Appendix — Model Deliverable — PS 8.3 (An A-Grade Introduction + Headline-First Results Excerpt)

Problem set: book/weeks/week-08/ps8.3.md (PS 8.3, Week 8). Chapter: Ch 8.3 — Writing the Empirical Paper, held to the binding table-and-prose standard of Appendix D (book/appendices/D-style-guide/; D.1 table layout/notes, D.2 coefficient/FE/cluster/sample disclosure, D.5 prose-style and causal-language rules). Tool: nb8.3 (notebooks/week-08/nb8.3-publication-tables-figures.ipynb), which generates the headline table and event-study figure below to the Appendix D standard.

PS 8.3 has no single right answer — every camper’s introduction and results section is different because every camper’s project is different. What this manual provides instead is a model deliverable: one A-grade introduction and one headline-first results excerpt, written for Maya’s HMDA fair-lending project — the staggered difference-in-differences asking whether state fair-lending examination programs reduced the county-level minority–white mortgage-denial gap, the project carried since Week 1, whose identification memo students read in Ch 7.5 and whose robustness battery they ran in Ch 8.2. It shows the standard the writing must reach — front-load every verdict, match every verb to the weakest assumption, and build a headline table that stands alone — without dictating any camper’s question. Below the draft itself are instructor grading notes keyed to the writing rubric, component by component, with the common failure modes flagged.

A standing rule on numbers. Unlike the pre-analysis plan of PS 7.3 (which is pre-results and so contains no estimates), this assignment is post-results, so reporting estimates is the whole point. Every number in this exemplar is illustrative — it is the synthetic, planted-truth output of nb8.3’s Maya DGP (the same generator as nb7.5: a planted average treatment effect on the treated of \tau = -1.80 percentage points, recovered in the primary specification as \hat{\beta} = -1.886 pp with a state-clustered standard error of 0.065), not an estimate from real HMDA data. We label it illustrative every time it appears, exactly as a student drafting before their own analysis is final would be required to. The HMDA snapshot is pinned in data-cards/hmda.md; any matched licensed data stays read-only on GMU infrastructure per CONVENTIONS §5. The headline table reproduces nb8.3’s building-up columns verbatim so a student can check their own generated table against it.

The model deliverable: Maya’s introduction and results excerpt

Conditional Examination, Conditional Disparity: How State Fair-Lending Examination Programs Move the Minority–White Mortgage-Denial Gap

Author: Maya · Working draft, introduction and results excerpt · All estimates from the frozen Ch 8.1 specification and the Ch 8.2 robustness battery (here, illustrative synthetic values from nb8.3)

1. Introduction

[HOOK] In 2023, mortgage applicants in majority-minority neighborhoods were denied at nearly twice the rate of applicants in majority-white neighborhoods — a gap that narrows but does not vanish once income and loan size are held fixed. Whether such gaps reflect differential treatment by lenders, and whether supervisory policy can actually move them, is at once a live question for fair-lending regulators and an unresolved empirical one, because the raw gap confounds how applicants are treated with who applies.

[CONTRIBUTION] This paper provides the first quasi-experimental estimate of how state fair-lending examination programs affect the county-level minority–white mortgage-denial gap, exploiting the staggered timing with which states adopted these programs as a source of plausibly exogenous variation in supervisory intensity. Where a descriptive literature has measured the gap and an audit-study literature has isolated differential treatment in the small, neither has been able to ask whether a policy — supervision at population scale — moves the gap; that is the question this design answers.

[“WE FIND” PREVIEW] We find that adopting an examination program reduces the county-level minority–white denial gap by approximately 1.9 percentage points — about one-fifth of the pre-adoption gap of roughly nine points — with the effect emerging within two years of adoption and stabilizing thereafter. The estimate is robust to using only never- and not-yet-treated states as controls (the Callaway–Sant’Anna comparison that avoids the forbidden-comparison bias of staggered two-way fixed effects), to alternative clustering, and to a placebo test that randomly reassigns adoption years; the pre-treatment event-study leads are flat and statistically indistinguishable from zero, consistent with the parallel-trends assumption on which our interpretation rests. We read the estimate as a credible effect of the programs under that assumption, not as proof that examinations eliminate discrimination — the gap shrinks by a fifth, it does not close.

[POSITIONING BRIDGE] Our work sits at the intersection of two literatures that have not met: a descriptive HMDA literature that measures the denial gap precisely but cannot separate differential treatment from differential applicant composition, and an audit-study and lending-discrimination literature — including Sun & Gao (2019) on the treatment of same-sex borrowers — that isolates differential treatment but cannot speak to the population-scale effect of supervisory policy.

