Appendix — Solutions — Problem Set 4.3 (Regression Discontinuity: Local-Polynomial Fitting and Bandwidth Experiments)

Full worked solutions to book/weeks/week-04/ps4.3.md. Notation follows CONVENTIONS §3 and Ch 4.3. Core objects: the running variable X and known cutoff c; the sharp treatment D_i=\mathbf 1\{X_i\ge c\}; the sharp-RD estimand \tau_{\text{SRD}}=\lim_{x\downarrow c}\mathbb{E}[Y\mid X=x]-\lim_{x\uparrow c}\mathbb{E}[Y\mid X=x] identified under continuity of the potential-outcome means \mathbb{E}[Y_i(1)\mid X=x], \mathbb{E}[Y_i(0)\mid X=x] at c; local linear estimation on a window |X_i-c|\le h with a triangular kernel; the bias–variance trade-off in h; the fuzzy-RD Wald ratio \tau_{\text{FRD}}=(\text{jump in }Y)/(\text{jump in }D) with instrument Z_i=\mathbf 1\{X_i\ge c\}; and the §9 validity-threat checklist. Citations used by name: Gelman, A. & Imbens, G. (2019), “Why High-Order Polynomials Should Not Be Used in Regression Discontinuity Designs,” Journal of Business & Economic Statistics 37(3), 447–456; Imbens, G. & Kalyanaraman, K. (2012), “Optimal Bandwidth Choice for the Regression Discontinuity Estimator,” Review of Economic Studies 79(3), 933–959; Calonico, S., Cattaneo, M. D. & Titiunik, R. (2014), “Robust Nonparametric Confidence Intervals for Regression-Discontinuity Designs,” Econometrica 82(6), 2295–2326; McCrary, J. (2008), “Manipulation of the Running Variable in the Regression Discontinuity Design: A Density Test,” Journal of Econometrics 142(2), 698–714. All arithmetic verified numerically.

Problem 1 — State the estimand and the identifying assumption (14 pts)

(a) (3 pts) With cutoff c=660, the sharp-RD estimand is the jump in the conditional-mean function of Y at the cutoff: \tau_{\text{SRD}}=\lim_{x\downarrow 660}\mathbb{E}[Y\mid X=x]-\lim_{x\uparrow 660}\mathbb{E}[Y\mid X=x]. The first term is the limiting average distress as you approach 660 from above (the approved side); the second is the limiting average as you approach from below (the rejected side). Their difference is a treatment effect, not just a slope, because the running variable X is continuous through 660 and enters the outcome smoothly — the smooth influence of “having a slightly higher score” is the same on both sides as x\to 660 and cancels in the difference, so the only thing that can open a gap between the two one-sided limits is approval switching from 0 to 1 at exactly 660.

(b) (4 pts) Continuity: the average potential outcomes are continuous functions of X at the cutoff, \mathbb{E}[Y_i(1)\mid X=x]\quad\text{and}\quad \mathbb{E}[Y_i(0)\mid X=x]\quad\text{are continuous in }x\text{ at }x=660. In plain words: had the cutoff sat slightly higher (so a barely-approved applicant had instead been rejected), that applicant’s distress would have evolved smoothly through 660 with no jump — the world does not put a cliff in the outcome at 660 except through approval itself. The function we never directly observe on the treated side is the untreated potential outcome \mathbb{E}[Y_i(0)\mid X=x] for the approved applicants (we cannot see how an approved person would have done unapproved); continuity says the just-below-cutoff (rejected) applicants supply that missing counterfactual in the limit.

(c) (4 pts) CIA (Week 3) demands that treated and untreated units be comparable after conditioning on a complete set of observed covariates — an untestable claim that no unobserved confounder is left, holding everywhere across the covariate space. Continuity demands far less: comparability only in the limit, exactly at the cutoff, secured by a smoothness condition on the potential-outcome means at one point. That is easier to defend because it does not require you to have measured and controlled for every confounder; it only requires that nothing jumps discontinuously at c except treatment — and, as Problems 5–6 show, that requirement leaves observable fingerprints (a smooth density, balanced covariates) that you can actually go and check, unlike CIA’s blanket no-unobservables claim.

(d) (3 pts) \tau_{\text{SRD}} is the average effect of approval for applicants right at X=660 — the marginal borrowers at the cutoff, not all approved borrowers and not deep-subprime or deep-prime applicants far from the line. This local estimand is exactly the right number for a regulator deciding whether to move the cutoff to 650, because the people who would be newly affected by relocating the threshold are precisely the marginal applicants near it, and \tau_{\text{SRD}} is their effect.

Problem 2 — A by-hand local-linear RD (20 pts)

(a) (6 pts) Control-side line through (-3,5.2) and (-1,5.4). Two-point slope: b_-=\frac{5.4-5.2}{-1-(-3)}=\frac{0.2}{2}=\boxed{0.10}\ \text{(% per rank)}. Solve for the intercept using (-1,5.4): 5.4=a_-+0.10\,(-1)\Rightarrow a_-=5.4+0.10=\boxed{5.5}. (Check with (-3): 5.5+0.10(-3)=5.2 ✓.) The extrapolated control-side height at the cutoff is the intercept, \lim_{x\uparrow 0}\widehat{\mathbb{E}}[Y\mid X=x]=a_-=\boxed{5.5}.

