Statistical Explainer: `home_court_analysis.py`

Author

Justin Pietsch

Published

July 4, 2026

Draft

A guide to every analysis that produces output in home_court_results.md: the data it uses, the statistical approach, why that approach was chosen, what the results mean, and, where a section has one, why its figure takes the form it does (a Why this chart note). Sections appear in the same order as home_court_results.md. The figures themselves are displayed and captioned in home_court_findings.md; here I only explain the reasoning behind each chart choice. Unlike home_court_findings.md, this document uses statistical terminology freely. It is the methods companion, not the narrative report.

0. The Game-Level Dataset (`build_game_dataset`)

The data. Every analysis (except shot zones, franchise HCA, referees, and parity, which use their own season-level inputs) runs on a single DataFrame with one row per game: 52,399 games from 1983–84 through 2025–26, regular season and playoffs, assembled from the cached game logs. Each row carries:

home_win (1/0), the outcome for all the logistic regressions
year, is_playoff, era (rule-change era), format_period (playoff scheduling era), covid flag
rest_diff, home team days of rest minus away team days of rest (NaN for each team’s first game of a season)
altitude_home, 1 if the home team is Denver or Utah
tz_diff, absolute time-zone difference between the two franchises
box-score differentials (home minus away): fouls, FG%, eFG%, 3PA rate, 3P%, FT%
tov_diff, reb_diff, home-minus-away turnovers and total rebounds (the extra channels used by the mediation decomposition)
oreb_diff, dreb_diff, reb_share_edge, league_oreb_rate, offensive/defensive rebound splits, the pace-free rebound-share advantage, and the league offensive-rebound rate (the rebounding decomposition, Section 12)
margin, home point differential
game_in_series, for playoff games, the game number (parsed from the game ID)
distance_miles, haversine distance from the away team’s home arena to the game arena
tpa_rate_avg, both teams’ combined 3PA as a share of combined FGA
pace_avg, estimated possessions per game (FGA − OREB + TOV + 0.44·FTA, averaged across both teams)
expected_pace, leave-one-out pace: each team’s average pace across all its other games that season, averaged for the two teams in this game. This matters for the pace analysis (Section 20): realized pace in a game is partly caused by the outcome (blowouts produce garbage-time possessions), so using each team’s typical pace from other games removes that endogeneity.

For playoff rest and seeding analyses, quality_diff is added: home team regular-season win% minus away team regular-season win% in the same season. Playoff rest is earned by winning series quickly, so rest and team strength are confounded; this column is the control.

1. The Overall Decline (`run_decline_trend`)

The data. Games aggregated to one row per season: wins, games, home win %. 43 regular seasons and 42 playoff seasons (lockout/COVID playoff gaps skipped).

The approach. Two regressions of home win rate on year, run separately for regular season and playoffs, plus the same pair re-run within each rule-change era:

Primary: a binomial GLM with (wins, losses) per season as the outcome. This models the win count directly, so seasons with more games automatically get more weight and the variance is correct for proportion data. The slope comes out in log-odds per year (log-odds is ln(p / (1 − p)), where 0 is a coin flip and positive values favor the home team) and is converted to percentage points at the mean win rate for readability.
Cross-check: OLS of the season percentage on year with Newey–West HAC (heteroskedasticity- and autocorrelation-consistent) standard errors (one lag). Season win rates are autocorrelated (a high-HCA season tends to follow a high-HCA season), which makes naive OLS standard errors too small. HAC standard errors stay honest about that.

Why two methods. The GLM is the statistically right model for binomial data; the OLS/HAC line is the familiar “fit a line through the points” everyone can picture, with autocorrelation-robust inference. When both agree, the finding doesn’t depend on modeling choices.

What the results mean. They agree almost exactly: the regular season declines about −0.25 pp/year (≈ −10 pp over 43 seasons, p < 0.001 in both, OLS R² = 0.74: year alone explains nearly three-quarters of season-to-season variation in HCA). The playoffs decline at a similar rate (−0.22 pp/yr, total ≈ −9.5 pp) but with much wider confidence intervals and a far lower R² (0.19), because each playoff season is only ~80 games of data. The per-era table shows the decline was not uniform: in the regular season the steepest significant declines were in 1984–94 (−0.52 pp/yr) and 2018–22 (−1.18 pp/yr); the 2023–26 slope (−0.77 pp/yr) is gentler and rests on only 4 seasons and isn’t significant (p = 0.223), with a flat-to-positive plateau between 1995 and 2004. No individual playoff era reaches significance: single playoff eras are just 3–13 small seasons, so the playoff conclusion rests on the full 42-season trend.

Why this chart. The decline is a four-decade drift, so the headline figure is the simplest thing that can carry it: one dot per season for the home win rate, regular season and playoffs on the same axes, each with a fitted line. A line lets a reader eyeball the slope and the scatter at once: the tight regular-season cloud (R² = 0.74) against the noisy playoff one (R² = 0.19). The era shading and the companion era-bar panel do what a single line can’t: they expose that the drift isn’t perfectly smooth, which sets up the discrete-drop question Section 14 tests.

A note on the per-era sub-regressions. Two eras have only 3–4 seasons (2002–04 has N=3 regular-season seasons; the 2002–04 and 2023–26 playoff groups have N=3 and N=4 respectively). With so few data points, the slope estimates are nearly unconstrained: a single unusual season can flip the sign. The output flags these with a warning; treat the flagged slopes as illustrative rather than reliable.

