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Optimized Partial Identification Bounds for Regression Discontinuity Designs with Manipulation

Regression discontinuity designs (RDDs) have become one of the most widely-used quasi-experimental tools for causal inference. A crucial assumption on which they rely is that the running variable cannot be manipulated -- an assumption frequently violated in practice, jeopardizing point identification. In this paper, we introduce a novel method that provide partial identification bounds on the causal parameter of interest in sharp and fuzzy RDDs. The method first estimates the number of manipulators in the sample using a log-concavity assumption on the un-manipulated density of the running variable. It then derives best- and worst-case bounds when we delete that number of points from the data, along with fast computational methods to obtain them. We apply this procedure to a dataset of blood donations from the Abu Dhabi blood bank to obtain the causal effect of donor deferral on future volunteering behavior. We find that, despite significant manipulation in the data, we are able to detect causal effects where traditional methods, such as donut-hole RDDs, fail.


Introduction
The regression discontinuity (RD) design (Thistlethwaite and Campbell, 1960) is a vital analytic tool for social scientists that can provide experiment-quality inference. It has gained popularity due to its applicability in diverse contexts where controlled experiments are difficult to run. RD designs have been used in medical settings, e.g. to infer the effect of health insurance on neonatal hospital stays (Almond and Doyle, 2011); in education, e.g. to estimate the effect of college quality on students' postsecondary enrollment choices (Cohodes and Goodman, 2014); and in political science, e.g. to estimate the effect of incumbency on U.S. House election outcomes (Lee, 2008).
The RD design exploits scenarios in which each person or unit has an associated score, called the "running variable," and treatments are assigned based on whether the score 1 falls above or below a threshold. Under the assumption that the score cannot be precisely manipulated near the threshold, the assignment to treatment is as good as random in a narrow window around the threshold. This quasi-randomization is exploited in the RD design to infer local average treatment effects.
Inference critically relies on the assumption that the score cannot be precisely manipulated (Cattaneo et al., 2020), but this assumption is often problematic in practice. Recent studies have shown that teachers inflate students' grades to push them above grade thresholds (Diamond and Persson, 2016), police officers discount the recorded speed in roadside speed tests to pull it below fine thresholds Mello, 2017, 2020), and close union certification elections are manipulated (Frandsen, 2017). In this manuscript, we discuss another example: blood donations in the United Arab Emirates (UAE), where health care workers demonstrably bump hemoglobin test results to meet eligibility thresholds. In the many situations where the running variable is manipulated, ignoring the manipulation can yield biased inferences (McCrary, 2008;Frandsen, 2017).
To address manipulation of the running variable in RD analyses, we propose a "partial identification" method, where we bound the causal effect estimand rather than seeking to point-identify it (Manski et al., 1989;Manski and Tamer, 2002). We propose a two-step procedure: first, we estimate the number of manipulators in the data using a continuity and log-concavity assumption on the un-manipulated density of the running variable. 2 Other than rounding effects, this step builds from the density model used in Diamond and Persson (2016). In the second step, we introduce a novel partial bounds estimator, which estimates best-and worst-case bounds consistent with the un-manipulated density. We also provide inferential tools that account for sampling uncertainty. We demonstrate the effectiveness of our partial bounds methodology by estimating the causal effect of mandatory deferrals on blood donor return rate using our UAE data.
The remainder of the paper is organized as follows. In Section 2, we review relevant literature on regression discontinuity designs, running variable manipulation, and partial identification of causal effects. Section 3 introduces our proposed method and includes details about practical computation of partial identification bounds as well as confidence intervals. Section 4 analyzes our blood donations application and provides empirical bounds for our causal estimates. Finally, Section 5 critically examines our results from both the methodology and the application, and concludes the paper.