(b) (6 pts) Treated-side line through (+1,5.9) and (+3,6.1). Slope: b_+=\frac{6.1-5.9}{3-1}=\frac{0.2}{2}=\boxed{0.10}\ \text{(% per rank)}. Intercept using (+1,5.9): 5.9=a_++0.10(1)\Rightarrow a_+=5.9-0.10=\boxed{5.8}. (Check with (+3): 5.8+0.10(3)=6.1 ✓.) The extrapolated treated-side height at the cutoff is \lim_{x\downarrow 0}\widehat{\mathbb{E}}[Y\mid X=x]=a_+=\boxed{5.8}.

(c) (4 pts) The estimated jump is \hat\tau_{\text{SRD}}=a_+-a_-=5.8-5.5=\boxed{0.30}\ \text{percentage points}. This is not the difference of the two nearest bins (5.9-5.4=0.5) because those two bins sit at x=+1 and x=-1, not at the cutoff x=0. The local-linear fit corrects for the fact that the outcome is trending on each side: it extrapolates each side’s line to the boundary x=0 before differencing, removing the part of the nearest-bin gap that is just the smooth slope of Y in X carrying you from -1 to +1, rather than the treatment.

(d) (4 pts) The nearest-bin difference (0.5) is bigger than the local-linear jump (0.30). Both side-trends slope upward (each slope is +0.10 per rank), so as you move from the control bin at x=-1 rightward to the treated bin at x=+1, the outcome rises for two reasons mixed together: the genuine treatment jump and two ranks’ worth of the rising smooth trend (2\times 0.10=0.20). The nearest-bin shortcut attributes all of that 0.5 to treatment, so it is biased upward by exactly the 0.20 of trend it failed to subtract; the local-linear fit, by extrapolating to the common point x=0, nets out the trend and leaves the clean 0.30. (The triangular kernel would not change anything here: a kernel reweights observations, but two points already determine a unique straight line, so any positive weights produce the same line through them.)

Problem 3 — Bandwidth, bias, variance, and the global-polynomial trap (18 pts)

(a) (5 pts) As h goes from 4 to 32: - Standard error falls (0.18\to 0.07). A wider window admits many more observations, and each fitted side-line is then estimated from far more points, so its sampling variability — and the variability of the boundary heights you difference — shrinks. More data, less noise: lower variance. - Bias rises (\hat\tau drifts from 0.56 away from the truth 0.60, down to 0.41). The smooth part of \mathbb{E}[Y\mid X] is convex on the treated side. A straight line fit over a wide treated window cannot follow that upward curve; it under-reads the treated-side curve’s height at the boundary, pulling a_+ — and hence the jump — too low. The wider the window, the more curvature the line must ignore, so higher bias. This is the bias–variance trade-off made numerical: too narrow is honest-but-noisy, too wide is precise-but-wrong.

(b) (3 pts) Naive 95\% intervals \hat\tau\pm 1.96\,\widehat{\text{se}}: h=4:\quad 0.56\pm 1.96(0.18)=0.56\pm 0.353=[\,0.21,\ 0.91\,]\quad(\text{width }0.71), h=32:\quad 0.41\pm 1.96(0.07)=0.41\pm 0.137=[\,0.27,\ 0.55\,]\quad(\text{width }0.27). An honest analyst prefers the h=4 window: its interval is wide but it is centered near the truth and actually contains 0.60, whereas the tight h=32 interval is mis-centered and excludes the true 0.60 entirely. “Narrow” measures only precision (how reproducible the estimate is); it says nothing about accuracy (whether the estimate is aimed at the right number) — a confidently-stated wrong answer is still wrong.

(c) (5 pts) The global quartic returns the same biased point (\approx 0.41) with a tight standard error — precise and wrong. Gelman–Imbens (2019) give three reasons a high-order global polynomial mis-estimates a boundary value: (i) polynomials behave erratically near the edges of the data, and the cutoff is exactly where two one-sided extrapolations meet; (ii) it lets data far from the cutoff (huge R1000 firms, tiny deep-R2000 firms) dictate the curvature right at c, manufacturing spurious wiggles or erasing real jumps at the boundary; (iii) the estimate is hostage to the arbitrary polynomial order, swinging between a cubic and a quartic with no principled way to choose, and the implicit weights on individual observations can even go negative. The “deceptively tight standard error around a wrong number” is the lesson in miniature: the global fit uses all 6{,}000 points so its variance is small, but it is estimating the wrong object (a boundary height corrupted by distant data), so small se buys you nothing — precision around a biased target is just confident inaccuracy.

(d) (5 pts) (i) Imbens–Kalyanaraman (2012) choose the bandwidth that minimizes the asymptotic mean squared error (MSE) of the RD estimator — they estimate the two ingredients of MSE (the curvature of the outcome function at c, which drives bias, and the noise variance, which drives variance) and plug them into the optimal-h formula. Because MSE = (bias)^2 + variance, minimizing it deliberately accepts some non-zero bias to buy a large variance reduction; the MSE-optimal h is, by construction, large enough that the leading bias term is not negligible. (ii) That leftover bias breaks the naive interval, because \hat\tau\pm 1.96\,\widehat{\text{se}} assumes the estimator is centered on the truth — at the MSE-optimal h it is not, so the interval is mis-located and undercovers (contains the true effect less than 95\% of the time). Calonico–Cattaneo–Titiunik (2014) robust bias-correction does two things: (1) it estimates the leading bias term explicitly and subtracts it from the point estimate (bias correction), and (2) it inflates the standard error to account for the extra noise that the bias-correction step itself introduces (the “robust” standard error). The repaired interval then achieves its nominal 95\% coverage even at the MSE-optimal bandwidth — fixing the undercoverage of the naive interval.