[ROADMAP] Section 2 positions our contribution in these literatures; Section 3 describes the HMDA sample and the construction of the county-year denial gap; Section 4 presents the staggered difference-in-differences design and states our identifying assumption; Section 5 reports the main results; Section 6 presents robustness checks organized around the threats to identification; Section 7 concludes.

2. Related literature (positioning excerpt)

Two strands of prior work frame our question, and the gap we fill is the empty space between them. One strand documents the disparity. Using the public HMDA Loan/Application Register, a large descriptive literature has established that minority applicants face higher denial rates than otherwise-similar non-minority applicants, and that the gap shrinks but persists after conditioning on observable risk (Bartlett, Morse, Stanton & Wallace, 2022; Bhutta, Hizmo & Ringo, forthcoming). This strand establishes that a conditional gap exists at scale; what it cannot do is separate differential treatment from differential applicant composition, because HMDA omits the credit score lenders legitimately price. A second strand isolates treatment. Audit and correspondence studies, and quasi-experimental analyses of specific lending margins — Sun & Gao (2019), who find that same-sex co-borrowers were treated differently than comparable opposite-sex applicants — credibly identify differential treatment by holding applicant characteristics fixed by design. This strand establishes that lenders treat similar applicants differently; what it cannot do is speak to the population-scale effect of policy, because an audit measures the behavior of the lenders studied, not the response of an entire market to a supervisory regime. We sit at the intersection these two strands leave empty: population-scale HMDA data and a policy shock — the staggered adoption of state examination programs — that lets us identify the effect of supervisory intensity on the gap itself. We build directly on the conditional-gap measurement of the first strand and the treatment-isolation logic of the second; our contribution is to bring a credible research design to a question both strands raise but neither can answer.

5. Results

Table 1 reports our main estimate. Column (4) is the pre-registered primary specification — the Callaway–Sant’Anna overall average treatment effect on the treated, against never- and not-yet-treated controls, with county and year fixed effects and standard errors clustered by state. Columns (1)–(3) build up to it from a raw difference in means, so a reader can see what each layer of the design buys.

Table 1. Effect of state fair-lending examination programs on the county-year minority–white mortgage-denial gap.

(1) (2) (3) (4)

OLS, raw + Year FE + County & Year FE Primary (CS ATT)

Examination program (post × adopter) −1.775*** −2.093*** −1.758*** −1.886*

(0.240) (0.313) (0.145) (0.065)

County applicant-composition controls No No Yes Yes

County fixed effects No No Yes Yes

Year fixed effects No Yes Yes Yes

Clean (never-/not-yet-treated) controls only No No No Yes

Observations (county-years) 2,400 2,400 2,400 2,400

Within-R^2 0.061 0.118 0.642 —

Notes. The dependent variable is the county-year minority–white mortgage-denial gap (minority denial rate minus white denial rate), in percentage points, constructed from the HMDA Loan/Application Register (snapshot pinned in data-cards/hmda.md). The unit of observation is a county-year; the sample is 2,400 county-years across 30 states over the adoption window. The reported coefficient is the effect of a state’s fair-lending examination program being active (columns 1–3, a post × adopter indicator estimated by OLS; column 4, the Callaway & Sant’Anna (2021) overall ATT aggregated from group-time effects against never- and not-yet-treated comparison states). Standard errors clustered by state (30 clusters) in parentheses. Column-4 within-R^2 is not defined for the group-time estimator and is reported as “—”. Stars: *** p<0.01, ** p<0.05, * p<0.10. All values are illustrative synthetic output from nb8.3 (planted ATT \tau = -1.80 pp), not estimates from production HMDA data.

Reading column (4): adopting a fair-lending examination program is associated with a decline in the county-year denial gap of 1.89 percentage points (clustered SE 0.065, t \approx 29 in the synthetic illustration; in real data we anticipate a far larger SE and a t nearer 2.5, as the Ch 8.2 clustering table shows). The sign is negative — the programs shrink the gap, the direction fair-lending supervision is meant to push. The magnitude matters in human terms, not merely statistically: against a pre-adoption gap of roughly nine percentage points, a 1.9-point reduction is about a fifth of the disparity, large enough that a regulator weighing whether to fund examinations would care, yet far from closing the gap. The building-up columns tell the design’s story: the raw OLS gap-shift in column (1) survives the addition of year fixed effects (2) and county fixed effects plus applicant-composition controls (3), and the move to the clean-control group-time estimator in (4) — which discards the forbidden already-treated comparisons that bias staggered two-way fixed effects (Ch 4.2) — leaves the point estimate essentially unchanged at −1.9 points. That stability across the columns is itself reassuring: the effect is not an artifact of the pooling that the naive estimator would have done.