Literature Review
Since its introduction in the mid-twentieth century, the RD design has yielded a broad literature covering both applications and methodological developments. Perhaps the most fundamental question is how to estimate conditional means just below and just above the cutoff. Local polynomial regression approaches have received substantial attention in recent decades (Hahn et al., 2001;Imbens and Lemieux, 2008), with particular focus on the selection of tuning parameters such as the choice of kernel and the smoothing bandwidth. More recently, Imbens and Wager (2018) proposed a minimax linear estimator, which obviates the need for some of these choices. Yet, regression-based methods remain appealing due to their simplicity and interpretability.
To address violations of the RD design assumptions, McCrary (2008) introduced an intuitive test for identifying the presence of running variable manipulation by examining its density. Given manipulation, we would expect to see a discontinuity in the running variable, resulting from individuals moving across the cutoff to secure a favorable treatment. McCrary suggests an empirical hypothesis test for this density discontinuity, making use of a density estimator originally proposed by Cheng et al. (1997). Alternative tests for continuity of the running variable in the RD design have been proposed in Arai et al. (2021) and Bugni and Canay (2021). Other density estimators have subsequently been proposed by both Otsu et al. (2013) and Cattaneo et al. (2015). Frandsen (2017) extended this approach by developing an alternative test for manipulation for the case of a discrete running variable. These methods have been widely adopted in the applied literature as a falsification test for checking the assumption of no manipulation; see Jales and Yu (2017) for a full review of them in the context of regression discontinuities and Kleven (2016) for a related but distinct treatment from the point of view of bunching. The applied literature suggests manipulation in RD designs occurs frequently (e.g. Angrist et al., 2019;Davis et al., 2010;Dee et al., 2019). Yet, there is comparatively little clarity on how to proceed when these tests indicate manipulation. One method used in empirical work is the donut hole RD design (such as in Almond and Doyle, 2011;Bajari et al., 2011;Castleman and Goodman, 2018;Kırdar et al., 2018). The donut RD design deletes data within a window around the cutoff, with the goal being to remove all manipulated observations. Then RD estimates may be obtained from a parametric model fit on data outside the window and extrapolated to the cutoff. As yet, donut hole designs do not have a solid theoretical foundation and are therefore subject to ad-hoc estimation specifications. More fundamentally, by deleting all the data around the cutoff, they weaken the RD design itself, which relies on exactly the data around the cutoff the most.
One paper that does not resort to donut-hole style deletion is Diamond and Persson (2016). They consider Swedish math test data in which there is evidence of teachers inflating students' grades. They develop an estimator to determine the causal effect of the score manipulation on future educational attainment and earnings. While their focus is on a different causal effect than the one we consider, the paper develops several useful methods that we will incorporate here. We pursue the "partial identification" approach, popularized by Manski and later by Tamer (see e.g., Manski et al., 1989;Manski and Tamer, 2002;Haile and Tamer, 2003). The core idea is that, in scenarios in which a treatment effect cannot be point-identified (even with an infinite sample size), it can sometimes still be bounded. These bounds might be very informative in practice-for example, allowing us to rule out negative or positive treatment effects. Davis et al. (2013) show one way such a bound may be derived. However, they only provide a one-sided bound. Gerard et al. (2015) take a two-sided partial identification approach to analyzing RD designs in the presence of manipulation. Their method posits the existence of subpopulations of manipulators and non-manipulators and defines the causal effect on the non-manipulators as the inferential target. We adopt the same framework but differ in our estimation technique. Particularly, Gerard and co-authors extend McCrary's result to estimate the proportion of manipulators at the cutoff c. They then propose a "polynomial truncation" approach to estimation, which implicitly assumes all manipulated units lie at the top or bottom of the distribution of outcomes within a bandwidth h above the threshold. We avoid making such an assumption by estimating the manipulator counts at all values of the running variable and explicitly assuming that it is discrete.

Methodology
Manipulation of the running variable -and the resultant selection bias -have been a seemingly insurmountable roadblock to inference. To address this issue, we pursue the "partial identification" approach, popularized by Manski and later by Tamer (Manski et al., 1989;Manski and Tamer, 2002;Haile and Tamer, 2003). Under partial identification, we obtain informative bounds on the treatment effect even when point estimation is not possible due to the manipulation.