Problem 4 — Fuzzy RD as the Wald ratio (18 pts)

(a) (4 pts) Jump in treatment (first stage) and jump in outcome (reduced form) at c=0: \text{jump in }D=\lim_{x\downarrow 0}\mathbb{E}[D\mid X]-\lim_{x\uparrow 0}\mathbb{E}[D\mid X]=0.70-0.30=\boxed{0.40}, \text{jump in }Y=\lim_{x\downarrow 0}\mathbb{E}[Y\mid X]-\lim_{x\uparrow 0}\mathbb{E}[Y\mid X]=61.0-57.4=\boxed{3.6}. The treatment jump is the empirical content of relevance — the fuzzy-RD analog of the first stage. A jump of 0.40 (treatment probability rising from 30\% to 70\% at the cutoff) is reassuring: it is a substantial, visible discontinuity, far from the near-zero denominator that would invite the weak-instrument pathology.

(b) (4 pts) The fuzzy-RD estimand is the ratio of the two jumps: \hat\tau_{\text{FRD}}=\frac{\text{jump in }Y}{\text{jump in }D}=\frac{61.0-57.4}{0.70-0.30}=\frac{3.6}{0.40}=\boxed{9.0}\ \text{governance-index points}. Interpretation: crossing the cutoff raised the governance index by 3.6 points but only moved an extra 40\% of firms into heavy passive ownership; scaling the reduced form up by the dose of treatment delivered, heavy passive ownership raises the governance index by about 9 points — for the firms the cutoff actually moved into treatment (the compliers at the cutoff), under monotonicity, not for all firms.

(c) (4 pts) The instrument is Z_i=\mathbf 1\{X_i\ge 0\}, the indicator for landing on the Russell-2000 (above-cutoff) side. The mapping to Week 3: - the jump in D (0.40) is the first stage — the effect of the instrument (crossing the cutoff) on the treatment; - the jump in Y (3.6) is the reduced form — the effect of the instrument on the outcome, ignoring D. \hat\tau_{\text{FRD}} is literally the Wald estimator of Ch 3.4, \hat\beta_1^{\text{Wald}}=(\text{reduced form})/(\text{first stage}), with the above-cutoff indicator playing the role of the randomized instrument: fuzzy RD is instrumental variables where the instrument is “which side of c you landed on.”

(d) (3 pts) Exclusion here means: crossing the rank cutoff must affect the governance index only through the treatment (heavy passive ownership), and nothing else may jump at c. A concrete violation: if crossing into the Russell 2000 also triggers, at the same rank, a change in analyst-coverage or index-reconstitution disclosure rules that independently affects governance, then Z reaches Y by a second road that bypasses D, and the Wald ratio is contaminated. This is an instance of the compound-treatment threat (§9, Threat 3) — for a fuzzy design, exclusion is the no-other-channel requirement.

(e) (3 pts) With the treatment jump collapsing to 0.05 while the outcome jump stays near 3.6, the point estimate balloons to 3.6/0.05=72 — the ratio becomes enormous and unstable because you are dividing by a near-zero first stage. Far worse, the precision collapses: the standard error of a ratio explodes as its denominator approaches zero, so the confidence interval blows up and the estimate becomes untrustworthy. This is the weak-instrument pathology of Ch 3.5, in RD clothing — a weak first stage (tiny treatment jump) makes the IV/Wald estimate both wildly imprecise and maximally vulnerable to any small exclusion violation.

Problem 5 — The McCrary density test and manipulation (16 pts)

(a) (4 pts) The McCrary (2008) density test estimates the density of the running variable X (here, credit scores) separately on each side of the cutoff — a local-linear density estimator on the left and on the right — and tests whether the two estimated densities agree at c. The null hypothesis is that the density of X is continuous at 660 (no sorting). Rejecting the null means there is a jump in the density at the cutoff — evidence of manipulation. You hope to fail to reject: a smooth density is consistent with the clean, no-manipulation story in which applicants cannot finely control which side of 660 they land on.

(b) (4 pts) If capable applicants sort from just-below to just-above 660, the histogram develops a characteristic two-sided distortion at the cutoff: too few observations pile up in the bins immediately below 660 (those people moved out) and too many in the bins immediately above 660 (that is where they moved to). The result is a visible cliff in the histogram of X exactly at 660 — a downward step on the left, an upward step on the right. That is the link from “sorting”: units relocating across the line deplete one side and overfill the other, which is a discontinuity in the density at c, precisely what McCrary’s test is built to detect. Under the no-manipulation story the density should pass through 660 smoothly (people don’t bunch at a threshold they can’t control).

(c) (4 pts) Sorting breaks the design even though approval still flips cleanly at 660, because RD’s credibility rests on local randomization / continuity, not on the sharpness of the treatment rule. The just-above group becomes enriched with strategic, more financially-capable applicants — the ones who knew to pay down a balance to cross the line — precisely the kind of unobserved characteristic (sophistication, resources) that continuity assumes is balanced across the cutoff. Once the just-above group is systematically more capable than the just-below group, the two are no longer exchangeable: they differ in a confounder, not just in treatment. The resulting \hat\tau_{\text{SRD}} then mixes the causal effect of approval with a selection effect — the capability gap between movers and stayers — so the jump no longer cleanly identifies the treatment.