We interpret this as a credible causal effect of the examination programs under the parallel-trends assumption, not as an unconditional fact about discrimination. The event-study profile (Figure 1, omitted here) supports the assumption on its testable margin: the pre-treatment leads are flat and statistically indistinguishable from zero, the effect appears at adoption, and it stabilizes within two years. A flat pre-trend cannot confirm the post-period counterfactual — it can only fail to refute it (Ch 4.1) — so we report the estimate as the program’s effect if adopting and never-adopting states’ gaps would have moved in parallel absent the programs, and we defend that “if” in Section 6. Secondary results — heterogeneity by applicant subgroup and by income band — are reported in Table 2 and discussed below; they enrich the picture but are not the confirmatory claim, and we flag them as exploratory throughout.

— End of Maya’s introduction and results excerpt.

	(1)	(2)	(3)	(4)
	OLS, raw	+ Year FE	+ County & Year FE	Primary (CS ATT)
Examination program (post × adopter)	−1.775***	−2.093***	−1.758***	−1.886*
	(0.240)	(0.313)	(0.145)	(0.065)

County applicant-composition controls	No	No	Yes	Yes
County fixed effects	No	No	Yes	Yes
Year fixed effects	No	Yes	Yes	Yes
Clean (never-/not-yet-treated) controls only	No	No	No	Yes
Observations (county-years)	2,400	2,400	2,400	2,400
Within-R^2	0.061	0.118	0.642	—

Instructor grading notes (keyed to the writing rubric)

The draft is graded on two cross-cutting principles, both from Ch 8.3: front-load every verdict (contribution leads the intro, table leads the results, topic sentence leads each paragraph) and match every verb to the weakest assumption (§7’s causal-language discipline). Below, the points per component, what the A-grade exemplar does, and the common failure modes that cost points.

Component 1 — The one-sentence contribution (15 pts). A-grade markers: the contribution sentence states what is now known (“the first quasi-experimental estimate of how examination programs affect the gap”), not what was done (“we run a DiD”); it names its job explicitly — the “first to credibly estimate” job — and the very next sentence shows the literature supports that claim (neither prior strand could ask the policy question), pre-empting the ten-second “but three papers did this” kill; the verb “exploiting plausibly exogenous variation” / “credibly estimate” is calibrated to a DiD whose parallel-trends assumption is untestable beyond the pre-period, never “we prove discrimination.” Deduct: a contribution sentence that describes the method instead of the finding (−4); claiming the “first” job with a literature review that exposes rather than supports it (−4) — the fastest route to a referee’s contempt; a verb the design has not earned, e.g. “we show that examinations cause a decline” for a DiD (−3, the §7 violation that recurs in every component). Common failure: the sentence is really two sentences, or it needs the rest of the introduction to be intelligible — the §3 stress test (hand it to a classmate cold) is the cheap detector, and an A-grade submission reports having run it.

Component 2 — The four-move introduction (35 pts; hook 8 + preview 8 + positioning 6 + roadmap 5 + verb audit 8). This is the largest weight and the heart of the assignment. A-grade markers: the hook leads with a fact and a tension (the 2x denial-rate gap, the regulatory stakes), not “the literature has long studied”; the “we find” preview gives the number, the human-unit magnitude (“1.9 pp, about a fifth of the pre-period gap”), the timing, the key robustness fact, AND names the assumption it rests on — and then explicitly bounds the claim (“the gap shrinks by a fifth, it does not close”), which is the calibration §7 wants; the positioning bridge constructs the gap by contrast in one or two sentences rather than listing; the roadmap is short and functional. The verb audit (8 pts) is where the A/B line is sharpest: the exemplar’s preview says “reduces … consistent with the parallel-trends assumption on which our interpretation rests,” and the results echo “credible causal effect under the parallel-trends assumption” — the verb is conditioned every time it could drift. Deduct: hook that opens with a citation or “in today’s mortgage market” (−4, CONVENTIONS §1 and §2’s hook rule); a preview that hides the number (“we present evidence on the question” — the spoiling-the-ending error §2 explicitly forbids, −5); magnitude given as a bare coefficient with no human unit (−3); drift caught nowhere — the preview hedges but a later sentence says “the program causes” (−4); over-hedging into mush (“may possibly tentatively suggest under certain conditions,” −3) — calibration cuts both ways, a clean DiD with flat pre-trends has earned a confident assumption-conditioned claim. Common failure: students treat the verb audit as a formality and do not actually report the verbs they changed; full marks require the before/after of at least one verb.

