences in ontology. Conditioning on a given X and Y the effects-of-cause question is E(Y _i(X _i = 1) − Y _i(X _i = 0)). By contrast, the cause-of-effects question can be written Pr(Y _i(0) = 0 | X _i = 1, Y _i(1) = 1). This expression asks what are the chances that Y would have been 0 if X were 0 for a unit i for which X was 1 and Y _i(1) was 1. The two questions are of a similar form though the cause-of-effects question is harder to answer (Dawid Reference Dawid2000). Once thought of as questions about what the estimand is, one can assess directly when one or another estimation strategy is more or less effective at facilitating inference about the estimand of interest. In fact, experiments are in general not able to solve the identification problem for cause-of-effects questions (Dawid Reference Dawid2000) and this may be one reason for why these questions are often ignored by quantitative researchers. Exceptions include Yamamoto (Reference Yamamoto2012) and Balke and Pearl (Reference Balke and Pearl1994).

Below, we demonstrate gains from declaration of designs in a common framework by providing examples of design declaration for crisp-set qualitative comparative analysis (Ragin Reference Ragin1987), nested case analysis (Lieberman Reference Lieberman2005), and CPO (causal process observation) process-tracing (Collier Reference Collier2011; Fairfield Reference Fairfield2013), alongside experimental and quasi-experimental designs.

Overall, this discussion suggests that the common ways in which designs are conceptualized produce three distinct problems. First, the different components of a design may not be chosen to work optimally together. Second, consideration is unevenly distributed across components of a design. Third, the absence of a common framework across research traditions obscures where the points of overlap and difference lie and may limit both critical assessment of approaches and cross-fertilization. We hope that the MIDA framework and tools can help address these challenges.

DECLARING AND DIAGNOSING RESEARCH DESIGNS IN PRACTICE

A design that can be declared in computer code can then be simulated in order to diagnose its properties. The approach to declaration that we advocate is one that conceives of a design as a concatenation of steps. To illustrate, the top panel of Table 3 shows how to declare a design in code using the companion software to this paper, DeclareDesign (Blair et al. Reference Blair, Cooper, Coppock, Humphreys and Fultz2018). The resulting set of objects (p_U, f_Y, I, p_S, p_Z, R, and A) are all steps. Formally, each of these steps is a function. The design is the concatenation of these, which we represent using the “+” operator: design <- p_U + f_Y + I + p_S + p_Z + R + A. A single simulation runs through these steps, calling each of the functions successively. A design diagnosis conducts m simulations, then summarizes the resulting distribution of diagnostic statistics in order to estimate the diagnosand.

TABLE 3. A Procedure for Declaring and Diagnosing Research Designs Using the Companion Software DeclareDesign (Blair et al. Reference Blair, Cooper, Coppock, Humphreys and Fultz2018)

Note: The top panel includes each element of a design that can be declared along with code used to declare them. The middle panel describes steps to simulate that design. The bottom panel includes the procedure to diagnose the design.

Diagnosands can be estimated with higher levels of precision by increasing m. However, simulations are often computationally expensive. In order to assess whether researchers have conducted enough simulations to be confident in their diagnosand estimates, we recommend estimating the sampling distributions of the diagnosands via the nonparametric bootstrap.^{Footnote 11} With the estimated diagnosand and its standard error, we can characterize our uncertainty about whether the range of likely values of the diagnosand compare favorably to reference values such as statistical power of 0.8.^{Footnote 12}

Design diagnosis places a burden on researchers to come up with a causal model, M. Since researchers presumably want to learn about the model, declaring it in advance may seem to beg the question. Yet declaring a model is often unavoidable when diagnosing designs. In practice, doing so is already familiar to any researcher who has calculated the power of a design, which requires the specification of effect sizes. The seeming arbitrariness of the declared model can be mitigated by assessing the sensitivity of diagnosis to alternative models and strategies, which is relatively straightforward given a diagnosand-complete design declaration. Further, researchers can inform their substantive models with existing data, such as baseline surveys. Just as power calculators focus attention on minimum detectable effects, design declaration offers a tool to demonstrate design properties and how they change depending on researcher assumptions.

In the next sections, we illustrate how research designs that aim to answer descriptive, causal, and exploratory research questions can be declared and diagnosed in practice. We then describe how the estimand-focused approach we propose works with designs that focus less on estimand estimation and more on modeling data generating processes. In all cases, we highlight potential gains from declaring designs using the MIDA framework.

Causal Inference

The approach to design diagnosis we propose can be used to declare and diagnose a range of research designs typically employed to answer causal questions in the social sciences.