(d) (4 pts) (i) A passed density test is necessary but not sufficient because it rules out only the crudest fingerprint of sorting — a discontinuity in the density — but cannot by itself prove the design is clean: sorting that happens to preserve the density (contrived but logically possible), or any threat that does not move the density, slips right past it. A smooth density is a hurdle the design must clear, not a certificate that it is valid. (ii) One §9 threat a passed density test cannot rule out at all is the compound-treatment threat (Threat 3): if some other policy changes at the same cutoff, the density of X stays perfectly smooth (nobody is sorting), yet the design is broken — exactly the case Problem 6 develops. (Covariate imbalance, Threat 2, is likewise invisible to the density test.)

Problem 6 — Validity threats: the compound-treatment critique (14 pts)

(a) (4 pts) This is the compound-treatment threat (§9, Threat 3): the same threshold c=660 triggers more than one thing at once — approval and the rate switch and securitization eligibility. The one-sentence identification condition it violates is the through-line of §9: RD is identified by the assumption that crossing the cutoff changes one thing and only one thing, smoothly in everything else. Here three things change at 660, so that assumption fails.

(b) (4 pts) No statistical test can detect a compound treatment because every test in the kit checks for some discontinuity, and here all the discontinuities are real and all happen at the same point — there is nothing anomalous to flag. McCrary sees a smooth density (nobody is sorting). Covariate balance sees no jump (pre-determined characteristics really are balanced). A donut RD still finds the jump (it isn’t driven by exactly-at-the-line cases). A bandwidth sweep finds the jump stable (it is a genuine effect of crossing 660). The contrast with the manipulation threat of Problem 5 is exactly this: manipulation leaves a statistical fingerprint (a density discontinuity) that a test can catch, whereas a compound treatment leaves none — the jump is real, it is simply the effect of the bundle. Maya must therefore use institutional evidence: documentation of how the underwriting rule actually works, to establish what does and does not change at 660 — exactly as the exclusion restriction is argued, not tested, in Week 3.

(c) (3 pts) Maya’s RD still identifies a real causal effect — the effect of crossing the 660 threshold, i.e. the effect of the bundle (approval + the switch to a lower variable rate + securitization eligibility) taken together, for applicants at the cutoff: \hat\tau=\text{effect on default of the entire }660\text{-cutoff package, at the margin.} It is not the “effect of approval” she wanted, because approval is only one of three things that flip at 660; she cannot attribute the default jump to approval alone when the rate change and securitization moved in lockstep with it.

(d) (3 pts) In a fuzzy design with Z=\mathbf 1\{X\ge 660\} as the instrument for approval, the compound treatment breaks exclusion. Exclusion requires that crossing 660 affect default only through approval; but the rate switch and securitization give crossing 660 additional channels to default that bypass approval, so \operatorname{Cov}(Z,\varepsilon)\ne 0 and the Wald ratio is contaminated — it scales up a reduced form that already includes the rate and securitization effects, mis-crediting all of them to approval.

End of solutions for PS 4.3. Cross-references: Ch 4.3 (sharp-RD estimand & continuity §2–§3, fuzzy RD/Wald ratio §4, local linear vs. global polynomial / Gelman–Imbens §5, bandwidth bias–variance & IK/CCT §6, reading the RD plot §7, McCrary density test §8, validity threats §9, Russell sharp-vs-fuzzy wrinkle §10, code §11); Ch 3.1 (potential outcomes); Ch 3.4 (Wald estimator, relevance/exclusion, LATE/compliers, monotonicity); Ch 3.5 (weak-instrument pathology, here the collapsing first-stage jump of P4(e)). Numeric keys: P2 control line b_-=0.10, a_-=5.5; treated line b_+=0.10, a_+=5.8; jump \hat\tau_{\text{SRD}}=0.30 (vs. nearest-bin 0.5, biased up by 0.20 of trend). P3 naive CIs h{=}4:[0.21,0.91] (brackets truth 0.60), h{=}32:[0.27,0.55] (excludes 0.60). P4 jump in D=0.40, jump in Y=3.6, \hat\tau_{\text{FRD}}=9.0; weak case 3.6/0.05=72. Companion: nb4.3 (rdrobust, CCT bandwidth, rdplot, density test, fuzzy IV/Wald).