Component 3 — The positioning literature review (15 pts; group-and-contrast 9 + load-bearing 3 + tone 3). A-grade markers: the section is built as two named strands, each characterized by what it established and what it could not (“documents the gap but cannot separate treatment from composition”; “isolates treatment but cannot speak to policy at scale”), so the gap is constructed out of the literature, not asserted; Sun & Gao (2019) is placed inside the treatment-isolation strand, load-bearing (it marks the edge of the hole, not decoration); the tone is generous and precise (“we build directly on … our contribution is to bring a credible design to a question both strands raise”), never “prior work was wrong.” Deduct: the annotated bibliography — “Smith finds A. Jones finds B. We contribute.” (−6, the §4 named failure); a citation that could be deleted without moving the gap (−3, padding); dismissiveness toward prior work (−3); a fabricated or unverifiable citation not tagged [CHECK] (−3 and a flag, CONVENTIONS §6 — a hallucinated reference is the one error a referee never forgives). Common failure: students summarize each paper (“a book report”) instead of giving its coordinate on the map; the fix is one sentence per paper, with the contrast doing the work.

Component 4 — The headline-first results section (25 pts; table 12 + walk-through 9 + causal language 4). A-grade markers: the headline table is the first object in the section and stands alone — a reader seeing only Table 1 can recover the dependent variable, units (percentage points), sample (2,400 county-years, 30 states), estimator (OLS in 1–3, Callaway–Sant’Anna in 4), the meaning of the stars (defined in the notes), and the FE/clustering (disclosed in dedicated rows and restated in the notes, “clustered by state, 30 clusters”); the SEs are in parentheses beneath the coefficients with the flavor named and the cluster level stated; significant digits are sensible and consistent (coefficients to 3 decimals, not 6; the gap reported as “1.89 pp” in prose, “about a fifth” in interpretation); the within-R^2 row honestly reports “—” for the group-time estimator rather than inventing one; the illustrative-numbers caveat is in the note. The walk-through leads with the headline, gives sign + human-unit magnitude + precision, then interprets economically (“about a fifth of the disparity … large enough that a regulator would care, yet far from closing the gap” — importance, not just significance) and subordinates the secondary results explicitly. The causal language is conditioned (“credible causal effect under the parallel-trends assumption”; “a flat pre-trend cannot confirm the counterfactual”). Deduct: a hand-formatted table rather than one generated by nb8.3 (−3 and a process flag — hand-typing is how tables silently drift from the analysis); a bare “(0.065)” with no SE flavor named (−3, Appendix D.2); stars used but not defined in the notes (−2); a table that needs the prose to be intelligible (−4, the §8 standalone failure); a data dump — several tables of equal weight with no headline led (−4, the §5 cardinal sin); magnitude reported only as “significant at the 1% level” with no economic interpretation (−3, significance-is-not-importance); the verb drifts to an unconditional “the program causes” in the results (−3, the §7 spot where drift bites hardest). Common failure: students report the t-statistic and stars and stop, never telling the reader whether 1.9 points is a big effect — the prose must carry the economics the stars cannot.

Cross-cutting (folded into the above, not separately scored). Front-loading: an A-grade draft passes the “first sentence of every unit” test — a reader who quits after the first sentence of the introduction, the results section, or any paragraph has still learned that unit’s most important thing. Real vs. illustrative numbers: the only legitimate numbers are the frozen Ch 8.1/8.2 estimates or clearly-labeled illustrative nb8.3 values; numbers tuned after seeing the table, or a table retyped rather than generated, are capped the way a drifted manuscript would be — and the standing-rule caveat must appear. Appendix D is the binding spec: this PS dictates the moves; D dictates the table craft and prose style (D.1 layout/notes, D.2 disclosure lines, D.5 causal language). A table that violates D loses points on Component 4a no matter how good the surrounding prose.

End of model deliverable and grading notes for PS 8.3. This exemplar is consistent with Maya’s introduction skeleton in Ch 8.3 §9, her identification memo in Ch 7.5 (the parallel-trends contract every verb here is conditioned on), her robustness battery in Ch 8.2 (the clustering table that explains why the real-data t is nearer 2.5 than the synthetic 29), and the publication-quality table nb8.3 generates from the frozen synthetic results. The introduction is the promise the whole paper defends; the results section, led by the headline table, is where Maya begins to redeem it. Both live or die on the two disciplines this week teaches: say the important thing first, at every scale, and claim exactly as much as your design supports — no more, and no less.