2. Structural Break Test (`run_structural_break_test`)

The question. Section 1 shows the overall 40-year decline and Section 14 tests whether rule-change boundaries produced discrete steps. This section asks a different question: where does the data itself see the strongest break, with no prior assumption about which year matters?

The data. The same season-level home win % series: 43 regular-season seasons and 42 playoff seasons.

The approach. The QLR (Quandt Likelihood-Ratio, or supremum Chow) test, the standard econometric test for an unknown break point. For each candidate year t (the outer 15% trimmed to ensure both sub-samples have at least a handful of seasons), a Chow F-test asks: does fitting two separate regression lines (before t and after t) reduce the residual sum of squares (the total squared distance from the data points to the fitted line) enough to be noteworthy? The F-statistic at each candidate is

F(t) = [(RSS_full − RSS_before(t) − RSS_after(t)) / k] / [(RSS_before(t) + RSS_after(t)) / (n − 2k)]

where k = 2 (intercept + slope). The supremum of F(t) over all candidate years is the QLR test statistic.

Because I take the max over ~33 candidates, the standard F-distribution p-value would overstate significance (I’m doing multiple implicit tests). The correct reference is the asymptotic critical values from Andrews (1993), which account for the maximization: 10% → 7.12, 5% → 8.85, 1% → 12.37 (k=2, outer 15% trimmed). The output also reports the conditional p-value (treating the break year as if it were known in advance) as a lower-bound reference.

Why not just use the rule-change years. Section 14 tests those. This test is the data-driven complement: it finds where the decline most abruptly changed pace, which may or may not align with a rule change. When the two methods converge, confidence increases; when they diverge, there’s something to investigate.

What the results mean. - Regular season: The strongest data-implied break falls at 1999 (supremum Chow F = 10.22), clearing the 5% Andrews threshold. Before 1999, the regular-season HCA was declining steeply (−0.65 pp/yr); after 1999 the decline slowed markedly (−0.25 pp/yr). The top-5 candidates all cluster in 1992–2003, bracketing the anti-hand-checking era (1995–01). The data-implied break is near but not identical to the rule-change boundary: 1999 falls at the end of the aggressive-enforcement window, not its start. - Playoffs: The supremum is only 3.23 (at 2006), well below even the 10% threshold. The playoff decline shows no single data-implied break, consistent with Section 14’s finding that playoff HCA is a smooth drift.

3. CUSUM Test: Parameter Stability (`run_cusum_test`)

Why this section exists. The structural break test (Section 2) finds the single year where the decline most sharply changes pace. This section asks the complementary question: is the trend globally stable, or does it wander outside what one straight line can absorb, anywhere, not just at one break?

The data. The same season-level home win % series, 43 regular-season and 42 playoff seasons.

The approach. The CUSUM test (Brown–Durbin–Evans) accumulates the recursive residuals from the linear year-trend and tracks the running sum against a 5% critical band that widens through the sample. If the cumulative sum exits the band, the parameters are unstable somewhere in that stretch. Where QLR (Section 2) pinpoints one break, CUSUM tests overall stability: agreement raises confidence, disagreement flags something to investigate.

What the results mean. Both contexts stay inside the band. The regular-season CUSUM peaks at 87% of the 5% boundary (|CUSUM| = 14.0 at 2019 vs. a bound of ±16.1), close, but never out; the playoffs are calmer (peak 32% of the boundary). The apparent tension with Section 2, which did find a regular-season break near 1999, is the point: that break is a gradual slope change (−0.65 → −0.25 pp/yr), not a discrete level jump, and CUSUM has low power against slope-only breaks. Read together, the two tests say the decline bent once, gently, in the late 1990s and has otherwise been a stable straight-line drift, with no hidden instability elsewhere.

3a. Bayesian Change-Point Model (`compute_bayesian_changepoint`)

The question. Sections 2 and 3 run two frequentist tests with an apparent tension: the QLR finds a significant slope change near 1999, while CUSUM finds no structural instability. This section reconciles them by asking a broader question: how many slope breaks does the 40-year series actually need, integrating over all possible break locations?

The data. Season-level home win % series, 43 regular-season observations, weighted by games per season. Regular season only; too few playoff seasons to support a k=2 model reliably.

The approach. Four nested piecewise models: k=0 (a single linear trend), k=1 (two segments, one break), k=2 (three segments, two breaks), and k=3 (four segments, three breaks). Each model is estimated by weighted least squares (WLS) with game counts as weights; within each segment the fit is an intercept plus slope. For a given k, break locations are treated as latent: every valid configuration (minimum 3 seasons per segment) is evaluated, and the marginal likelihood is approximated using the BIC (Bayesian Information Criterion, which rewards fit while charging a penalty for each added parameter, so a model with more breaks only wins when the extra fit outweighs the cost):

log Z_k ≈ logsumexp(−BIC(τ)/2 over all configurations τ) − log(n_configurations)

The BIC score per configuration is n·log(weighted RSS/n) + p·log(n), with p = 2(k+1) parameters (intercept + slope per segment). Posterior model probabilities are proportional to exp(log Z_k), normalized across k=0, 1, 2, 3. For k=1, the posterior distribution over individual break years follows directly from the per-year BIC values; the best-fit break year (MAP: maximum a posteriori) is the highest-posterior year and the 95% HPD (highest-probability-density interval) is the narrowest set of years that accumulates 95% of the posterior mass.