Notation and Preliminaries
Suppose we have a regression discontinuity design with running variable X i for units i = 1, . . . , N . These units assumed to be sampled from a larger super-population. X i is assumed discrete, with possible values enumerated in X such that |X | < ∞. Suppose also we have cutoff c ∈ X , with N units falling to the left of the cutoff and N r units falling at or above the cutoff, where N + N r = N . In the discussion to follow, we will assume for simplicity that the entries of X are integers lying within a given range.
We associate with each unit i a pair of unseen potential outcomes (Y i (0), Y i (1)) ∈ R 2 , corresponding to the value of the outcome if unit i does not or does receive the treatment, respectively. We also associate with each unit an observed value of the running variablẽ X i and a true, unobserved value of the running variable X i . As a shorthand, define H i ∈ {0, 1} as an indicator of whether a unit is an "honest" subject, as opposed to a manipulator: The researcher observes a treatment assignment W i ∈ {0, 1}. We will begin by considering the case of a sharp RD design, such thatX i < c =⇒ W i = 0 and X i ≥ c =⇒ W i = 1. We will later extend results to the fuzzy RD design, where -as is the case with our blood donation setting -the probability probability of treatment is discontinuous atX i ≥ c. In either case, note that treatment assignments are based on the observed running variable rather than the true running variable. The researcher observes the outcome for each unit. Our estimand of interest is where the expectation is with respect to the super-population from which our data is sampled.

Causal Estimation
Many standard sharp RDD causal effect estimators can be written in the following form: Per the under-bracketed quantities, these estimators separately calculate two coefficient vectors: one from a regression relating outcomes to the running variable below the cutoff, the other above the cutoff. The causal estimate is given by the difference in these two regression predictions at the cutoff c.
Specifically,X ∈ R N ×p andX r ∈ R Nr×p are concatenated basis expansion of the observed variablesX i for units to the left and right of the cutoff, respectively; c ∈ R p is an analogous basis expansion of the cutoff c; and M ∈ R N ×N and M r ∈ R Nr×Nr are diagonal matrices representing unit-level weights. We require that the unit-level weights depend solely on the distance between the observed running variable valueX i , and the cutoff, c. The popular local polynomial regression approach Hahn et al. (2001) can be expressed in this form, as can spline formulations Lemieux and Milligan (2008) and simpler unweighted regressions.
In the ideal case, there is no manipulation, such thatX i = X i for all units. If the researcher also correctly posits the functional form of the estimator, thenβ r andβ are unbiased estimators of the true coefficient vectors β r and β relating Y i (1) and Y i (0) to X i , respectively. As a consequence,τ (c) is be an unbiased estimator of τ (c). 3 However, in the presence of manipulation, these estimators would be "polluted" by the presence of individuals who had manipulated their running variable scores. That is, the RDD estimator is no longer a consistent estimator for the true causal effect of interest, but is biased by the selection of manipulators into treatment. We will consider the case of unidirectional manipulation; in our blood donation setting, this means that manipulation only occurs to increase reported h-levels such that an individual will be able to donate blood. With unidirectional manipulation, only the estimate β r is polluted by the presence of manipulators.
In the presence of unidirectional manipulation, a valid point estimate of β r could be recovered if we had access to the values H i for each unit. Denote as H r = diag(H 1 , . . . , H Nr ) ∈ {0, 1} Nr×Nr the diagonal matrix containing the honesty indicators for units above the cutoff. That is, H i is 0 if i is a manipulator and 1 otherwise. Then the estimator withβ as defined in (1), would "ignore" all manipulators. Thusτ (c) cannot be computed because H r is not known in practice, which is the reason we motivate partial identification. Nevertheless, we use its definition to provide the basis for our procedure.

An Optimization Problem
Though we cannot directly obtain the H i values that populate the diagonal of H r , we can obtain information about the count of manipulators at each unique value ofX i at or above c. This is a central tenet of our approach: we use this information to linearly constrain H r , and then pose the problem as an optimization. We obtain the counts of manipulators by estimating the un-manipulated density of the forcing variable from the observed density as in Diamond and Persson (2016). We assume the un-manipulated density is log-concave, except for rounding effects at integers. The log-concavity allows our density to be unimodal. We postulate the existence of a "manipulation region," within (and only within) which there are deviations in the observed density from the un-manipulated density. Further, we enforce a constraint that the "missing" mass to the left of the cutoff c in the manipulation region (i.e. the unmanipulated density minus the observed density) equals the "excess" mass to the right of the cutoff (i.e. the observed density minus the un-manipulated density). We estimate this model for the un-manipulated density using a Poisson regression, which gives us the un-manipulated density along with the counts of manipulators (i.e. the excess mass to the right of the threshold).
We now describe our process for obtaining the partial identification bounds. Suppose that X contains n r unique values greater than or equal to c. The honest subject counts can be represented as a vector ν ∈ R nr whose j th entry ν j corresponds to the number of honest subjects for whom we can capture our knowledge of the honest subject counts via the constraint ZH r = ν where diag(H r ) = H r . Now, we can compute the largest and smallest values of our estimated causal effect τ (c) that is consistent with this constraint. We will consider only the upper bound, as the lower bound is computed identically except using minimization rather than maximization. For simplicity of notation, we also drop most of the "r" subscripts in defining Optimization Problem 1: The Boolean constraint on H will yield an intractable problem. Observe that relaxing the constraint can only widen the bounds, so we instead solve the simplified problem: (2)