# Model Deliverable — PS 8.3 (An A-Grade Introduction + Headline-First Results Excerpt) **Problem set:** `book/weeks/week-08/ps8.3.md` (PS 8.3, Week 8). **Chapter:** Ch 8.3 — Writing the Empirical Paper, held to the binding table-and-prose standard of **Appendix D** (`book/appendices/D-style-guide/`; D.1 table layout/notes, D.2 coefficient/FE/cluster/sample disclosure, D.5 prose-style and causal-language rules). **Tool:** `nb8.3` (`notebooks/week-08/nb8.3-publication-tables-figures.ipynb`), which generates the headline table and event-study figure below to the Appendix D standard. PS 8.3 has no single right answer — every camper's introduction and results section is different because every camper's project is different. What this manual provides instead is a **model deliverable**: one A-grade introduction and one headline-first results excerpt, written for **Maya's** HMDA fair-lending project — the staggered difference-in-differences asking whether state fair-lending examination programs reduced the county-level minority–white mortgage-denial gap, the project carried since Week 1, whose identification memo students read in Ch 7.5 and whose robustness battery they ran in Ch 8.2. It shows the standard the writing must reach — *front-load every verdict, match every verb to the weakest assumption, and build a headline table that stands alone* — without dictating any camper's question. Below the draft itself are **instructor grading notes keyed to the writing rubric**, component by component, with the common failure modes flagged. **A standing rule on numbers.** Unlike the pre-analysis plan of PS 7.3 (which is *pre-results* and so contains no estimates), this assignment is *post-results*, so reporting estimates is the whole point. **Every number in this exemplar is illustrative** — it is the synthetic, planted-truth output of `nb8.3`'s Maya DGP (the same generator as nb7.5: a planted average treatment effect on the treated of $\tau = -1.80$ percentage points, recovered in the primary specification as $\hat{\beta} = -1.886$ pp with a state-clustered standard error of $0.065$), not an estimate from real HMDA data. We label it illustrative every time it appears, exactly as a student drafting before their own analysis is final would be required to. The HMDA snapshot is pinned in `data-cards/hmda.md`; any matched licensed data stays read-only on GMU infrastructure per CONVENTIONS §5. The headline table reproduces `nb8.3`'s building-up columns verbatim so a student can check their own generated table against it. --- ## The model deliverable: Maya's introduction and results excerpt > **Conditional Examination, Conditional Disparity: How State Fair-Lending Examination Programs Move the Minority–White Mortgage-Denial Gap** > > *Author: Maya · Working draft, introduction and results excerpt · All estimates from the frozen Ch 8.1 specification and the Ch 8.2 robustness battery (here, illustrative synthetic values from `nb8.3`)* > > --- > > ### 1. Introduction > > **[HOOK]** In 2023, mortgage applicants in majority-minority neighborhoods were denied at nearly twice the rate of applicants in majority-white neighborhoods — a gap that narrows but does not vanish once income and loan size are held fixed. Whether such gaps reflect differential *treatment* by lenders, and whether supervisory policy can actually move them, is at once a live question for fair-lending regulators and an unresolved empirical one, because the raw gap confounds how applicants are *treated* with who *applies*. > > **[CONTRIBUTION]** This paper provides the first quasi-experimental estimate of how state fair-lending examination programs affect the county-level minority–white mortgage-denial gap, exploiting the staggered timing with which states adopted these programs as a source of plausibly exogenous variation in supervisory intensity. Where a descriptive literature has measured the gap and an audit-study literature has isolated differential treatment in the small, neither has been able to ask whether a *policy* — supervision at population scale — moves the gap; that is the question this design answers. > > **["WE FIND" PREVIEW]** We find that adopting an examination program reduces the county-level minority–white denial gap by approximately **1.9 percentage points** — about one-fifth of the pre-adoption gap of roughly nine points — with the effect emerging within two years of adoption and stabilizing thereafter. The estimate is robust to using only never- and not-yet-treated states as controls (the Callaway–Sant'Anna comparison that avoids the forbidden-comparison bias of staggered two-way fixed effects), to alternative clustering, and to a placebo test that randomly reassigns adoption years; the pre-treatment event-study leads are flat and statistically indistinguishable from zero, consistent with the parallel-trends assumption on which our interpretation rests. We read the estimate as a credible effect of the programs *under that assumption*, not as proof that examinations eliminate discrimination — the gap shrinks by a fifth, it does not close. > > **[POSITIONING BRIDGE]** Our work sits at the intersection of two literatures that have not met: a descriptive HMDA literature that measures the denial gap precisely but cannot separate differential treatment from differential applicant composition, and an audit-study and lending-discrimination literature — including Sun & Gao (2019) on the treatment of same-sex borrowers — that isolates differential treatment but cannot speak to the population-scale effect of supervisory *policy*. > > **[ROADMAP]** Section 2 positions our contribution in these literatures; Section 3 describes the HMDA sample and the construction of the county-year denial gap; Section 4 presents the staggered difference-in-differences design and states our identifying assumption; Section 5 reports the main results; Section 6 presents robustness checks organized around the threats to identification; Section 7 concludes. > > --- > > ### 2. Related literature *(positioning excerpt)* > > Two strands of prior work frame our question, and the gap we fill is the empty space between them. **One strand documents the disparity.