Why BIC-based marginal likelihoods. Exact Bayesian computation requires specifying priors on slope and intercept parameters. BIC approximates the marginal likelihood up to a constant that cancels in model-probability ratios (Bayes factors). With N=43, this is an approximation; the results are read as model-selection guidance, not exact posterior probabilities. A uniform prior is placed over k and over valid break locations within each k.

What the results mean. The single linear trend is effectively ruled out: the model strongly favors at least one slope change, with BF(k=1 vs k=0)=14.2 (strong on the Jeffreys scale). Past that, the evidence splits. The posterior allocates 40.5% to k=2 (best-fit breaks: 1992 and 2020), 38.8% to k=3 (best-fit breaks: 1988, 1998, 2020), and 19.3% to k=1 (best-fit break: 1999, 95% HPD 1992–2003). The k=2 and k=3 models are essentially tied: BF(k=3 vs k=2)=1.0, meaning the data offer no reason to prefer three breaks over two. All three multi-break structures place a break in the late 1980s to mid-1990s window, consistent with the hand-checking period. The 2020 break appearing in both k=2 and k=3 likely reflects the COVID disruption and the accelerating modern decline; the underlying slope change began post-2017, but the Bayesian model locates the break closer to 2020 than to 2017. Break years are not precisely datable: the single best-fitting break carries a bootstrap range of roughly a decade. For k=1, the posterior-weighted slopes are −0.577 pp/yr before the break and −0.255 pp/yr after.

This resolves the QLR–CUSUM tension without contradicting either. The QLR asks “if there is exactly one break, where does it best fit?” and answers 1999. The CUSUM asks “does the trend wander outside what a single straight line can absorb?” and says no, because each break is a slope moderation, not a level jump. The Bayesian model asks “how many breaks, integrating over all locations?” and answers “at least one, with the evidence split between two and three, location uncertain.”

Why this chart. Two panels for two purposes. The left panel overlays the k=0 (grey dashed), k=1 best-fit (blue solid), k=2 best-fit (red dash-dot), and k=3 best-fit (green dotted) fitted lines on the season-level time series: putting all four models together makes the structural comparison immediate and shows where each model’s kinks fall. The right panel is a bar chart of the posterior distribution over break year for k=1, with the 95% HPD highlighted: it shows both where the model places the break and how concentrated the posterior is: the dominant mass at 1999 with the HPD spanning 1992–2003 carries more information than a single best-fit year would.

4. Foul & Shooting Differentials by Era (`run_differential_analysis`)

The data. Per-game home-minus-away differentials in seven box-score metrics (personal fouls, free throw attempts, FG%, eFG%, 3PA rate, 3P%, FT%) for all games in both contexts. The home_court_results.md table reports all seven; the six-panel chart uses FTA diff as its first panel rather than foul diff, because free throw attempts are the scoring consequence of foul-calling asymmetry and are more legible to a general audience.

The approach. Era-bucketed means per metric, plus an OLS trend on year per metric with significance stars. Negative foul diff = referees call fewer fouls on the home team; positive FTA diff = home team earned more free throw attempts.

Why. These differentials are the mechanisms of HCA, the measurable things home teams get on the court. The era means show levels; the year trends show which mechanisms are fading, which is the heart of research question 3.

What the results mean. Two mechanisms are clearly fading and one is not:

Foul/FTA bias collapsed: the regular-season home foul advantage went from −1.23 fouls/game (1984–94) to −0.25 (2023–26), trend +0.022/yr, p < 0.001, an ~80% reduction. The chart’s first panel shows the same story via FTA: the home free-throw-attempt advantage fell from +1.97/game (1984–94) to +0.46 (2023–26), trend −0.036/yr, p < 0.001. The playoffs show the same direction for fouls (−1.58 → −0.68, trend +0.020/yr, p < 0.01) and FTA (+2.35 → +1.09, trend −0.021/yr, not significant), retaining about 2.7× the residual foul bias relative to the regular season.
The shooting advantage is shrinking in the regular season: FG% diff trend −0.021 pp/yr and eFG% −0.015 pp/yr (both p < 0.001), from ~+1.6 pp to ~+0.7–1.0 pp. Playoff shooting trends point the same way but aren’t significant: the playoff shooting advantage has held up better.
3PA rate diff trends positive (home teams historically took fewer threes than visitors; that gap is closing), consistent with league-wide shot-selection convergence. 3P% and FT% diffs show no significant trend: those were never large or changing.

Section 7 takes these differentials and quantifies how much of the HCA level and its decline each one accounts for.

Why this chart. Six small-multiple panels, one per box-score metric, each a home-minus-away line over time with a fitted trend and a zero reference line. The first panel shows FTA differential rather than foul differential: both tell the same story but FTA (free throw attempts taken) is the direct scoring consequence and is easier to interpret without statistical context. Small multiples on a shared layout let a reader scan in one sweep which mechanisms are sliding toward zero (free throw attempts, shooting) and which are flat (3P%, FT%); the era means in the table give the levels, the lines give the trends. The zero line matters: “toward zero” is the finding, so it has to be on the axis.

5. Referee Crew Home Foul Bias: Playoffs (`run_referee_analysis`)

The data. Per-official playoff records built from box-score officials data: for each of the 47 officials with ≥50 playoff games, the mean and SD of foul_diff = PF_home − PF_away across their games (negative = home-favoring), plus the same stats within each era.