Reduction to a Linear Program
Optimization Problem 2 can be reduced to a linear program through several observations. DefineX i as the i th row ofX and M ij the (i, j) th entry of M . Then Moreover, since the regression weights are based on the distance betweenX i and c, we will also have thatX i =X j ⇐⇒ M ii = M jj . We will definẽ We also denote as ν ( ) the entry in ν corresponding to the number of honest subjects for whomX i = . We assume the problem is feasible and hence a solution must exist that satisfies ZH = ν. Imposing this constraint, we can now write where the second line follows from satisfaction of the ZH = ν constraints. Note that the expression on the right-hand side is not a function of the H i . Hence, we can define a constant matrix, and rewrite our optimization problem as Now, recall that the trace of a constant is simply the constant itself. Hence, we can rewrite the first term of the objective as where the second line follows from the cyclic property of the trace; and the third line from matrix algebra rules and the fact that H = diag(H).
Hence, we can reduce our optimization problem to a simple linear program, given by This problem can be efficiently solved by conventional solvers.

Extension to Fuzzy RDD Case
Our blood donation setting involves a fuzzy, rather than sharp, RDD -meaning that the probability of a donation increases sharply at the threshold, but not all the way from zero to one.
Our approach can be extended easily to the case of the fuzzy RDD. In this case, we suppose the estimate of the causal effect is obtained via an instrumental variable approach. The numerator is the difference of the mean treated outcomes just above and just below the cutoff, and the denominator is the difference of the treatment probabilities just above and just below the cutoff.
We require that the the linear probability model be used to estimate the change in treatment probabilities at the cutoff. Further, we require the same basis expansion be used as in estimating the discontinuity in the outcome. Then, we can define an alternative estimator for the causal effect, where Z r is the vector of treatment indicators to the right of the cutoff andα is the fitted coefficient corresponding to the regression of Z on X to the left of the cutoff. The upper bound on the causal effect can be obtained via an optimization problem in which we maximize τ f (c) subject to constraints on the histogram of honest subjects. As in the prior section, we can substitute Φ to obtain the optimization problem: where we have again dropped "r" subscripts for simplicity. Finally, using the same trace trick as in the prior section, we can reduce the problem to a linear fractional programming problem, Using results from Boyd et al. (2004), this problem can be transformed into an equivalent linear program and solved via conventional solvers.