Process Tracing

Although not all approaches to process tracing are readily amenable to design declaration (e.g., theory-building process tracing, see Beach and Pedersen Reference Beach and Pedersen2013, 16), some are. We focus here on Bayesian frameworks that have been used to describe process tracing logics (e.g., Bennett Reference Bennett, Bennett and Checkel2015; Humphreys and Jacobs Reference Humphreys and Jacobs2015; Fairfield and Charman Reference Fairfield and Charman2017). In these approaches, “causal process observations” (CPOs) are believed to be observed with different probabilities depending on the causal process that has played out in a case. Ideal-type CPOs as described by Van Evera (Reference Van Evera1997) are “hoop tests” (CPOs that are nearly certain to be seen if the hypothesis is true, but likely either way), “smoking-gun tests” (CPOs that are unlikely to be seen in general but are extremely unlikely if a hypothesis is false), and “doubly-decisive tests” (CPOs that are likely to be seen if and only if a hypothesis is true).^{Footnote 13} Unlike much quantitative inference, such studies often pose “causes-of-effects” inquiries (did the presence of a strong middle class cause a revolution?), and not “effects-of-causes” questions (what is the average effect of a strong middle class on the probability of a revolution happening?) (Goertz and Mahoney Reference Goertz and Mahoney2012). Such inquiries often imply a hypothesis—“the strong middle class caused the revolution,” say—that can be investigated using Bayes’ rule.

Formalizing this kind of process-tracing exercise leads to non-obvious insights about the tradeoffs involved in committing to one or another CPO strategy ex ante. We declare a design based on a model of the world in which both the driver, X, and the outcome, Y, might be present in a given case either because X caused Y or because Y would have been present regardless of X (or perhaps, an alternative cause was responsible for Y). See Supplementary Materials Section 3.3. The inquiry is whether X in fact caused Y in the specific case under analysis (i.e., would Y have been different if X were different?). The data strategy consists of selecting one case from a population of cases, based on the fact that both X and Y are present, and then collecting two causal process observations. Even before diagnosis, the declaration of the design illustrates an important point: the case selection strategy informs the answer strategy by enabling the researcher to narrow down the number of causal processes that might be at play. This greatly simplifies the application of Bayes’ rule to the case in question.

Importantly, the researcher attaches two different ex ante probabilities to the observation of confirmatory evidence in each CPO, depending on whether X did or did not cause Y. Specifically, the first CPO contains evidence that is more likely to be seen when the hypothesis is true, Pr(E ₁|H) = 0.75, but even when H is false and Y happened irrespective of X, there is some probability of observing the first piece of evidence: Pr(E ₁|¬H) = 0.25. The first CPO thus constitutes a “straw-in-the-wind” test (albeit a reasonably strong one). By contrast, the probability of observing the evidence in the second CPO when the hypothesis that X caused Y is true, Pr(E ₂|H) is 0.30, whereas the probability of observing the evidence when the hypothesis is false, Pr(E ₂|¬H) is only 0.05. The second CPO thus constitutes a “smoking gun” test of H. Observing the second piece of evidence is more informative than observing the first, because it is so unlikely to observe a smoking gun when the hypothesis is false.

Diagnosis reveals that a researcher who relied solely on the weaker “straw-in-the-wind” test would make better inferences on average than one who relied solely on the “smoking gun” test. One does better relying on the straw because, even if it is less informative when observed, it is much more commonly observed than the smoking gun, which is an informative, but rare, clue. The Collier (Reference Collier2011, 826) assertion that, of the four tests, straws-in-the-wind are “the weakest and place the least demand on the researcher’s knowledge and assumptions” might thus be seen as an advantage rather than a disadvantage. In practice, of course, scholars often seek multiple CPOs, possibly of different strength (see, for example, Fairfield Reference Fairfield2013). In such cases, the diagnosis suggests the learning depends on the ways in which these CPOs are correlated. There are large gains from seeking two CPOs when they are negatively correlated—for example, if they arise from alternative causal processes. But there are weak gains when CPOs arise from the same process. Presentations of process tracing rarely describe correlations between CPO probabilities yet the need to specify these (and the gain from doing so) presents itself immediately when a process tracing design is declared.

Qualitative Comparative Analysis (QCA)

One approach to mixed methods research focuses on identifying ways that causes combine to produce outcomes. What, for instance, are the combinations of demography, natural resource abundance, and institutional development that give rise to civil wars? An answer might be of the form: conflicts arise when there is natural resource abundance and weak institutional structure or when there are deep ethnic divisions. The key idea is that different configurations of conditions can lead to the same outcome (equifinality) and the interest is in assessing which combinations of conditions matter.