# Solutions — Problem Set 4.3 (Regression Discontinuity: Local-Polynomial Fitting and Bandwidth Experiments) *Full worked solutions to `book/weeks/week-04/ps4.3.md`. Notation follows CONVENTIONS §3 and Ch 4.3. Core objects: the running variable $X$ and known cutoff $c$; the sharp treatment $D_i=\mathbf 1\{X_i\ge c\}$; the **sharp-RD estimand** $\tau_{\text{SRD}}=\lim_{x\downarrow c}\mathbb{E}[Y\mid X=x]-\lim_{x\uparrow c}\mathbb{E}[Y\mid X=x]$ identified under **continuity** of the potential-outcome means $\mathbb{E}[Y_i(1)\mid X=x]$, $\mathbb{E}[Y_i(0)\mid X=x]$ at $c$; **local linear** estimation on a window $|X_i-c|\le h$ with a **triangular kernel**; the bias–variance trade-off in $h$; the **fuzzy-RD** Wald ratio $\tau_{\text{FRD}}=(\text{jump in }Y)/(\text{jump in }D)$ with instrument $Z_i=\mathbf 1\{X_i\ge c\}$; and the §9 validity-threat checklist. Citations used by name: Gelman, A. & Imbens, G. (2019), "Why High-Order Polynomials Should Not Be Used in Regression Discontinuity Designs," Journal of Business & Economic Statistics 37(3), 447–456; Imbens, G. & Kalyanaraman, K. (2012), "Optimal Bandwidth Choice for the Regression Discontinuity Estimator," Review of Economic Studies 79(3), 933–959; Calonico, S., Cattaneo, M. D. & Titiunik, R. (2014), "Robust Nonparametric Confidence Intervals for Regression-Discontinuity Designs," Econometrica 82(6), 2295–2326; McCrary, J. (2008), "Manipulation of the Running Variable in the Regression Discontinuity Design: A Density Test," Journal of Econometrics 142(2), 698–714. All arithmetic verified numerically.* --- ## Problem 1 — State the estimand and the identifying assumption (14 pts) **(a) (3 pts)** With cutoff $c=660$, the sharp-RD estimand is the jump in the conditional-mean function of $Y$ at the cutoff: $$ \tau_{\text{SRD}}=\lim_{x\downarrow 660}\mathbb{E}[Y\mid X=x]-\lim_{x\uparrow 660}\mathbb{E}[Y\mid X=x]. $$ The first term is the limiting average distress as you approach $660$ from **above** (the approved side); the second is the limiting average as you approach from **below** (the rejected side). Their difference is a treatment effect, not just a slope, because the running variable $X$ is *continuous through* $660$ and enters the outcome smoothly — the smooth influence of "having a slightly higher score" is the *same* on both sides as $x\to 660$ and cancels in the difference, so the only thing that can open a gap between the two one-sided limits is approval switching from $0$ to $1$ at exactly $660$. **(b) (4 pts)** **Continuity:** the average potential outcomes are continuous functions of $X$ at the cutoff, $$ \mathbb{E}[Y_i(1)\mid X=x]\quad\text{and}\quad \mathbb{E}[Y_i(0)\mid X=x]\quad\text{are continuous in }x\text{ at }x=660. $$ In plain words: *had the cutoff sat slightly higher* (so a barely-approved applicant had instead been rejected), that applicant's distress would have evolved **smoothly** through $660$ with no jump — the world does not put a cliff in the outcome at $660$ except through approval itself. The function we never directly observe on the treated side is the **untreated** potential outcome $\mathbb{E}[Y_i(0)\mid X=x]$ for the approved applicants (we cannot see how an approved person would have done *unapproved*); continuity says the just-**below**-cutoff (rejected) applicants supply that missing counterfactual in the limit. **(c) (4 pts)** CIA (Week 3) demands that treated and untreated units be comparable **after conditioning on a complete set of observed covariates** — an untestable claim that *no* unobserved confounder is left, holding *everywhere* across the covariate space. Continuity demands far less: comparability only **in the limit, exactly at the cutoff**, secured by a smoothness condition on the potential-outcome means at one point. That is easier to defend because it does not require you to have measured and controlled for every confounder; it only requires that nothing *jumps discontinuously* at $c$ except treatment — and, as Problems 5–6 show, that requirement leaves observable fingerprints (a smooth density, balanced covariates) that you can actually go and check, unlike CIA's blanket no-unobservables claim. **(d) (3 pts)** $\tau_{\text{SRD}}$ is the average effect of approval **for applicants right at $X=660$** — the *marginal* borrowers at the cutoff, not all approved borrowers and not deep-subprime or deep-prime applicants far from the line. This local estimand is exactly the right number for a regulator deciding whether to move the cutoff to $650$, because the people who would be newly affected by relocating the threshold are precisely the marginal applicants near it, and $\tau_{\text{SRD}}$ is their effect. --- ## Problem 2 — A by-hand local-linear RD (20 pts) **(a) (6 pts)** Control-side line through $(-3,5.2)$ and $(-1,5.4)$. Two-point slope: $$ b_-=\frac{5.4-5.2}{-1-(-3)}=\frac{0.2}{2}=\boxed{0.10}\ \text{(% per rank)}. $$ Solve for the intercept using $(-1,5.4)$: $5.4=a_-+0.10\,(-1)\Rightarrow a_-=5.4+0.10=\boxed{5.5}$. (Check with $(-3)$: $5.5+0.10(-3)=5.2$ ✓.) The extrapolated control-side height at the cutoff is the intercept, $$ \lim_{x\uparrow 0}\widehat{\mathbb{E}}[Y\mid X=x]=a_-=\boxed{5.5}. $$ **(b) (6 pts)** Treated-side line through $(+1,5.9)$ and $(+3,6.1)$. Slope: $$ b_+=\frac{6.1-5.9}{3-1}=\frac{0.2}{2}=\boxed{0.10}\ \text{(% per rank)}. $$ Intercept using $(+1,5.9)$: $5.9=a_++0.10(1)\Rightarrow