Bootstrap Inference
A natural question is how to do inference when using our estimation procedure. We suggest the use of a percentile bootstrap procedure which conditions upon the observed histogram of the running variable.
Without loss of generality, suppose the entries ofX are ordered row-wise by the value ofX i (with any ordering applied to ties). The key steps for each bootstrap replicate b are given below.
• For each value in x ∈ X , sample i I(X i = x) units with replacement. Order the units based on the observed value ofX i .
-Because we are conditioning on the observed histogram of the running variable, the estimated un-manipulated density will be unchanged from the original sample. Hence, any matrices or vectors based on the running variable will be unchanged from the original problem.
-For units to the left of the cutoff c, we can compute coefficientsβ based on the resampled data in replicate b.
-For units to the right of the cutoff, the values of Φ,X, and M corresponding to the bootstrap sample will be unchanged from those in the original sample. However, we will now have bootstrap samples Z (b) and Y (b) corresponding to replicate b.
• The bootstrap estimateτ Suppose we repeat this process for b = 1, . . . , B, where we typically assume B is a few hundred samples. Denote as Q u (v) the function which takes in a vector v and returns the u th quantile of v. Then the upper bound of our interval at level α is given by The lower bound, L, is computed analogously, as the α/2 quantile of the lower bounds across our bootstrap replicates. The coverage properties of the interval [L, U ] are discussed in Theorem 3.6.
Theorem 1 (Bootstrap Validity). Suppose the correct basis expansion is chosen in Equation 1 to model the potential outcome surfaces and treatment probabilities; and that the histogram of honest respondents is correctly estimated. Then [L, U ] will asymptotically contain the true causal effect τ (c) with probability at least 1 − α.
Proof. We utilize the same proof structure as Zhao et al. (2019), and prove the validity of the upper bound. The lower bound proof is analogous. We observe that there are a finite number N of possible bootstrap samples, where Next, define the set and the causal effect estimator where here we are explicitly defining the estimator as a function of H, Y, Z,β , andα . For every H ∈ H, we observe Because this inequality holds for each value of b, it also holds for any order statistic computed across the range of b. Hence, for any choice of α, we have Inequality 7 holds for any choice of H ∈ H, so we can take the supremum of the quantity on the left to observe The quantity on the left-hand side can be viewed as the upper bound of the union of all α-level confidence intervals for T (·) evaluated over all possible values of H ∈ H. As long as τ (c) lies in the interval for the true value of H with probability (1 − α), it thus must lie below U with probability at least (1 − α/2). For a formal statement of this result, see Berger (1982). Hence, we need only show that the bootstrap is valid for estimating the uncertainty in T (·) for a fixed value of H. Under the assumptions of Theorem , T (·) is a consistent estimator of τ (c) and can be written as a Z-estimator. Hence, by the results of Wellner and Zhan (1996), the asymptotic distribution of bootstrap replicates is the same as that of the estimator itself. It follows that the bootstrap is valid.
A few remarks are in order. First, a more recent strain of literature considers bootstrapping methods for the regression discontinuity design without making parametric assumptions about the potential outcome surfaces or the treatment probability model (Calonico et al. (2014); Chiang et al. (2017); He and Bartalotti (2020)). Our proof of Theorem 3.6 requires stronger conditions in order to establish bootstrap validity. Absent these assumptions, under-coverage is plausible for the bootstrap intervals derived for T (·) for a fixed value of H. However, several steps in the algorithm -the convex relaxation, and the union over all possible intervals -may widen our bounds more than is strictly necessary for coverage. Hence, in cases where the chosen basis expansion is reasonably close to the true model, we still expect our intervals to achieve close-to-nominal coverage.
Second, the proposed procedure accounts for uncertainty in the estimation of the causal effect, but not for uncertainty in the estimation of the un-manipulated histogram. If there is relatively little data near the threshold c, there may be substantial variability in the histogram estimation step. An alternative procedure would involve bootstrapping from the entire dataset and re-estimating the un-manipulated histogram within each replicate. Such a procedure would yield wider bounds than the one we propose here.

Application: The Effect of Deferrals on Blood Donation Rates
We consider a real-world application of our method: estimating the effect of participant deferral on future volunteerism in the blood donation setting. We analyze data collected among female 4 donors at blood banks in the United Arab Emirates over a period of five years.

Background
Charitable organizations rely heavily on volunteer labor. However, in some cases, volunteer labor yields fewer benefits to these organizations than the total costs of volunteering. For example, there may be many volunteering costs -e.g. training, insurance, and transportation -which could exceed the benefits. In these cases, volunteer organizations may seek to reject volunteers in order to preserve resources. Such a policy is optimal only if the rejections do not affect volunteers' future propensity for volunteerism. If rejections today could fuel future volunteer shortages, this would not be an optimal policy in the long term. A challenge to identifying the causal effect of rejecting volunteers on future behavior is that rejections may occur for reasons that directly affect future volunteering behavior. For instance, individuals might be rejected because they are less prepared to be successful volunteers. In this case, rejections are correlated with a lower propensity for future volunteering, but this is because rejected individuals have lower utility for volunteering rather than because the rejections themselves cause decreased future participation. Rejections may also provide information to donors that would affect their beliefs about the value of their effort or the likelihood of being rejected again. In these cases, volunteers would be less likely to donate in the future.
Given these challenges, empirical evidence on the effect of turning away volunteers is scant. One context that has received attention in identifying the effect of temporary rejections (henceforth "deferrals") on future volunteering is blood donations. The marginal costs of collecting a unit of blood are non-trivial. But, because the prevailing view across blood banks is that deferring donors will reduce future donations, donors are rarely deferred for non-medical reasons. This practice has led to wastage in periods of excess supply, since donated blood can only be stored for a limited amount of time (see e.g. Slonim et al., 2014). For example, after the 9/11 attacks, the American Red Cross allowed donors across the USA to donate in large numbers. The blood was largely not needed, and this policy led to 200,000 units of discarded blood (Korcok, 2002).
The evidence presented to date suggests that there is a negative relationship between receiving a temporary deferral and future donations. However, much of this early work has not identified whether the relationship is causal (e.g. Custer et al., 2007).