The approach. Four layers, each fixing a known statistical trap:

Real one-sample t-tests per official, using each official’s per-game SD, testing whether their mean foul_diff differs from zero. (An earlier version used a degenerate zero-variance test that made every official “significant”; this is the corrected test.)
Benjamini–Hochberg FDR correction across all 47 simultaneous tests: with 47 officials, ~2 would clear p < 0.05 by luck alone; BH controls the expected false-discovery rate at 5%.
Method-of-moments variance decomposition of the career means: how much of the spread between officials is real vs. sampling noise.
Empirical-Bayes shrinkage of each official’s mean toward the league mean before ranking, plus the same variance decomposition within each era to test whether the spread of officials has compressed over time.

Why all the machinery. Referee-bias rankings are the most misuse-prone output in the project: a raw leaderboard of 47 noisy means will always produce dramatic-looking “most biased ref” headlines. The t-tests establish whether individual effects are real, BH keeps the count of significant officials honest, and shrinkage keeps the ranking from rewarding small samples.

What the results mean. The bias is universal, not a few bad apples: 45 of 47 officials show home-favoring means, 29 of 47 are individually significant and all 29 survive BH correction. That combination is the signature of a real, widespread effect. The league mean is −1.10 fouls/game in favor of the home team. Between-official differences are mostly noise (60% of observed spread; true between-official SD ≈ 0.41 fouls/game), so even shrunken rankings should be read loosely. The era decomposition shows compression over time: mean bias fell from −2.24 (1995–01) to −0.75 (2023–26), and in the recent eras the true between-official SD estimates hit zero: modern officials are both less home-favoring and more uniform. (The headline numbers in home_court_findings.md quoting “−1.6 → −0.7” come from Section 4’s game-level playoff table; this section’s −1.10 league mean is an across-officials average and differs slightly by construction.)

Why this chart. Two panels for two jobs. A horizontal ranked bar chart of the top/bottom officials answers “who, and how big”, but on its own it is exactly the leaderboard bait the section warns against, so it is paired with a per-era box plot. The box plot shows the distribution of official biases narrowing and centering over time, which is the real finding; a bar ranking cannot show a distribution compressing, and a box plot is the standard tool for that.

6. Shot Zone Differentials by Era (`run_shot_zone_analysis`)

The data. Season-level (not game-level) home-minus-road differences in the share of FGA taken from four zones (paint, mid-range, corner 3, above-break 3) from the NBA’s shot-location tables, available only from 1996–97 (30 regular seasons, 23 playoff seasons).

The approach. Same template as Section 4: era means per zone plus an OLS trend on year. N is seasons, not games, so power is much lower.

Why. Section 4 shows home teams shoot better; this section shows they historically also shot from better places. Zone shares isolate shot selection from shot making.

What the results mean. The home paint advantage is evaporating in the regular season: +1.28 pp of FGA share in 1995–01 down to +0.24 in 2023–26 (trend −0.041/yr, p < 0.001), with the mid-range deficit shrinking in mirror image (+0.025/yr, p < 0.001). Visiting teams now generate paint shots nearly as well as home teams: analytics-driven offense doesn’t care where it’s played. The playoff trends point the same direction (paint −0.032/yr) but are not significant on only 23 seasons of noisier data; the 2023–26 playoff paint advantage (+1.35) remains near its historical level, so the convergence is only firmly established for the regular season.

Why this chart. Four panels, one per shot zone, each a home-minus-road share line over time with a zero reference, the same small-multiple logic as Section 4. The eye tracks the paint advantage sliding toward zero and the mid-range deficit closing in mirror image across the panels. Lines rather than bars because the claim is a multi-decade convergence trend, not a level comparison.

7. Mediation: Box-Score Channels (`run_mediation_analysis`)

The data. All games with the four home-minus-away channel differentials: eFG% (shooting), fouls (which carries the free-throw-attempt channel), turnovers, and rebounds (49,104 regular-season and 3,292 playoff games). FT% diff is excluded as negligible (mean ≈ +0.3 pp).

The approach. A linear-probability model (LPM), OLS of home_win on the four differentials, with cluster-robust SEs by season, used to drive two exact accounting identities:

Level identity: mean win % = intercept + Σ (coef × mean diff). This splits the home advantage (the amount above a coin flip) into a contribution from each channel.
Trend identity: total pp/yr = unmediated pp/yr + Σ (coef × channel trend/yr). This splits the decline into per-channel contributions, using each channel differential’s own year-trend (from the Section 4 template).

A third block, a 3PA-control diagnostic, was added to settle whether the turnover and rebounding contributions are independent or merely downstream of the three-point revolution. For each channel it refits the differential’s year-trend twice, channel ~ year and channel ~ year + tpa_rate_avg, with season-clustered SEs, and reports how much of the year-trend the game-level 3PA rate absorbs. Game-to-game 3PA variation within a season gives the control real identifying power (season means alone would be near-collinear with year). The test is asymmetric: a trend that survives the control is strong evidence of an independent driver; heavy absorption is only weakly informative because 3PA and the calendar move together.

Why an LPM, not a logit. The whole point is the additive decomposition, contributions that sum exactly to the level and to the trend. That additivity holds only in a linear model; a logit’s nonlinearity breaks the identity. The usual LPM cost (fitted probabilities can leave [0,1]) is irrelevant for an accounting exercise. The channels are proximate, how HCA expresses itself in the box score, so the level/trend split is mediation in the accounting sense; the 3PA-control diagnostic is what adds a causal-ordering question on top.