Many applications of qualitative comparative analysis use Boolean minimization algorithms to assess which configurations of factors are associated with different outcomes. Critics have highlighted that these algorithms are sensitive to measurement error (Hug Reference Hug2013). Pointing to such sensitivity, some even go as far as to call for the rejection of QCA as a framework for inquiry (Lucas and Szatrowski Reference Lucas and Szatrowski2014; for a nuanced response, see Baumgartner and Thiem Reference Baumgartner and Thiem2017).

However, a formal declaration of a QCA design makes clear that these criticisms unnecessarily conflate QCA answer strategies with their inquiries (for a similar argument, see Collier Reference Collier2014). Contrary to claims that regression analysis and QCA stem from fundamentally different ontologies (Thiem, Baumgartner, and Bol Reference Thiem, Baumgartner and Bol2016), we show that saturated regression analysis may mitigate measurement error concerns in QCA. This simple proof of concept joins efforts toward unifying QCA with aspects of mainstream statistics (Braumoeller Reference Braumoeller2003; Rohlfing Reference Rohlfing2018) and other qualitative approaches (Rohlfing and Schneider Reference Rohlfing and Schneider2018).

In Supplementary Materials Section 3.4 we declare a QCA design, focusing on the canonical case of binary variables (“crisp-set QCA”). The model features an outcome Y that arises in a case if and only if cause A is absent and cause B is present (Y = a * B). The approach extends readily to cases with many causes in complex configurations. For our inquiry, we wish to know the true minimal set of configurations of conditions that are sufficient to cause Y. The data strategy involves measuring and encoding knowledge about Y in a truth table. We allow for some error in this process. As in Rohlfing (Reference Rohlfing2018), we are agnostic as to how this error arises: it may be that scholarly debate generates epistemic uncertainty about whether Y is truly present or absent in a given case, or that there is measurement error due to sampling variability.

For answer strategies, we compare two QCA minimization approaches. The first employs the classical Quine-McCluskey (QMC) minimization algorithm (see Duşa and Thiem Reference Duşa and Thiem2015, for a definition) and the second the “Consistency Cubes” (CCubes) algorithm (Duşa Reference Duşa2018) to solve for the set of causal conditions that produces Y. This comparison demonstrates the utility of declaration and diagnosis for researchers using QCA algorithms, who might worry about whether their choice of algorithm will alter their inferences.^{Footnote 14} We show that, at least in simple cases such as this, such concerns are minimal.

We also consider how ordinary least squares minimization performs when targeting a QCA estimand. The right hand side of the regression includes indicators for membership in all feasible configurations of A and B. Configurations that predict the presence of Y with probability greater than 0.5 are then included in the set of sufficient conditions.

The diagnosis of this design shows that QCA algorithms can be successful at pinpointing exactly the combination of conditions that give rise to outcomes. When there is no error and the sample is large enough to ensure sufficient variation in the data, QMC and CCubes successfully recover the correct configuration 100% of the time. The diagnosis also confirms that QCA via saturated regression can recover the data generating process correctly and the configuration of causes estimand can then be computed, correctly, from estimated marginal effects.

This last point is important for thinking through the gains from employing the MIDA framework. The declaration clarifies that QCA is not equivalent to saturated regression: without substantial transformation, regression does not target the QCA estimands (Thiem, Baumgartner, and Bol Reference Thiem, Baumgartner and Bol2016). However, it also clarifies that regression models can be integrated into classical QCA inquiries, and do very well. Using regression to perform QCA is equivalent to QMC and CCubes when there is no error, and even slightly outperforms these algorithms (on the diagnosands we consider) in the presence of measurement error. More work is required to understand the conditions under which the approaches perform differently.

However, the declaration and diagnosis illustrate that there need not be a tension between regression as an estimation procedure and causal configurations as an estimand. Rather than seeing them as rival research paradigms, scholars interested in QCA estimands can combine the machinery developed in the QCA literature to characterize configurations of conditions with the machinery developed in the broader statistical literature to uncover data generating processes. Thus, for instance, in answer to critiques that the method does not have a strategy for causal identification (Tanner Reference Tanner2014), one could in principle try to declare designs in which instrumental variables strategies, say, are used in combination with QCA estimands.