** Using the public HMDA Loan/Application Register, a large descriptive literature has established that minority applicants face higher denial rates than otherwise-similar non-minority applicants, and that the gap shrinks but persists after conditioning on observable risk (Bartlett, Morse, Stanton & Wallace, 2022; Bhutta, Hizmo & Ringo, forthcoming). This strand establishes *that* a conditional gap exists at scale; what it cannot do is separate differential *treatment* from differential applicant *composition*, because HMDA omits the credit score lenders legitimately price. **A second strand isolates treatment.** Audit and correspondence studies, and quasi-experimental analyses of specific lending margins — Sun & Gao (2019), who find that same-sex co-borrowers were treated differently than comparable opposite-sex applicants — credibly identify differential treatment by holding applicant characteristics fixed by design. This strand establishes *that lenders treat similar applicants differently*; what it cannot do is speak to the population-scale effect of *policy*, because an audit measures the behavior of the lenders studied, not the response of an entire market to a supervisory regime. We sit at the intersection these two strands leave empty: population-scale HMDA data *and* a policy shock — the staggered adoption of state examination programs — that lets us identify the effect of supervisory intensity on the gap itself. We build directly on the conditional-gap measurement of the first strand and the treatment-isolation logic of the second; our contribution is to bring a credible research design to a question both strands raise but neither can answer. > > --- > > ### 5. Results > > **Table 1 reports our main estimate.** Column (4) is the pre-registered primary specification — the Callaway–Sant'Anna overall average treatment effect on the treated, against never- and not-yet-treated controls, with county and year fixed effects and standard errors clustered by state. Columns (1)–(3) build up to it from a raw difference in means, so a reader can see what each layer of the design buys. > > *Table 1. Effect of state fair-lending examination programs on the county-year minority–white mortgage-denial gap.* > > | | (1) | (2) | (3) | (4) | > |---|:---:|:---:|:---:|:---:| > | | OLS, raw | + Year FE | + County & Year FE | **Primary (CS ATT)** | > | Examination program (post × adopter) | −1.775*** | −2.093*** | −1.758*** | **−1.886*** | > | | (0.240) | (0.313) | (0.145) | **(0.065)** | > | | | | | | > | County applicant-composition controls | No | No | Yes | Yes | > | County fixed effects | No | No | Yes | Yes | > | Year fixed effects | No | Yes | Yes | Yes | > | Clean (never-/not-yet-treated) controls only | No | No | No | Yes | > | Observations (county-years) | 2,400 | 2,400 | 2,400 | 2,400 | > | Within-$R^2$ | 0.061 | 0.118 | 0.642 | — | > > *Notes.* The dependent variable is the county-year minority–white mortgage-denial gap (minority denial rate minus white denial rate), in percentage points, constructed from the HMDA Loan/Application Register (snapshot pinned in `data-cards/hmda.md`). The unit of observation is a county-year; the sample is 2,400 county-years across 30 states over the adoption window. The reported coefficient is the effect of a state's fair-lending examination program being active (columns 1–3, a post × adopter indicator estimated by OLS; column 4, the Callaway & Sant'Anna (2021) overall ATT aggregated from group-time effects against never- and not-yet-treated comparison states). **Standard errors clustered by state (30 clusters) in parentheses.** Column-4 within-$R^2$ is not defined for the group-time estimator and is reported as "—". Stars: \*\*\* $p<0.01$, \*\* $p<0.05$, \* $p<0.10$. *All values are illustrative synthetic output from `nb8.3` (planted ATT $\tau = -1.80$ pp), not estimates from production HMDA data.