What the results mean. The four channels capture nearly all of HCA’s level in both contexts and nearly all of its regular-season decline:

Regular-season level: channels carry 95% of the +10.1 pp home advantage. Shooting (eFG%) is the largest single channel at 43% (+4.4 pp), then rebounds 25% (+2.5 pp), fouls 14% (+1.4 pp), turnovers 13% (+1.3 pp); 5% unexplained.
Regular-season trend: channels carry 96% of the −0.244 pp/yr decline, spread fairly evenly across rebounds (30%), turnovers (27%), shooting (21%), and fouls (18%); only 4% is unmediated.
Playoffs: channels carry 93% of the level but only 67% of the decline: 33% of the playoff decline runs outside the measured box-score channels.

The 3PA-control diagnostic then resolves the obvious follow-up: are rebounds and turnovers real drivers or just downstream of the perimeter shift? The answers differ by channel:

Shooting is fully downstream: controlling for 3PA, the home eFG% trend vanishes (absorbed ≈ 210%). The fading home shooting advantage is the three-point story. The point estimate even flips sign, but 3PA rate is a mediator of the same strategic shift, and conditioning on a mediator is exactly where a coefficient can flip as an artifact, so read this as “fully absorbed,” not as a genuine reversal of the shooting advantage.
Rebounding is independent: only ≈8% of its year-trend is absorbed and it stays highly significant (p < 0.001). The home team’s rebounding advantage has slid for reasons the perimeter shift does not explain, a genuine fourth strand of the decline, now reflected in home_court_findings.md §3 and §7 (Summary). In the playoffs the rebounding fade is, if anything, sharper net of 3PA.
Fouls and turnovers are roughly half-and-half (≈51% and ≈54% absorbed) but both survive, partly the perimeter story, partly their own.

So the earlier worry that the turnover/rebound shares were “just downstream” was half right (turnovers, partly) and half wrong (rebounding is its own thing). One remaining caution: the playoff numbers fold in the seed-quality gap (the home team is usually the better team), which Section 26 isolates and controls.

A fourth block checks whether the pooled coefficients are stable across eras. The pooled decomposition uses one set of channel weights estimated across all 43 seasons, which assumes the marginal effect of each channel on home winning probability has not shifted over time. Re-fitting the LPM within each of the six rule-change eras (regular season only; playoffs have too few games per era for stable fits) shows the coefficients barely move: eFG% ranges +3.28 to +3.61 pp per unit, fouls −1.63 to −2.20, turnovers −3.19 to −3.57, rebounds +1.57 to +1.70, all within roughly 20% of their pooled values. The slight recent drift in the foul coefficient (weaker in 2018–26) is consistent with foul differentials themselves compressing: when there are fewer fouls to call asymmetrically, each remaining foul call carries slightly less decisive advantage. None of the shifts are large enough to question the decomposition. The channel share percentages are a blend of very similar effects across eras, not an artifact of mixing radically different regimes.

A fifth block puts bootstrap 95% confidence intervals on every share percentage by resampling whole seasons with replacement (B = 500) and recomputing the decomposition each time. The band is the 2.5–97.5 percentile across resamples. In the regular season the shares are tightly pinned: level [91, 97]% total mediated, trend [87, 107]%; individual channel trend bands are 10–15 pp wide (e.g. eFG% trend: [11, 28]%, REB trend: [25, 38]%). In the playoffs the bands are far wider because each playoff season carries only ~80 games; the eFG% and turnover trend shares have CIs spanning ±40 pp, meaning those individual playoff shares are loosely determined. The playoff headline (67% of the decline mediated) has a bootstrap band of [38, 107]%. Read the regular-season shares as reliable; read the playoff trend shares as directional. Resampling seasons rather than individual games preserves the block structure of the data: correlations within a season are intact in every resample.

Why this chart. Stacked horizontal bars, normalized to 100%, one stack for the level, one for the decline, regular season vs. playoffs. The whole point of a decomposition is composition: how the advantage splits into parts that sum to a whole. A stacked bar is the one chart form that shows shares adding to 100% at a glance; a line or grouped bars would hide the very accounting identity the LPM exists to deliver. The grey residual segment is deliberate too: it shows the unexplained remainder rather than quietly dropping it.

7a. Out-of-Sample Forecast (`run_out_of_sample_forecast`)

Why this section exists. The mediation decomposition (Section 7) fits the four-channel model on all 43 seasons and reports that channels explain 96% of the decline. Fitting and testing on the same data risks overfitting: the model has four predictors and 43 data points, so it might be capturing historical noise as structure. This section answers the harder question: does the channel mapping estimated on early seasons predict the later decline it never saw?

The approach. A train/test split on the season-level mediation series. The LPM from Section 7 is re-estimated on the training seasons (1984–2013) only; all four channel coefficients are frozen at those 1984–2013 values and never updated. For each held-out season (2014–2026), the model predicts that season’s home win % by applying the frozen mapping to that season’s actual box-score channel edges. Two baselines compete: (a) a flat forecast using the training-era mean home win %, and (b) a trend extrapolation projecting the training-era linear year-trend forward into the test window. The quality metric is RMSE (root mean squared error) across the 13 held-out regular-season seasons (12 playoff seasons, with the 2020 playoff bubble excluded).

What the results mean. In the regular season the frozen early channel model reaches 0.95 pp RMSE vs. 1.45 pp for the trend extrapolation and 5.48 pp for the flat mean. The channel model wins because it responds to the actual edges in each held-out season: when rebounding and foul differentials compressed sharply in 2020–22, the frozen coefficients translated that compression into lower predicted home win rates, tracking what actually happened. The trend extrapolation cannot do that: it projects the pre-2014 slope, which is slightly too steep for the post-2018 period. In the playoffs the margin is larger in absolute terms (3.87 pp channel vs. 7.30 trend vs. 8.11 flat) but noisier, because each playoff season is only ~80 games; the individual-season predictions vary more wildly. The out-of- sample result is the sharpest validation of the mediation mechanism: the box-score mapping is stable across the train/test split, not a post-hoc fit to hindsight.