Nested Mixed Methods

A second approach to mixed methods research nests qualitative small N analysis within a strategy that involves movement back and forwards between large N theory testing and small N theory validation and theory generation. Lieberman (Reference Lieberman2005) describes a strategy of nested analysis of this form. In Supplementary Materials Section 3.5, we specify the estimands and analysis strategies implied by the procedure proposed in Lieberman (Reference Lieberman2005). In our declaration, we assume a model with binary variables and an inquiry focused on the relationship between X and Y (both causes-of-effects and effects-of-causes are studied). The model allows for the possibility that there are variables that are not known to the researcher when conducting large N analysis, but might modify or confound the relationship between X and Y. The data strategy and answer strategies are quite complex and integrated with each other. The researcher begins by analyzing a data set involving X and Y. If the quantitative analysis is “successful” (defined in terms of sufficient residual variance explained), the researcher engages in within-case “on the regression line” analysis. Using within-case data, the researcher assesses the extent to which X plausibly caused Y (or not X caused not Y) in these cases. If the qualitative or quantitative analyses reject the model, then a new qualitative analysis is undertaken to better understand the relationship between X and Y. In the design, this qualitative exploration is treated as the possibility of discovering the importance of a third variable that may moderate the effect of X on Y. If an alternative model is successfully developed, it is then tested on the same large N data.

Diagnosis of this design illustrates some of its advantages. In particular, in some settings the within-case analysis can guide researchers to models that better capture data generating processes and improve identification. The declaration also highlights the design features that are left to researchers. How many cases should be gathered and how should they be selected? What thresholds should be used to decide whether a theory is successful or not? The design diagnosis suggests interesting interactions between these design elements. For instance, if the bar for success in the theory testing stage is low in terms of the minimum share of cases explained that are considered adequate, then the researcher might be better off sampling fewer qualitative cases in the testing stage and more in the development stage. More variability in the first stage makes it more likely that one would reject a theory, which might in turn lead to the discovery of a better theory.

Observational Regression-Based Strategies

Many observational studies seek to make causal claims, but do not explicitly employ the potential outcomes framework, instead describing inquiries in terms of model parameters. Sometimes studies describe their goal as the estimation of a parameter β from a model of the form y _i = α + βx _i + ε _i. What is the estimand here? If we believe that this model describes the true data generating process, then β is an estimand: it is the true (constant) marginal effect of x on y. But what if we are wrong about the model? We run into a problem if we want to assess the properties of strategies under different assumptions about data generation when the inquiry itself depends on the data generating model.

To address this problem, we can declare an inquiry as a summary of differences in potential outcomes across conditions, β. Such a summary might derive from a simple comparison of potential outcomes—for example τ ≡ E _xE _i(Y _i(x) − Y _i(x − 1)) captures the difference in outcomes between having income x and having a dollar less, x − 1, for different possible income levels. Or it could be a parameter from a model applied to the potential outcomes. For example we might define α and β as the solutions to:

$$\mathop {\min }\limits_{\left( {\alpha ,\beta } \right)} \sum\limits_i {\int {{{\left( {{Y_i}\left( x \right) - \alpha - \beta x} \right)}^2}} } f\left( x \right){\rm{d}}x$$

Here Y _i(x) is the (unknown) potential outcome for unit i in condition x. Estimand β can be thought of as the coefficient one would get on x if one were to able to regress all possible potential outcomes on all possible conditions for all units (given density of interest f(x)).^{Footnote 15} Our data strategy will simply consist of the passive observation of units in the population, and we assess the performance of an answer strategy employing an OLS model to estimate β under different conditions.

To illustrate, we declare a design that lets us quickly assess the properties of a regression estimate under the assumption that in the true data-generating process y is in fact a nonlinear function of x (Supplementary Materials Section 3.6). Diagnosis of the design shows that under uniform random assignment of x, the linear regression returns an unbiased estimate of a (linear) estimand, even though the true data generating process is nonlinear. Interestingly, with the design in hand, it is easy to see that unbiasedness is lost in a design in which different values of x _i are assigned with differing probabilities. The benefit of declaration here is that, without defining I, it is hard to see the conditions under which A is biased or unbiased. Declaration and diagnosis clarify that, even though the answer strategy “assumes” a non-linear relationship in M that does not hold, under certain conditions OLS is still able to estimate a linear summary of that relationship.

Matching on Observables

In many observational research designs, the processes by which units are assigned to treatment are not known with certainty. In matching designs, the effects of unknown assignment procedure may, for example, be assessed by matching units on their observable traits under an assumption of as-if random assignment between matched pairs. Diagnosis in such instances can shed light on risks when such assumptions are not justified. In Supplementary Materials Section 3.7, we declare a design with a model in which three observable random variables are combined in a probit process that assigns the treatment variable, Z. The inquiry pertains to the average treatment effect of Z on the outcome Y among those actually assigned to treatment, which we estimate using an answer strategy that tries to reconstruct the assignment process to calculate a ^A. Our diagnosis shows that matching improves mean-squared-error (E[(a ^A − a ^M)²]) relative to a naive difference-in-means estimator of the treatment effect on the treated (ATT), but can nevertheless remain biased (E[a ^A − a ^M] ≠ 0) if the matching algorithm does not successfully pair units with equal probabilities of assignment, i.e., if matching has not eliminated all sources of confounding. The chief benefit of the MIDA declaration here is to separate out beliefs about the data generating process (M) from the details of the answer strategy (A), whose robustness to alternative data generating processes can then be assessed.