a_+=5.9-0.10=\boxed{5.8}$. (Check with $(+3)$: $5.8+0.10(3)=6.1$ ✓.) The extrapolated treated-side height at the cutoff is $$ \lim_{x\downarrow 0}\widehat{\mathbb{E}}[Y\mid X=x]=a_+=\boxed{5.8}. $$ **(c) (4 pts)** The estimated jump is $$ \hat\tau_{\text{SRD}}=a_+-a_-=5.8-5.5=\boxed{0.30}\ \text{percentage points}. $$ This is *not* the difference of the two nearest bins ($5.9-5.4=0.5$) because those two bins sit at $x=+1$ and $x=-1$, not at the cutoff $x=0$. The local-linear fit corrects for the fact that the outcome is **trending** on each side: it extrapolates each side's line *to the boundary* $x=0$ before differencing, removing the part of the nearest-bin gap that is just the smooth slope of $Y$ in $X$ carrying you from $-1$ to $+1$, rather than the treatment. **(d) (4 pts)** The nearest-bin difference ($0.5$) is **bigger** than the local-linear jump ($0.30$). Both side-trends slope **upward** (each slope is $+0.10$ per rank), so as you move from the control bin at $x=-1$ rightward to the treated bin at $x=+1$, the outcome rises for *two* reasons mixed together: the genuine treatment jump *and* two ranks' worth of the rising smooth trend ($2\times 0.10=0.20$). The nearest-bin shortcut attributes all of that $0.5$ to treatment, so it is **biased upward** by exactly the $0.20$ of trend it failed to subtract; the local-linear fit, by extrapolating to the common point $x=0$, nets out the trend and leaves the clean $0.30$. (The triangular kernel would not change anything here: a kernel reweights observations, but two points already determine a unique straight line, so any positive weights produce the same line through them.) --- ## Problem 3 — Bandwidth, bias, variance, and the global-polynomial trap (18 pts) **(a) (5 pts)** As $h$ goes from $4$ to $32$: - **Standard error falls** ($0.18\to 0.07$). A wider window admits many more observations, and each fitted side-line is then estimated from far more points, so its sampling variability — and the variability of the boundary heights you difference — shrinks. More data, less noise: *lower variance*. - **Bias rises** ($\hat\tau$ drifts from $0.56$ away from the truth $0.60$, down to $0.41$). The smooth part of $\mathbb{E}[Y\mid X]$ is **convex on the treated side**. A straight line fit over a wide treated window cannot follow that upward curve; it under-reads the treated-side curve's *height at the boundary*, pulling $a_+$ — and hence the jump — too low. The wider the window, the more curvature the line must ignore, so *higher bias*. This is the bias–variance trade-off made numerical: too narrow is honest-but-noisy, too wide is precise-but-wrong. **(b) (3 pts)** Naive $95\%$ intervals $\hat\tau\pm 1.96\,\widehat{\text{se}}$: $$ h=4:\quad 0.56\pm 1.96(0.18)=0.56\pm 0.353=[\,0.21,\ 0.91\,]\quad(\text{width }0.71), $$ $$ h=32:\quad 0.41\pm 1.96(0.07)=0.41\pm 0.137=[\,0.27,\ 0.55\,]\quad(\text{width }0.27). $$ An honest analyst prefers the **$h=4$ window**: its interval is wide but it is *centered near the truth* and actually contains $0.60$, whereas the tight $h=32$ interval is mis-centered and **excludes** the true $0.60$ entirely. "Narrow" measures only *precision* (how reproducible the estimate is); it says nothing about *accuracy* (whether the estimate is aimed at the right number) — a confidently-stated wrong answer is still wrong. **(c) (5 pts)** The global quartic returns the same biased point ($\approx 0.41$) with a *tight* standard error — precise *and* wrong. **Gelman–Imbens (2019)** give three reasons a high-order global polynomial mis-estimates a boundary value: (i) polynomials behave **erratically near the edges** of the data, and the cutoff is exactly where two one-sided extrapolations meet; (ii) it lets data **far from the cutoff** (huge R1000 firms, tiny deep-R2000 firms) dictate the curvature right at $c$, manufacturing spurious wiggles or erasing real jumps at the boundary; (iii) the estimate is **hostage to the arbitrary polynomial order**, swinging between a cubic and a quartic with no principled way to choose, and the implicit weights on individual observations can even go negative. The "deceptively tight standard error around a wrong number" is the lesson in miniature: the global fit uses all $6{,}000$ points so its *variance* is small, but it is estimating the *wrong object* (a boundary height corrupted by distant data), so small se buys you nothing — precision around a biased target is just confident inaccuracy. **(d) (5 pts)** (i) **Imbens–Kalyanaraman (2012)** choose the bandwidth that **minimizes the asymptotic mean squared error (MSE)** of the RD estimator — they estimate the two ingredients of MSE (the curvature of the outcome function at $c$, which drives bias, and the noise variance, which drives variance) and plug them into the optimal-$h$ formula. Because MSE = (bias)$^2$ + variance, *minimizing* it deliberately accepts **some non-zero bias** to buy a large variance reduction; the MSE-optimal $h$ is, by construction, large enough that the leading bias term is **not negligible**. (ii) That leftover bias breaks the naive interval, because $\hat\tau\pm 1.96\,\widehat{\text{se}}$ assumes the estimator is centered on the truth — at the MSE-optimal $h$ it is not, so the interval is mis-located and **undercovers** (contains the true effect less than $95\%$ of the time). **Calonico–Cattaneo–Titiunik (2014)** robust bias-correction does two things: (1) it **estimates the leading bias term explicitly and subtracts it** from the point estimate (bias correction), and (2) it **inflates the standard error** to account for the extra noise that the bias-correction step itself introduces (the "robust" standard error). The repaired interval then achieves its nominal $95\%$ coverage even at the MSE-optimal bandwidth — fixing the undercoverage of the naive interval. --- ## Problem 4 — Fuzzy RD as the Wald ratio (18 pts) **(a) (4 pts)** Jump in treatment (first stage) and jump in outcome (reduced form) at $c=0$: $$ \text{jump in }D=\lim_{x\downarrow 0}\mathbb{E}[D\mid X]-\lim_{x\uparrow 0}\mathbb{E}[D\mid X]=0.70-0.30=\boxed{0.40}, $$ $$ \text{jump in }Y=\lim_{x\downarrow 0}\mathbb{E}[Y\mid X]-\lim_{x\uparrow 0}\mathbb{E}[Y\mid X]=61.0-57.4=\boxed{3.6}. $$ The treatment jump is the empirical content of **relevance** — the fuzzy-RD analog of the first stage. A jump of $0.40$ (treatment probability rising from $30\%$ to $70\%$ at the cutoff) is **reassuring**: it is a substantial, visible discontinuity, far from the near-zero denominator that would invite the weak-instrument pathology. **(b) (4 pts)** The fuzzy-RD estimand is the ratio of the two jumps: $$ \hat\tau_{\text{FRD}}=\frac{\text{jump in }Y}{\text{jump in }D}=\frac{61.0-57.4}{0.70-0.30}=\frac{3.6}{0.40}=\boxed{9.0}\ \text{governance-index points}. $$ Interpretation: crossing the cutoff raised the governance index by $3.6$ points but only moved an extra $40\%$ of firms into heavy passive ownership; scaling the reduced form up by the dose of treatment delivered, heavy passive ownership raises the governance index by about **$9$ points** — for the **firms the cutoff actually moved into treatment** (the compliers at the cutoff), under monotonicity, not for all firms. **(c) (4 pts)** The instrument is $Z_i=\mathbf 1\{X_i\ge 0\}$, the indicator for landing on the **Russell-2000 (above-cutoff) side**. The mapping to Week 3: - the **jump in $D$** ($0.40$) is the **first stage** — the effect of the instrument (crossing the cutoff) on the treatment; - the **jump in $Y$** ($3.6$) is the **reduced form** — the effect of the instrument on the outcome, ignoring $D$. $\hat\tau_{\text{FRD}}$ is *literally* the Wald estimator of Ch 3.4, $\hat\beta_1^{\text{Wald}}=(\text{reduced form})/(\text{first stage})$, with the above-cutoff indicator playing the role of the randomized instrument: fuzzy RD is instrumental variables where the instrument is "which side of $c$ you landed on." **(d) (3 pts)** **Exclusion** here means: crossing the rank cutoff must affect the governance index **only through** the treatment (heavy passive ownership), and nothing else may jump at $c$. A concrete violation: if crossing into the Russell 2000 *also* triggers, at the same rank, a change in **analyst-coverage or index-reconstitution disclosure rules** that independently affects governance, then $Z$ reaches $Y$ by a second road that bypasses $D$, and the Wald ratio is contaminated. This is an instance of the **compound-treatment** threat (§9, Threat 3) — for a fuzzy design, exclusion *is* the no-other-channel requirement. **(e) (3 pts)** With the treatment jump collapsing to $0.05$ while the outcome jump stays near $3.6$, the point estimate balloons to $3.6/0.05=72$ — the ratio becomes enormous and unstable because you are **dividing by a near-zero first stage**. Far worse, the *precision* collapses: the standard error of a ratio explodes as its denominator approaches zero, so the confidence interval blows up and the estimate becomes untrustworthy. This is the **weak-instrument pathology** of Ch 3.5, in RD clothing — a weak first stage (tiny treatment jump) makes the IV/Wald estimate both wildly imprecise and maximally vulnerable to any small exclusion violation. --- ## Problem 5 — The McCrary density test and manipulation (16 pts) **(a) (4 pts)** The **McCrary (2008) density test** estimates the **density of the running variable $X$** (here, credit scores) separately on each side of the cutoff — a local-linear density estimator on the left and on the right — and tests whether the two estimated densities **agree at $c$**. The **null hypothesis** is that the density of $X$ is *continuous at $660$* (no sorting). **Rejecting** the null means there is a jump in the density at the cutoff — evidence of **manipulation**. You *hope* to **fail to reject**: a smooth density is consistent with the clean, no-manipulation story in which applicants cannot finely control which side of $660$ they land on. **(b) (4 pts)** If capable applicants sort from just-below to just-above $660$, the histogram develops a characteristic two-sided distortion at the cutoff: **too few** observations pile up in the bins **immediately below** $660$ (those people moved out) and **too many** in the bins **immediately above** $660$ (that is where they moved to). The result is a visible **cliff in the histogram of $X$ exactly at $660$** — a downward step on the left, an upward step on the right. That is the link from "sorting": units relocating across the line deplete one side and overfill the other, which *is* a discontinuity in the density at $c$, precisely what McCrary's test is built to detect. Under the no-manipulation story the density should pass through $660$ smoothly (people don't bunch at a threshold they can't control). **(c) (4 pts)** Sorting breaks the design even though approval