Why this chart. A dual-line plot of actual vs. channel-predicted home win % for the 2014–2026 held-out seasons, with the trend-extrapolation line as a third reference. Putting all three on one panel makes the main claim immediately visible (the channel line tracks the actual season-to-season zigzag while the trend line slowly diverges) without needing a table. The RMSE numbers in the text then quantify what the chart shows.

7b. Mediation Sensitivity to Unmeasured Confounding (`run_mediation_sensitivity`)

Why this section exists. The mediation (Section 7) is an accounting decomposition: it splits the home advantage into channel shares but assumes the channels are the path the advantage takes. If some variable the box score never recorded is associated with both a channel and the outcome, that channel’s coefficient is biased and its share is off. This section bounds that risk with sensitivity to unmeasured confounding in the sense of Cinelli & Hazlett (2020): two summaries, the partial R² and the robustness value (RV), that say how strong a hidden confounder would have to be to overturn a channel’s estimated effect.

The approach. Refit the full mediation model home_win ~ year + efg_pct_diff + foul_diff + tov_diff + reb_diff by OLS, regular season and playoffs separately, using classical (non-robust) standard errors and residual degrees of freedom, the sensemakr standard. For a channel with t-statistic t on dof residual degrees of freedom:

Partial R² = t² / (t² + dof). This is the share of the outcome variation the channel explains once the other terms are already in the model: a measure of how much work the channel does.
Let f = t / √dof (the partial Cohen’s f). The robustness value is RV = ½·(√(f⁴ + 4f²) − f²). It is the threshold, on a 0–1 scale, such that a confounder explaining at least that fraction of the residual variation in both the channel and the outcome could drive the channel’s coefficient to zero. A confounder weaker than the RV on either side cannot.

Both are reported as percentages. Higher RV means the link is harder to explain away. The cluster-by-year p-value from Section 7 is printed alongside for context, but the RV is computed from the classical t-statistic, not the clustered one.

What the results mean. In the regular season the shooting channel carries a robustness value of 60.5% against a partial R² of 48.1%, and the foul channel a robustness value of 28.9% against a partial R² of 10.5%. A confounder would have to explain a large share of the leftover variation in both the channel and home wins to erase either link, which is a demanding requirement. The playoffs give similar values on far fewer games. This bounds robustness to an omitted cause; it is not a proof of causation, since the design is observational and the channels remain proximate box-score expressions of the advantage.

Why no chart of its own here. The companion figure (home_court_mediation_sensitivity.svg) is a horizontal bar of each channel’s robustness value, regular season and playoffs; taller bars resist a hidden cause.

8. Rest Differential: Buckets and Era Stability (`run_rest_bucket_analysis`)

The data. All games with computable rest for both teams (48,424 regular season, 2,956 playoffs), bucketed into away-more-rested / equal / home-more-rested.

The approach. Bucket win rates with a chi-square test across buckets; a bivariate logistic regression of home_win ~ rest_diff within each era; and a rest × era interaction LR test (comparing rest_diff + C(era) against rest_diff * C(era)).

Why. The buckets make the effect visible in plain percentages. The per-era logits and the interaction test answer the change-over-time question that drives the whole project: did the rest effect itself strengthen or weaken, which could have contributed to the HCA decline?

What the results mean. Rest matters: regular-season home win % runs from 57.6% (away more rested) to 62.8% (home more rested), χ² p < 0.001, roughly +1–3 pp per day of rest advantage in every era. The playoff buckets are more extreme (75.0% when home has more rest) but tiny (144 games), and confounded, see Section 9. The key result is the interaction test: p = 0.474 (RS) and 0.727 (playoffs). No evidence the rest effect changed across eras. Rest is a real component of any given night’s HCA, but a stable one; it cannot explain the 40-year decline.

9. Rest, Altitude, and Time Zone (`run_factor_summary`)

The data. Games with complete rest and time-zone features: 48,424 regular season, 2,956 playoffs.

The approach. Bivariate logistic regressions, each factor alone against home_win, in both contexts, with marginal effects in pp and 95% CIs. Then a targeted follow-up: playoff rest re-estimated with quality_diff (the home–away gap in regular-season win %) added as a control.

Why bivariate. This section answers “does each factor matter at all?” in its simplest form; the multivariable versions live in Section 23. The playoff quality control exists because playoff rest is endogenous: teams earn extra rest by sweeping, and teams that sweep are better teams. Without the control, the rest coefficient absorbs team quality.

What the results mean.

Rest: significant in both contexts: +1.6 pp/day regular season, +2.4 pp/day playoffs (bivariate). But the playoff effect dies under the quality control: rest drops to +1.6 pp/day with p = 0.113, while quality_diff is overwhelming (+112 pp per unit, p < 0.001, an extrapolated marginal effect over a full 0-to-1 win-% gap, so it exceeds the 100 pp a probability could literally move). Playoff “rest advantage” is mostly just being the better team.
Altitude: Denver/Utah home games run +7.9 pp above baseline in the regular season (p < 0.001) but −1.6 pp, n.s., in the playoffs. The playoff null is partly confound (good Denver/Utah teams face good opponents) and partly small samples, but there is no detectable playoff altitude advantage.
Time zones: null in both contexts (−0.4 pp/zone RS, p = 0.086; +1.0 playoffs, p = 0.330). Only 107 coast-to-coast playoff games exist in 43 seasons, so the playoff test has little power, but the regular-season test has plenty and still finds nothing meaningful.