Regression Discontinuity

While in many observational settings researchers do not know the assignment process, in others, researchers may know how assignment works without necessarily controlling it. In regression discontinuity designs, causal identification is often premised on the claim that potential outcomes are continuous at a critical threshold (see De la Cuesta and Imai Reference De la Cuesta and Imai2016; Sekhon and Titiunik Reference Sekhon and Titiunik2016). The declaration of such designs involves a model that defines the unknown potential outcomes functions mapping average outcomes to the running and treatment variables. Our inquiry is the difference in the conditional expectations of the two potential outcomes functions at the discontinuity. The data strategy involves passive observation and collection of the data. The answer strategy is a polynomial regression in which the assignment variable is linearly interacted with a fourth order polynomial transformation of the running variable. In Supplementary Materials Section 3.8, we declare and diagnose such a design.

The declaration highlights a difference between this design and many others: the estimand here is not an average of potential outcomes of a set of sample units, but rather an unobservable quantity defined at the limit of the discontinuity. This feature makes the definition of diagnosands such as bias or external validity conceptually difficult. If researchers postulate unobservable counterfactuals, such as the “treated” outcome for a unit located below the treatment threshold, then the usefulness of the regression discontinuity estimate of the average treatment effect for a specific set of units can be assessed.

Experimental Design

In experimental research, researchers are in control of sample construction and assignment of treatments, which makes declaring these parts of the design straightforward. A common choice faced in experimental research is between employing a 2-by-2 factorial design or a three-arm trial where the “both” condition is excluded. Suppose we are interested in the effect of each of two treatments when the other condition is set to control. Should we choose a factorial design or a three-arm design? Focusing for simplicity on the effect of a single treatment, we declare two designs under a range of alternative models to help assess the tradeoffs. For both designs, we consider models M ₁,…, M _K, where we let the interaction between treatments vary over the range −0.2 to +0.2. Our inquiry is always the average treatment effect of treatment 1 given all units are in the control condition for treatment 2. We consider two alternative data strategies: an assignment strategy in which subjects are assigned to a control condition, treatment 1, or treatment 2, each with probability 1/3; and an alternative strategy in which we assign subjects to each of four possible combinations of factors with probability 1/4. The answer strategy in both cases involves a regression of the outcome on both treatment indicators with no interaction term included.

We declare and diagnose this design and confirm that neither design exhibits bias when the true interaction term is equal to zero (Figure 1 left panel). The details of the declaration can be found in Supplementary Materials Section 3.9. However, when the interaction between the two treatments is stronger, the factorial design renders estimates of the effect of treatment 1 that are more and more biased relative to the “pure” main effect estimand. Moreover, there is a bias-variance tradeoff in choosing between the two designs when the interaction is weak (Figure 1 right panel). When the interaction term is close to zero, the factorial design is preferred, because it is more powerful: it compares one half of the subject pool to the other half, whereas the three-arm design only compares a third to a third. However, as the magnitude of the interaction term increases, the precision gains are offset by the increase in bias documented in the left-panel. When the true interaction between treatments is large, the three-arm design is then preferred. This exercise highlights key points of design guidance. Researchers often select factorial designs because they expect interaction effects, and indeed factorial designs are required to assess these. However if the scientific question of interest is the pure effect of each treatment, researchers should (perhaps counterintuitively) use a factorial design if they expect weak interaction effects. An integrated approach to design declaration here illustrates non-trivial interactions between the data strategy, on the one hand, and the ability of answers (a ^A) to approximate the estimand (a ^M), on the other.

FIGURE 1. Diagnoses of Designs With Factorial or Three-Arm Assignment Strategies Illustrate a Bias-Variance Tradeoff

Bias (left), root mean-squared-error (center), and power (right) are displayed for two assignment strategies, a 2 × 2 treatment arm factorial design (black solid lines; circles) and a three-arm design (gray dashed lines; triangles) according to varying interaction effect sizes specified in the potential outcomes function (x axis). The third panel also shows power for the interaction effect (squares) from the factorial design.

PUTTING DECLARATIONS AND DESIGN DIAGNOSIS TO USE

We have described and illustrated a strategy for declaring research designs for which “diagnosands” can be estimated given conjectures about the world. How might declaring and diagnosing research designs in this way affect the practices of authors, readers, and replication authors? We describe implications for how designs are chosen, communicated, and challenged.