still flips cleanly at $660$, because RD's credibility rests on **local randomization / continuity**, not on the sharpness of the treatment rule. The just-**above** group becomes **enriched** with strategic, more financially-capable applicants — the ones who knew to pay down a balance to cross the line — precisely the kind of **unobserved characteristic** (sophistication, resources) that continuity assumes is *balanced* across the cutoff. Once the just-above group is systematically more capable than the just-below group, the two are **no longer exchangeable**: they differ in a confounder, not just in treatment. The resulting $\hat\tau_{\text{SRD}}$ then **mixes the causal effect of approval with a selection effect** — the capability gap between movers and stayers — so the jump no longer cleanly identifies the treatment. **(d) (4 pts)** (i) A passed density test is **necessary but not sufficient** because it rules out only the *crudest* fingerprint of sorting — a discontinuity in the *density* — but cannot by itself prove the design is clean: sorting that happens to preserve the density (contrived but logically possible), or any threat that does not move the density, slips right past it. A smooth density is a hurdle the design must clear, not a certificate that it is valid. (ii) One §9 threat a passed density test cannot rule out at all is the **compound-treatment** threat (Threat 3): if some *other* policy changes at the same cutoff, the density of $X$ stays perfectly smooth (nobody is sorting), yet the design is broken — exactly the case Problem 6 develops. (Covariate imbalance, Threat 2, is likewise invisible to the density test.) --- ## Problem 6 — Validity threats: the compound-treatment critique (14 pts) **(a) (4 pts)** This is the **compound-treatment** threat (§9, Threat 3): the *same* threshold $c=660$ triggers *more than one thing at once* — approval **and** the rate switch **and** securitization eligibility. The one-sentence identification condition it violates is the through-line of §9: **RD is identified by the assumption that crossing the cutoff changes one thing and only one thing, smoothly in everything else.** Here three things change at $660$, so that assumption fails. **(b) (4 pts)** No statistical test can detect a compound treatment because every test in the kit checks for *some discontinuity*, and here **all the discontinuities are real and all happen at the same point** — there is nothing anomalous to flag. McCrary sees a smooth density (nobody is sorting). Covariate balance sees no jump (pre-determined characteristics really are balanced). A donut RD still finds the jump (it isn't driven by exactly-at-the-line cases). A bandwidth sweep finds the jump stable (it is a genuine effect of crossing $660$). The contrast with the **manipulation** threat of Problem 5 is exactly this: manipulation leaves a *statistical fingerprint* (a density discontinuity) that a test can catch, whereas a compound treatment leaves **none** — the jump is real, it is simply the effect of the *bundle*. Maya must therefore use **institutional evidence**: documentation of how the underwriting rule actually works, to establish what does and does not change at $660$ — exactly as the exclusion restriction is argued, not tested, in Week 3. **(c) (3 pts)** Maya's RD still identifies a real causal effect — the effect of **crossing the $660$ threshold**, i.e. the effect of the *bundle* (approval + the switch to a lower variable rate + securitization eligibility) taken together, for applicants at the cutoff: $$ \hat\tau=\text{effect on default of the entire }660\text{-cutoff package, at the margin.} $$ It is **not** the "effect of approval" she wanted, because approval is only one of three things that flip at $660$; she cannot attribute the default jump to approval alone when the rate change and securitization moved in lockstep with it. **(d) (3 pts)** In a fuzzy design with $Z=\mathbf 1\{X\ge 660\}$ as the instrument for approval, the compound treatment breaks **exclusion**. Exclusion requires that crossing $660$ affect default *only through* approval; but the rate switch and securitization give crossing $660$ **additional channels to default that bypass approval**, so $\operatorname{Cov}(Z,\varepsilon)\ne 0$ and the Wald ratio is contaminated — it scales up a reduced form that already includes the rate and securitization effects, mis-crediting all of them to approval. --- *End of solutions for PS 4.3. Cross-references: Ch 4.3 (sharp-RD estimand & continuity §2–§3, fuzzy RD/Wald ratio §4, local linear vs. global polynomial / Gelman–Imbens §5, bandwidth bias–variance & IK/CCT §6, reading the RD plot §7, McCrary density test §8, validity threats §9, Russell sharp-vs-fuzzy wrinkle §10, code §11); Ch 3.1 (potential outcomes); Ch 3.4 (Wald estimator, relevance/exclusion, LATE/compliers, monotonicity); Ch 3.5 (weak-instrument pathology, here the collapsing first-stage jump of P4(e)). Numeric keys: P2 control line $b_-=0.10$, $a_-=5.5$; treated line $b_+=0.10$, $a_+=5.8$; jump $\hat\tau_{\text{SRD}}=0.30$ (vs. nearest-bin $0.5$, biased up by $0.20$ of trend). P3 naive CIs $h{=}4$:$[0.21,0.91]$ (brackets truth $0.60$), $h{=}32$:$[0.27,0.55]$ (excludes $0.60$). P4 jump in $D=0.40$, jump in $Y=3.6$, $\hat\tau_{\text{FRD}}=9.0$; weak case $3.6/0.05=72$. Companion: nb4.3 (rdrobust, CCT bandwidth, rdplot, density test, fuzzy IV/Wald).*