10. League-Wide 3-Point Shooting (`run_3pa_analysis`)

The data. Per-game combined 3PA rate (tpa_rate_avg: both teams’ threes as a share of both teams’ FGA), in both contexts.

The approach. Five layers, run for regular season and playoffs:

Season-level Pearson and Spearman correlations between mean 3PA rate and home win %.
A game-level bivariate logistic of home_win ~ tpa_rate_avg with season-clustered SEs.
The same logistic controlling for era (+ C(era)), the critical test.
A partial correlation: detrend both season-level series against year, then correlate the residuals. If the raw r collapses once the shared trend is gone, the correlation was mostly the trend; if a substantial piece survives, there is a genuine year-to-year link.
A rolling 10-season Pearson r to check whether the relationship is stable across the sample or only appears in one stretch (sign flips or wide swings would point to a spurious, trend-driven correlation).

Why the era control is the crux. 3PA rate and HCA both trended hard over 40 years, so a raw correlation between them is guaranteed and proves nothing (“ice cream sales and drownings”). The within-era model asks: among games in the same era, do higher-3PA games show lower home win rates? If yes, the relationship survives removal of the shared time trend and is much more likely to be mechanistic (more threes → more variance → weaker advantage for the slightly better side, which at home is usually the home team).

What the results mean. The season-level correlation is enormous (r = −0.90 regular season) but, per the above, that alone is just the two trends. The decisive result is that the within-era effect barely budges from the bivariate one: −2.27 pp per 10 pp of 3PA rate (p < 0.001) vs. −2.64 unadjusted. The 3PA–HCA link is not merely the shared trend: it holds game-by-game within eras. The playoffs show an even stronger coefficient (−3.12 pp per 10 pp within era) at p = 0.027 on 3,292 games, directionally identical and now clearly significant. This is the strongest mechanistic candidate the data offers for the decline.

Cointegration and detrending. Two checks confirm that the raw r = −0.90 is mostly, but not entirely, the shared trend. First, an Engle-Granger cointegration test: both 3PA rate and home win % are I(1) (nonstationary trending series, per ADF unit-root tests), but they are not cointegrated, so they have no genuine long-run equilibrium relationship and a large part of the raw correlation is just two series drifting in opposite directions for 43 years. Second, the partial correlation quantifies how much: detrending both series against year drops the season-level r from −0.902 to −0.526 (still p < 0.001), so roughly 40% of the raw correlation is the shared trend and a real year-to-year association remains. (The rolling 10-season r swings from −0.87 to −0.19 with no sign flips, moderate instability consistent with a relationship that is partly trend-driven.) The reconciliation is the within-era game-level effect: the raw r overstates the link, the detrended residual and the within-era logit agree that a genuine component survives, and the within-era result is the cleanest evidence of it. This is why Section 10’s critical test is “does it survive the era control,” not “how strong is the raw r.”

Why this chart. Three panels that walk the trap and its resolution. Panel 1 is a dual-axis time series, 3PA rate rising as home win% falls, which looks like proof but is exactly the shared-trend illusion. Panels 2 and 3 are season scatters (regular season, playoffs) with the raw correlation annotated. Showing the seductive dual-axis line right next to the scatter is deliberate: it puts the very correlation the within-era model then has to defuse in front of the reader, so the payoff lands.

11. Granger Causality: Does 3PA Lead HCA? (`_run_granger_3pa`)

The question. The within-era test (Section 10) establishes that higher-3PA games tend to have lower home win rates within the same era. But correlation within eras still doesn’t settle the direction: does the three-point revolution cause the decline, or do both respond to the same underlying forces (analytics culture, officiating philosophy, roster construction) without one driving the other?

Granger causality offers a limited time-series test: if 3PA rate in year t predicts home win % in year t+1 better than past HCA values alone do, then 3PA “Granger-causes” HCA: it leads in the time series, at minimum. That is necessary (though not sufficient) for a causal story. If the reverse also holds (HCA predicting future 3PA), causality runs both ways or both are downstream of something else.

The approach. A VAR-based Granger test (grangercausalitytests from statsmodels) on the two-variable system [ΔHCA, Δ3PA], where Δ denotes first differences (used because both series are I(1); Granger tests assume stationarity). The test at lag L fits two VARs, one with HCA’s own lags only, one adding L lags of 3PA, and compares the residual sums of squares with an F-test. Both directions are tested; with N = 42 first-differenced observations, max 2 lags is used to preserve degrees of freedom.

What the results mean. No Granger causality in either direction, at either lag (all F p-values > 0.2). Neither does 3PA rate in year t predict ΔHCA in year t+1, nor does HCA in year t predict Δ3PA in year t+1. The two series trend together but neither temporally leads the other.

This is informative even though it’s a null result: it means the 3PA–HCA association is contemporaneous rather than leading/lagging. The within-era game-level link (Section 10) is the evidence that it’s a real mechanical effect, not just a shared trend; the Granger null suggests that the annual adoption of threes and the annual change in HCA move together in the same season rather than one predicting the other a year ahead. Both may be downstream of the same broader strategic shift in how the game is played. The Granger test’s practical limit here is power: with only 42 seasonal observations, lags of 1–2 years leave few degrees of freedom, so moderate causal effects could go undetected.