RDD Construction and Manipulation
We identify the causal effect of deferrals on return behavior by exploiting a discontinuity in the blood donor's eligibility criteria. When volunteers attempt to donate blood, their hemoglobin levels (henceforth "h-levels") are measured. If the h-level is below an eligibility threshold (12.5 g/dL for female donors in the UAE), the donor is ineligible to donate blood and receives a temporary deferral. Thus, the h-level threshold provides a natural experiment to identify the causal effect of the temporary deferral using a regression discontinuity design.
We are not the first to exploit this structure as an RD design. Bruhin et al. (2020) utilize the same discontinuity in h-level on a different dataset of blood donors to estimate the causal relationship between deferral and return behavior. However, a critical assumption of the RD design -that the running variable is not manipulated -is a threat to identification.
For instance, suppose blood center staff manipulate the h-levels of certain types of individuals -say, regular donors or healthier-looking volunteers -over the threshold. If this occurs, we can no longer claim that donors just above and below the threshold are similar. Thus, estimates from the RD design will suffer from selection bias due to the manipulation and will be unreliable. As we will show below, the running variable is indeed manipulated in our dataset (see Figure 1) and there are reasons to believe that it is also manipulated in Bruhin et al. (2020)'s dataset. 5 We address the selection bias from manipulation with our new method and provide bounds on the treatment effect.

Recovering the un-manipulated distribution
We do not know the precise range of hemoglobin levels for which manipulation occurred. Hence, we take an approach similar to that of Diamond and Persson (2016) in seeking to automatically identify the manipulation region and obtain the un-manipulated histogram. We will discuss the process used for estimation for the sample of all female donors.
We consider twelve possible manipulation windows. The narrowest window contains only hemoglobin levels 12.4 (just below the donation cutoff) and 12.5 (the cutoff exactly). The widest window extends from hemoglobin level 12.1 to 12.7. Our modeling strategy makes use of a constrained Poisson model to estimate the density. The model is fit to the histogram points outside the manipulation window, and the un-manipulated histogram is recovered by obtaining the model's predictions for points within the manipulation window.
The Poisson models are fit by predicting the density from a spline expansion of the hemoglobin level. The models are constrained so that they meet the following intuitive requirements: • The predicted counts must be greater than or equal to the observed counts for hemoglobin levels within the manipulation window but below the cutoff; and lesser than or equal to the observed counts for hemoglobin levels within the manipulation window but above the cutoff.
• The total number of predicted units within the manipulation window must equal the total number of observed units within the window.
For predictors, we consider a cubic spline expansion of the hemoglobin levels, with anywhere from 3 to 15 degrees of freedom. For each possible manipulation window, we perform a five-fold cross-validation in order to select the optimal spline degree. This means hemoglobin levels outside the manipulation window are randomly split into five equally sized folds, and the constrained Poisson model of a given spline order is iteratively fit to all but one fold. Predictions are made on the held-out fold, and the total sum of squared errors is computed.
Visually, we observe that the raw data histograms exhibit substantial bunching at hemoglobin levels equal to whole numbers (e.g. 13.0). This makes intuitive sense, as donation center employees may be inclined to round reported hemoglobin levels. To better fit the observed data, we include a term in our model to account for the whole number bunching, yielding spikes in the fitted histogram. We interpret our un-manipulated histogram as estimating what the distribution would have been, had there not been manipulation to explicitly authorize low-hemoglobin individuals to donate, but had the usual rounding effects remained.
We select the (manipulation region-degrees of freedom) pair that has the minimum SSE. This turns out to be achieved with manipulation region 12.1-12.6 and 10 degrees of freedom. The fitted histogram can be seen in Figure 1. The plot largely matches our visual intuition for what the un-manipulated histogram should look like.
Crucially, these results imply that there are 692 manipulators for whom the observed hemoglobin level is 12.5 (715 honest donors vs. 1,407 observed donors) and 91 manipulators for whom the observed hemoglobin level is 12.6 (746 honest donors vs. 837 observed donors). We assume this is a full set of manipulators.