Challenging Design Choices

The independent replication of the results of studies after their publication is an essential component of the shift toward more credible science. Replication—whether verification, reanalysis of the original data, or reproduction using fresh studies—provides incentives for researchers to be clear and transparent in their analysis strategies, and can build confidence in findings.^{Footnote 17}

In addition to rendering the design more transparent, diagnosand-complete declaration can allow for a different approach to the re-analysis and critique of published research. A standard practice for replicators engaging in reanalysis is to propose a range of alternative strategies and assess the robustness of the data-dependent estimates to different analyses. The problem with this approach is that, when divergent results are found, third parties do not have clear grounds to decide which results to believe. This issue is compounded by the fact that, in changing the analysis strategy, replicators risk departing from the estimand of the original study, possibly providing different answers to different questions. In the worst case scenario, it can be difficult to determine what is learned both from the original study and from the replication.

A more coherent strategy facilitated by design simulations would be to use a diagnosand-complete declaration to conduct “design replication.” In a design replication, a scholar restates the essential design characteristics to learn about what the study could have revealed, not just what the original author reports was revealed. This helps to answer the question: under what conditions are the results of a study to be believed? By emphasizing abstract properties of the design, design replication provides grounds to support alternative analyses on the basis of the original authors’ intentions and not on the basis of the degree of divergence of results. Conversely, it provides authors with grounds to question claims made by their critics.

Table 4 illustrates situations that may arise. In a declared design an author might specify situation 1: a set of claims on the structure of the variables and their potential outcomes (the model) and an estimator (the answer strategy). A critic might then question the claims on potential outcomes (for example, questioning a no-spillovers assumption) or question estimation strategies (for example, arguing for inclusion or exclusion of a control variable from an analysis), or both.

TABLE 4. Diagnosis Results Given Alternative Assumptions About the Model and Alternative Answer Strategies

Note: Four scenarios encountered by researchers and reviewers of a study are considered depending on whether the model or the answer strategy differ from the author’s original strategy and model.

In this context, there are several possible criteria for admitting alternative answer strategies:

• • Home Ground Dominance. If ex ante the diagnostics for situation 3 are better than for 1 then this gives grounds to switch to 3. That is, if a critic can demonstrate that an alternative estimation strategy outperforms an original estimation strategy even under the data generating process assumed by an original researcher, then they have strong grounds to propose a change in strategies. Conversely, if an alternative estimation strategy produces different results, conditional on the data, but does not outperform the original strategy given the original assumptions, this gives grounds to question the reanalysis.

• • Robustness to Alternative Models. If the diagnostics in situation 3 are as good as in 1 but are better in situation 4 than in situation 2 this provides a robustness argument for altering estimation strategies. For example, in a design with heterogeneous probabilities by block, an inverse propensity-weighted estimator will do about as well as a fixed effects estimator in terms of bias when treatment effects are constant, but will perform better on this dimension when effects are heterogeneous.

• • Model Plausibility. If the diagnostics in situation 1 are better than in situation 3, but the diagnostics in situation 4 are better than in situation 2, then things are less clear and the justification of a change in estimators depends on the plausibility of the different assumptions about potential outcomes.

The normative value or relative ranking of these criteria should be left to individual research communities. Without a declared design, in particular the model and inquiry, none of these criteria can be evaluated, complicating the defense of claims for both the critic and the original author.

APPLICATION: DESIGN REPLICATION OF Björkman and Svensson (Reference Björkman and Svensson2009)

We illustrate the insights that a formalized approach to design declaration can reveal through an application to the design of Björkman and Svensson (Reference Björkman and Svensson2009), which investigated whether community-based monitoring can improve health outcomes in rural Uganda.

We conduct a “design replication:” using available information, we posit a Model, Inquiry, Data, and Answer strategy to assess properties of Björkman and Svensson (Reference Björkman and Svensson2009). This design replication can be contrasted with the kind of reanalysis of the study’s data that has been conducted by Donato and Garcia Mosqueira (Reference Donato and Garcia Mosqueira2016) or the reproduction by Raffler, Posner, and Parkerson (Reference Raffler, Posner and Parkerson2019) in which the experiment was conducted again.

The exercise serves three purposes: first, it sheds light on the sorts of insights the design can produce without using the original study’s data or code; second, it highlights how difficulties can arise from designs in which the inquiry is not well-defined; third, we can assess the properties of replication strategies, notably those pursued by Donato and Garcia Mosqueira (Reference Donato and Garcia Mosqueira2016) and Raffler, Posner, and Parkerson (Reference Raffler, Posner and Parkerson2019), in order to make clearer the contributions of such efforts.