* > > Reading column (4): adopting a fair-lending examination program is associated with a decline in the county-year denial gap of **1.89 percentage points** (clustered SE 0.065, $t \approx 29$ in the synthetic illustration; in real data we anticipate a far larger SE and a $t$ nearer 2.5, as the Ch 8.2 clustering table shows). The sign is negative — the programs *shrink* the gap, the direction fair-lending supervision is meant to push. The magnitude matters in human terms, not merely statistically: against a pre-adoption gap of roughly nine percentage points, a 1.9-point reduction is **about a fifth of the disparity**, large enough that a regulator weighing whether to fund examinations would care, yet far from closing the gap. The building-up columns tell the design's story: the raw OLS gap-shift in column (1) survives the addition of year fixed effects (2) and county fixed effects plus applicant-composition controls (3), and the move to the clean-control group-time estimator in (4) — which discards the forbidden already-treated comparisons that bias staggered two-way fixed effects (Ch 4.2) — leaves the point estimate essentially unchanged at −1.9 points. That stability across the columns is itself reassuring: the effect is not an artifact of the pooling that the naive estimator would have done. > > We interpret this as a **credible causal effect of the examination programs under the parallel-trends assumption**, not as an unconditional fact about discrimination. The event-study profile (Figure 1, omitted here) supports the assumption on its testable margin: the pre-treatment leads are flat and statistically indistinguishable from zero, the effect appears at adoption, and it stabilizes within two years. A flat pre-trend cannot *confirm* the post-period counterfactual — it can only fail to refute it (Ch 4.1) — so we report the estimate as the program's effect *if* adopting and never-adopting states' gaps would have moved in parallel absent the programs, and we defend that "if" in Section 6. Secondary results — heterogeneity by applicant subgroup and by income band — are reported in Table 2 and discussed below; they enrich the picture but are not the confirmatory claim, and we flag them as exploratory throughout. > > *— End of Maya's introduction and results excerpt.* --- ## Instructor grading notes (keyed to the writing rubric) The draft is graded on two cross-cutting principles, both from Ch 8.3: **front-load every verdict** (contribution leads the intro, table leads the results, topic sentence leads each paragraph) and **match every verb to the weakest assumption** (§7's causal-language discipline). Below, the points per component, what the A-grade exemplar does, and the common failure modes that cost points. **Component 1 — The one-sentence contribution (15 pts).** *A-grade markers:* the contribution sentence states *what is now known* ("the first quasi-experimental estimate of how examination programs affect the gap"), not *what was done* ("we run a DiD"); it names its **job** explicitly — the "first to credibly estimate" job — and the very next sentence shows the literature *supports* that claim (neither prior strand could ask the policy question), pre-empting the ten-second "but three papers did this" kill; the verb "exploiting plausibly exogenous variation" / "credibly estimate" is **calibrated to a DiD whose parallel-trends assumption is untestable beyond the pre-period**, never "we prove discrimination." *Deduct:* a contribution sentence that describes the method instead of the finding (−4); claiming the "first" job with a literature review that exposes rather than supports it (−4) — the fastest route to a referee's contempt; a verb the design has not earned, e.g. "we show that examinations cause a decline" for a DiD (−3, the §7 violation that recurs in every component). *Common failure:* the sentence is really two sentences, or it needs the rest of the introduction to be intelligible — the §3 stress test (hand it to a classmate cold) is the cheap detector, and an A-grade submission reports having run it. **Component 2 — The four-move introduction (35 pts; hook 8 + preview 8 + positioning 6 + roadmap 5 + verb audit 8).** This is the largest weight and the heart of the assignment. *A-grade markers:* the **hook leads with a fact and a tension** (the 2x denial-rate gap, the regulatory stakes), not "the literature has long studied"; the **"we find" preview gives the number, the human-unit magnitude ("1.9 pp, about a fifth of the pre-period gap"), the timing, the key robustness fact, AND names the assumption it rests on** — and then explicitly *bounds the claim* ("the gap shrinks by a fifth, it does not close"), which is the calibration §7 wants; the positioning bridge **constructs the gap by contrast** in one or two sentences rather than listing; the roadmap is short and functional. The **verb audit (8 pts)** is where the A/B line is sharpest: the exemplar's preview says "reduces ... consistent with the parallel-trends assumption on which our interpretation rests," and the results echo "credible causal effect *under the parallel-trends assumption*" — the verb is conditioned every time it could drift. *Deduct:* hook that opens with a citation or "in today's mortgage market" (−4, CONVENTIONS §1 and §2's hook rule); a preview that hides the number ("we present evidence on the question" — the spoiling-the-ending error §2 explicitly forbids, −5); magnitude given as a bare coefficient with no human unit (−3); **drift** caught nowhere — the preview hedges but a later sentence says "the program causes" (−4); **over-hedging into mush** ("may possibly tentatively suggest under certain conditions," −3) — calibration cuts both ways, a clean DiD with flat pre-trends has *earned* a confident assumption-conditioned claim. *Common failure:* students treat the verb audit as a formality and do not actually report the verbs they changed; full marks require the *before/after* of at least one verb. **Component 3 — The positioning literature review (15 pts; group-and-contrast 9 + load-bearing 3 + tone 3).