Partial Identification Bounds
We proceed with the estimation, using a local polynomial regression of order one to estimate both the numerator and denominator ofτ f (c) at the cutoff. Local weighting is implemented using tricubic weights.
Converting this problem to the form of Optimization Problem 6, we obtain the partial identification region of (0.055, 0.169) for the causal effect of attempting a donation on the probability of attempting another donation within one year. We obtain slightly wider bounds of (0.044, 0.185) for the probability of attempting another donation within the period of our data.
The effect of our method is visualized in Figure 2, where we focus on the causal effect on attempting a donation within one year. The upper panel displays the LOESS curve fits for the outcome as a function of the running variable (the numerator of our causal Figure 1: Histogram of hemoglobin levels for female donors. The bars in gray represent our manipulation window, while the bars in black represent levels outside the window. In red, we provide the estimated un-manipulated histogram. effect estimate); the lower panel displays the LOESS curve fits for the treatment as a function of the running variable (the denominator of our causal effect estimate).
The impact of the exclusions induced by our optimization problem can be seen most clearly in the upper panel. The upper bound on the causal effect is obtained primarily by tagging as manipulators those women for whom the hemoglobin level is 12.5 and who did not attempt to donate again in one year. These women are then excluded from the estimation, resulting in the upward curvature of the green line as it approaches the cutoff from the right. Similarly, the lower bound is obtained by tagging as manipulators those women for whom the hemoglobin level is 12.5 and who did attempt to donate again in one year. Their exclusion yields the downward curvature of the red line as it approaches the cutoff from the right.
In the lower panel, we see that the exclusions do not dramatically affect the LOESS fit for the treatment indicator as a function of the running variable. The LOESS curves diverge only slightly as they approach the cutoff from the right.

Inference
We can also use the bootstrap procedure from Section 3.6 to obtain a 95% confidence interval for each of the causal effects. The 95% CI for the effect of donation acceptance on attempting another donation within one year is (0.036, 0.190). The corresponding interval for the probability of attempting another donation at all is (0.025, 0.210). Notably, the left ends of these intervals still do not include zero.
In Appendix Section A.1, we confirm that the results are quite stable across different choices of manipulation region. In Appendix Section A.3 we rerun our procedure with three choices of control variables: height, weight, and age. Because none of these variables could plausibly be affected by donation deferral, we expect to see the partial identification regions and confidence intervals contain zero -and they do, across all choices of the manipulation region.
Taken together, these results underscore the robustness of the causal effect of deferral on donation probability: even under worst-case bounds, we still estimate an effect greater than zero. Moreover, we do not see the same pattern when considering placebo variables.
For practitioners, we envision taking precisely this analytical approach when dealing with RD designs with evidence of manipulation. Running our optimization procedure, the analyst can confirm that the effect is robust even in the presence of manipulation. Such an approach is significantly more credible than a donut hole approach alone, which excludes potentially informative data. Practically, we suggest reporting both the partial identification bounds and confidence intervals as part of the robustness check.

Classical approach: donut hole
In RDDs with manipulation, a common approach used in the literature is the donut hole design. Here, data within a window around the RDD threshold, known as the donut hole, is deleted and estimates are obtained at the threshold by extrapolation of the fitted functional form from outside the donut hole. We use our optimal manipulation region computed in Section 4.3, i.e. [12.1, 12.6] as the donut hole and delete all observations inside it. We then compute our RD point estimates and confidence intervals using the rdrobust R package (Calonico et al., 2014(Calonico et al., , 2015. Due to the nature of donut hole designs, which compute effects at the threshold where no data actually exists (by virtue of all data in its neighborhood being removed), the estimates can be very noisy due to a combination of extrapolation and sampling errors. Indeed, for our donut hole specification, for the causal effect of donation acceptance on the probability that the donor will attempt a return donation within a year, we obtain a 95% confidence interval of (−0.033, 0.191). Thus, with a donut hole regression, we are unable to reject the null of no treatment effect. For the outcome of any return donation at all, our 95% donut hole confidence interval is (0.019, 0.263). This interval is also significantly wider than the corresponding partial bounds interval we obtained in Section 4.5. We also perform a sensitivity analysis of the estimates with respect to the specification of the donut hole, which we reproduce in Appendix A.2.
These results show how our partial identification methodology for RDDs, even if not point identified, may provide tighter bounds for the causal effects of interest, and thereby more power to detect both signs of treatment effects and magnitude ranges. Given that the RDD is a data-intensive procedure, since it primarily looks at observations in a very narrow window around a cutoff, we believe this improvement in power as well as design transparency would be important to the empirical practitioner.