In the original study, Björkman and Svensson (Reference Björkman and Svensson2009) estimate the effects of treatment on two important indicators: child mortality, defined as the number of deaths per 1,000 live births among under-5 year-olds (taken at the catchment-area-level) and weight-for-age z-scores, which are calculated by subtracting from an infant’s weight the median for their age from a reference population, and dividing by the standard deviation of that population. In the original design, the authors estimate a positive effect of the intervention on weight among surviving infants. They also find that the treatment greatly decreases child mortality.

We briefly outline the steps of our design replication here, and present more detail in Supplementary Materials Section 4.

We began by positing a model of the world in which unobserved variables, “family health” and “community health,” determine both whether infants survive early childhood and whether they are malnourished.

Our attempt to define the study’s inquiry met with a difficulty: the weight of infants in control areas whose lives would have been saved if they had been in the treatment is undefined (for a discussion of the general problem known as “truncation-by-death,” see Zhang and Rubin Reference Zhang and Rubin2003). Unless we are willing to make conjectures about undefined states of the world (such as the control weight of a child who would not have survived if assigned to the control), we can only define the average difference in individuals’ potential outcomes for those children whose survival is unaffected by the treatment: E[Weight(Z = 1) − Weight(Z = 0)|Alive(Z = 0) = Alive(Z = 1) = 1].^{Footnote 18}

As in the original article we stratify sampling on catchment area and cluster-assign households in 25 of the 50 catchment areas to the intervention.

We estimate mortality at the cluster level and weight-for-age among living children at the household level, as in Björkman and Svensson (Reference Björkman and Svensson2009).

Figure 2 illustrates how the existence of an effect on mortality can pose problems for the unbiased estimation of an effect on weight-for-age. The histograms represent the sampling distributions of the average effect estimates of community monitoring on infant mortality and weight-for-age. The dotted vertical line represents the true average effect (a ^M). The mortality estimand is defined at the cluster level and the weight-for-age estimand is defined for infants who would survive regardless of treatment status. The dashed line represents the average answer, i.e., the answer we expect the design to provide (E[a ^A]). The weight-for-age answer strategy simply compares the weights of surviving infants across treatment and control. Under our postulated model of the world, the estimates of the effect on weight-for-age are biased downwards because it is precisely those infants with low health outcomes whose lives are saved by the treatment.

FIGURE 2. Data-independent Replication of Estimates in Björkman and Svensson (Reference Björkman and Svensson2009)

Histograms display the frequency of simulated estimates of the effect of community monitoring on infant mortality (left) and on weight-for-age (right). The dashed vertical line shows the average estimate, the dotted vertical line shows the average estimand.

We draw upon the “robustness to alternative models” criterion (described in the previous section) to argue for an alternative answer strategy that exhibits less bias under plausible conjectures about the world.

An alternative answer strategy is to attempt to subset the analysis of the weight effects to a group of infants whose survival does not depend on the treatment. This approach is equivalent to the “find always-responders” strategy for avoiding post-treatment bias in audit studies (Coppock Reference Coppock2019). In the original study, for example, the effects on survival are much larger among infants younger than two years old. If indeed the survival of infants above this age threshold is unaffected by the treatment, then it is possible to provide unbiased estimates of the weight-for-age effect, if only among this group. In terms of bias, such an approach does at least as well if we assume that there is no correlation between weight and mortality, and better if such a correlation does exist. It thus satisfies the “robustness to alternative models” criterion.

A reasonable counter to this replication effort might be to say that the alternative answer strategy does not meet the criterion of “home ground dominance” with respect to RMSE. The increase in variance from subsetting to a smaller group may outweigh the bias reduction that it entails. In both cases, transparent arguments can be made by formally declaring and comparing the original and modified designs.

The design replication also highlights the relatively low power of the weight-for-age estimator. As Gelman and Carlin (Reference Gelman and Carlin2014) have shown, conditioning on statistical significance in such contexts can pose risks of exaggerating the true underlying effect size. Based on our assumptions, what can we say here, specifically, about the risk of exaggeration? How effectively does a design such as that used in the replication by Raffler, Posner, and Parkerson (Reference Raffler, Posner and Parkerson2019) mitigate this risk? To answer this question, we modify the sampling strategy of our simulation of the original study to include 187 clusters instead of 50.^{Footnote 19} We then define the diagnosand of interest as the “exaggeration ratio” (Gelman and Carlin Reference Gelman and Carlin2014): the ratio of the absolute value of the estimate to the absolute value of the estimand, given that the estimated effect is significant at the α = 0.05 level. This diagnosand thus provides a measure of how much the design exaggerates effect sizes conditional on statistical significance.