** *A-grade markers:* the section is built as **two named strands**, each characterized by *what it established and what it could not* ("documents the gap but cannot separate treatment from composition"; "isolates treatment but cannot speak to policy at scale"), so the gap is *constructed out of the literature*, not asserted; **Sun & Gao (2019) is placed inside the treatment-isolation strand**, load-bearing (it marks the edge of the hole, not decoration); the tone is **generous and precise** ("we build directly on ... our contribution is to bring a credible design to a question both strands raise"), never "prior work was wrong." *Deduct:* the **annotated bibliography** — "Smith finds A. Jones finds B. We contribute." (−6, the §4 named failure); a citation that could be deleted without moving the gap (−3, padding); dismissiveness toward prior work (−3); a fabricated or unverifiable citation not tagged `[CHECK]` (−3 and a flag, CONVENTIONS §6 — a hallucinated reference is the one error a referee never forgives). *Common failure:* students summarize each paper ("a book report") instead of giving its coordinate on the map; the fix is one sentence per paper, with the *contrast* doing the work. **Component 4 — The headline-first results section (25 pts; table 12 + walk-through 9 + causal language 4).** *A-grade markers:* the **headline table is the first object** in the section and **stands alone** — a reader seeing only Table 1 can recover the dependent variable, units (percentage points), sample (2,400 county-years, 30 states), estimator (OLS in 1–3, Callaway–Sant'Anna in 4), the meaning of the stars (defined in the notes), and the FE/clustering (disclosed in dedicated rows and restated in the notes, "clustered by state, 30 clusters"); the SEs are in parentheses beneath the coefficients with the **flavor named and the cluster level stated**; significant digits are **sensible and consistent** (coefficients to 3 decimals, not 6; the gap reported as "1.89 pp" in prose, "about a fifth" in interpretation); the within-$R^2$ row honestly reports "—" for the group-time estimator rather than inventing one; the **illustrative-numbers caveat is in the note**. The walk-through **leads with the headline, gives sign + human-unit magnitude + precision, then interprets economically** ("about a fifth of the disparity ... large enough that a regulator would care, yet far from closing the gap" — importance, not just significance) and **subordinates the secondary results explicitly**. The causal language is conditioned ("credible causal effect *under the parallel-trends assumption*"; "a flat pre-trend cannot confirm the counterfactual"). *Deduct:* a **hand-formatted table** rather than one generated by `nb8.3` (−3 and a process flag — hand-typing is how tables silently drift from the analysis); a bare "(0.065)" with no SE flavor named (−3, Appendix D.2); stars used but **not defined in the notes** (−2); a table that **needs the prose to be intelligible** (−4, the §8 standalone failure); a **data dump** — several tables of equal weight with no headline led (−4, the §5 cardinal sin); magnitude reported only as "significant at the 1% level" with no economic interpretation (−3, significance-is-not-importance); the verb **drifts to an unconditional "the program causes"** in the results (−3, the §7 spot where drift bites hardest). *Common failure:* students report the $t$-statistic and stars and stop, never telling the reader whether 1.9 points is a big effect — the prose must carry the economics the stars cannot. **Cross-cutting (folded into the above, not separately scored).** *Front-loading:* an A-grade draft passes the "first sentence of every unit" test — a reader who quits after the first sentence of the introduction, the results section, or any paragraph has still learned that unit's most important thing. *Real vs. illustrative numbers:* the only legitimate numbers are the frozen Ch 8.1/8.2 estimates or clearly-labeled illustrative `nb8.3` values; numbers tuned after seeing the table, or a table retyped rather than generated, are capped the way a drifted manuscript would be — and the standing-rule caveat must appear. *Appendix D is the binding spec:* this PS dictates the *moves*; D dictates the *table craft and prose style* (D.1 layout/notes, D.2 disclosure lines, D.5 causal language). A table that violates D loses points on Component 4a no matter how good the surrounding prose. --- *End of model deliverable and grading notes for PS 8.3. This exemplar is consistent with Maya's introduction skeleton in Ch 8.3 §9, her identification memo in Ch 7.5 (the parallel-trends contract every verb here is conditioned on), her robustness battery in Ch 8.2 (the clustering table that explains why the real-data $t$ is nearer 2.5 than the synthetic 29), and the publication-quality table `nb8.3` generates from the frozen synthetic results. The introduction is the promise the whole paper defends; the results section, led by the headline table, is where Maya begins to redeem it. Both live or die on the two disciplines this week teaches: say the important thing first, at every scale, and claim exactly as much as your design supports — no more, and no less.*

The model deliverable: Maya’s introduction and results excerpt

1. Introduction

2. Related literature (positioning excerpt)

5. Results

Instructor grading notes (keyed to the writing rubric)