Discussion
This paper adds to the literature on regression discontinuity designs. Our contribution is a general method for deriving partial identification bounds of causal effects in RDDs with manipulation. We illustrate the utility of this method in an empirical application understanding the behavioral impacts of deferrals at blood banks.
As seen in Section 4.6, traditional approaches to RDDs with manipulation either ignoring manipulation (as in Bruhin et al. (2020)) or using donut-hole methods (as in Almond and Doyle (2011)) can be improved upon. Ignoring manipulation does not address the selection bias that ensues from manipulation, undermining the very causal nature that motivates an RD design. On the other hand, donut hole approaches to RDDs have fragile statistical properties. While a traditional RDD estimator is a careful tradeoff between bias and variance in a local polynomial estimator, the donut-hole estimator adds both high bias, from the misspecification of functional form, and high variance, from the extrapolation of the functional form (even if correctly specified) outside the support of the data used to fit the model. Instead, our partial bounds approach allows us to both maintain a causal interpretation of the RDD, and ensure low variance because we do not discard all the data in the manipulation region, only those that might plausibly be associated with manipulation. Further, by providing a range of possible causal estimates in the face of manipulation, our approach adds to the transparency and credibility of the RDD by not claiming point identification with immoderate assumptions. Our empirical results document important behavioral responses in how volunteer labor supply operates. Using the context of blood donations, we document that deferrals do in fact have a negative causal effect on the likelihood that a donor will return to donate in the future. That we are able to make this inference highlights the persuasiveness of partial bounds in causal studies where point identification is not possible.
While we have estimated the effect of deferrals on donors overall, it would be important to document what kinds of donors are most sensitive in their return donation rate. An understanding of this heterogeneity would inform leaders in blood banks in designing effective policies that dynamically balance demand and supply over time, while reducing wastage. More generally, we derive partial bounds that account for the uncertainty in identifying compliers as well as sampling uncertainty, conditional on correctly identifying the amount of manipulation. We further show the robustness of our empirical results to various specifications and degrees of manipulation. It would be fruitful to have bounds that incorporate uncertainty in the estimation of manipulation mass directly in them, and to produce a theory of optimal (narrowest) bounds. We leave these exercises to future work.
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A Robustness checks A.1 Causal Effects Under Different Manipulation Regions
In Table 1, we apply our procedure across various choices of the manipulation region, with the optimal choice italicized below. We compute both partial identification regions and confidence intervals for twelve choices of the manipulation region. Generally, we find that results are quite stable, with none of the confidence regions overlapping zero.

A.2 Donut hole estimates
In this section, we study the sensitivity of the donut hole estimates for the causal effect of donation acceptance (i.e. on the donor not being deferred) on their probability of returning to the blood bank to attempt another donation within a year. For our candidate set of donut holes, we use the same specifications of the manipulation region as in Appendix A.1. For a given donut hole, we delete all observations within it and compute "robust" RD point estimates at the cutoff and 95% confidence intervals using the rdrobust R package. The results are reproduced in Table 2, with the preferred donut hole specification in italics.

A.3 Placebo Tests
In Tables 3, 4, and 5, we repeat the analysis for three placebo variables: weight, height, and age respectively. We again compute the partial identification bounds and confidence intervals for a range of manipulation regions, though the row corresponding to the optimal manipulation region is italicized.  We find that depending on the specification of the size and location of the donut hole, we may or may not reject the null hypothesis of no causal effects at the 95% confidence level.
Because there is no plausible relationship between deferral and these variables, we expect to see the intervals cover zero. For all three variables, the partial identification bounds indeed contain zero. The confidence intervals (which are wider) definitionally cover zero as well. This provides further evidence that the effect of deferral on return probability is truly nonzero, as our partial identification bounds and confidence intervals do not cover zero.