The original design exhibits a high exaggeration ratio, according to the assumptions employed in the simulations: on average, statistically significant estimates tend to exaggerate the true effect of the intervention on mortality by a factor of two and on weight-for-age by a factor of four. In other words, even though the study estimates effects on mortality in an unbiased manner, limiting attention to statistically significant effects provides estimates that are twice as large in absolute value as the true effect size on average. By contrast, using the same sample size as that employed in Raffler, Posner, and Parkerson (Reference Raffler, Posner and Parkerson2019) reduces the exaggeration ratio on the mortality estimand to where it should be, around one.

Finally, we can also address the analytic replication by Donato and Garcia Mosqueira (Reference Donato and Garcia Mosqueira2016). The replicators (D&M) noted that the eighteen community-based organizations who carried out the original “power to the people” (P2P) intervention were active in 64% of the treatment communities and 48% of the control communities. Donato and Garcia Mosqueira (Reference Donato and Garcia Mosqueira2016) posit that prior presence of these organizations may be correlated with health outcomes, and therefore include in their analytic replication of the mortality and weight-for-age regressions both an indicator for CBO presence and the interaction of the intervention with CBO presence. The inclusion of these terms into the regression reduces the magnitude of the coefficients on the intervention indicator and thereby increases the p-values above the α = 0.1 threshold in some cases. The original authors (B&S) criticized the replicators’ decision to include CBO presence as a regressor, on the grounds that in any such study it is possible to find some unrelated variable whose inclusion will increase standard error of the treatment effect estimate.

In short, the original replicators make a set of contrasting claims about the true model of the world: B&S claim that CBO presence is unrelated to the outcome of interest (Björkman Nyqvist and Svensson Reference Björkman Nyqvist and Svensson2016), whereas D&M claim that CBO presence might indeed affect (or be otherwise correlated with) health outcomes. As we argued in the previous section, diagnosis of the properties of the answer strategy under these competing claims should determine which answer strategy is best justified.

Since we do not know whether the replicators would have conditioned on CBO presence and its interaction with the intervention if it had not been imbalanced, we modify the original design to include four different replicator strategies: the first ignores CBO presence as in the original study; the second includes CBO presence irrespective of imbalance; the third includes an indicator for CBO presence only if the CBO presence is significantly imbalanced among the 50 treatment and control clusters at the α = 0.05 level; and the last strategy includes terms for both CBO presence and an interaction of CBO presence with the treatment irrespective of imbalance. We consider how these strategies perform under a model in which CBO presence is unrelated to health outcomes, and another in which, as claimed by the replicators, CBO presence is highly correlated with health outcomes.

Including the interaction term is a strictly dominated strategy from the standpoint of reducing mean squared error: irrespective of whether CBO presence is correlated with health outcomes or imbalanced, the RMSE expected under this strategy is higher than under any other strategy. Thus, based on a criterion of “Home Ground Dominance” in favor of B&S, one would be justified in discounting the importance of the replicators’ observation that “including the interaction term leads to a further reduction in magnitude and significance” of the estimated treatment effect (Donato and Garcia Mosqueira Reference Donato and Garcia Mosqueira2016, 19).

Supposing now that there is no correlation between CBO presence and health outcomes, inclusion of the CBO indicator does increase RMSE ever so slightly in those instances where there is imbalance, and the standard errors are ever so slightly larger. On average, however, the strategies of conditioning on CBO presence regardless of balance and conditioning on CBO presence only if imbalanced perform about as well as a strategy of ignoring CBO presence when there is no underlying correlation. However, when there is a correlation between health outcomes and CBO presence, strategies that include CBO presence improve RMSE considerably, especially when there is imbalance. Thus, D&M could make a “Robustness to Alternative Models” claim in defense of their inclusion of the CBO dummy: including CBO presence does not greatly diminish inferential quality on average, even if there is no correlation in CBO presence and outcomes; and if there is such a correlation, including CBO presence in the regression specification strictly improves inferences. In sum, a diagnostic approach to replication clarifies that one should resist updating beliefs about the study based on the use of interaction terms, but that the inclusion of the CBO indicator only harms inferences in a very small subset of cases. In general, including it does not worsen inferences and in many cases can improve them. This approach helps to clarify which points of disagreement are most critical for how the scientific community should interpret and learn from replication efforts.

SUPPLEMENTARY MATERIAL

To view supplementary material for this article, please visit https://doi.org/10.1017/S0003055419000194.

Replication materials can be found on Dataverse at: https://doi.org/10.7910/DVN/XYT1VB.