12. Rebounding Decomposition (`run_rebounding_decomposition`)

Why this section exists. Section 7 establishes that rebounding carries the single largest share of the decline but cannot say why the home rebounding advantage faded. This section answers that, using only the cached box scores.

The data. The same game-level dataset, now carrying four rebounding columns computed in _compute_rebound_components: oreb_diff and dreb_diff (home-minus-away offensive/defensive rebounds), reb_diff (total), and reb_share_edge.

The rebound-share metric. Raw rebound counts are a poor measure of skill: they rise and fall with pace and with how many shots miss (more misses → more boards to grab). The clean measure is the share of available rebounds a team captures. A team’s offensive-rebound share is

OREB ÷ (own OREB + opponent DREB)

i.e. offensive boards grabbed divided by the team’s own missed shots that were reboundable. reb_share_edge is the home team’s offensive-rebound share minus the away team’s, in percentage points. Because it is a ratio of boards won to boards available, it is immune to the pace/shot-volume confound, a like-for-like measure of who controls the glass.

The approach. An era table and an OLS year-trend (stat ~ year) for each of the four columns, separately for regular season and playoffs, identical in form to the differential analysis (Section 4). Then a season-level Pearson correlation between the mean reb_share_edge and the league-wide offensive-rebound rate (league_oreb_rate = both teams’ OREB ÷ all rebounds), testing whether the home advantage tracks the league’s strategic retreat from the offensive glass.

Reading the output. - The advantage died on the offensive glass: regular-season oreb_diff falls from +0.61 to −0.05 (home teams no longer out-offensive-rebound visitors at all), while dreb_diff only softens (+1.64 → +0.59). All trends negative and highly significant (OREB −0.018, DREB −0.027, REB −0.044 per year, all p < 0.001). - It is not a pace artifact: reb_share_edge still collapses ~10×, +2.14 pp → +0.21 pp (trend −0.052 pp/yr, p < 0.001). - It is league-driven: the season-level correlation between the home share advantage and the league offensive-rebound rate is r = +0.82 (p < 0.001, N = 43); the league rate fell 33% → 26% over the same span. As teams abandoned offensive rebounding for transition defense, the effort-driven boards where a home advantage could form disappeared. However, the cointegration check shows both series are I(1) (nonstationary) but not cointegrated: the r = +0.82 is likely spurious correlation from parallel trends rather than a genuine long-run relationship. The section-level 3PA-control from Section 7’s mediation (rebounding survives with only ~8% absorbed) is the stronger evidence that the rebounding fade is a real, independent trend. - The playoffs show the same shape (share advantage +2.74 → +0.70 pp, trend −0.046 pp/yr, p = 0.004), on a smaller sample.

A note on the share identity. Because available offensive rebounds for one team are the same boards the other team can defensively rebound, the home team’s offensive-share advantage equals its defensive-share advantage exactly: there is one “control of the glass” number, reported here as the offensive-rebound share advantage.

Player-tracking footnote. A separate set of helpers (compute_tracking_rebound_stats and run_tracking_rebound_analysis) pulls NBA player-tracking and hustle data (offensive-rebound conversion, box-outs, second-chance points) split Home/Road via location_nullable. It corroborates the mechanism (no measurable home box-out advantage today, offensive-rebound conversion still shrinking) but only covers the tracking era (~2014 on), too short to carry the 40-year story, so it is summarized in one sentence in home_court_findings.md §3 rather than reported as its own section here. The code is retained but unwired from the pipeline.

Why this chart. Four panels for the rebounding and turnover story. Panel 1 puts home and away offensive-rebound rates on the left axis and defensive-rebound rates on the right, with symmetric y-limits (left 17–37%, right 63–83%) so the convergence reads at the same scale on both sides. The design makes the accounting identity explicit: DREB rate = 100 − opponent OREB rate, so a single asymmetric retreat from the offensive glass produces matching collapses on both sides simultaneously: one panel rather than two. Panel 2 shows the raw OREB and DREB differentials (home minus away per game), which are pace-sensitive but make the absolute magnitudes visible; the DREB advantage fell more in absolute terms because it starts from a higher base. Panel 3 is a scatter of the total rebound differential against each season’s home win rate: the claim is an association, and a scatter with a fitted line shows that more honestly than a time-series overlay. Panel 4 shows the turnover advantage (away minus home turnovers per game), placed here because the mediation analysis (Section 7) links both categories: they declined over the same span, and pairing them lets the eye compare their shape and timing.

13. Player-Tracking Rebounding Mechanism (`run_tracking_rebound_analysis`)

Why this section exists. The rebounding decomposition (Section 12) shows the home advantage died on the offensive glass, using box scores back to the 1980s. This section corroborates how that advantage expresses itself up close, using the NBA’s player-tracking and hustle data, a much shorter window, but one that can see box-outs and second chances the box score cannot.

The data. Home-minus-road differentials in three tracking metrics, split Home/Road via location_nullable: offensive-rebound conversion (share of one’s own missed shots recovered), box-outs per game, and second-chance points per game. Coverage is the tracking era only: ~2013–14 on (13 seasons), ~2016 on for box-outs (11 seasons).

The approach. Identical in form to the box-score sections: a season-level mean and an OLS year-trend (stat ~ year) per metric, with significance stars. With at most 13 seasons, power is limited: this is a corroborating check, not a primary test.

What the results mean. The modern home advantage is small and flat-to-declining on every metric. Offensive-rebound conversion is the only one with a significant trend (mean +0.71 pp, −0.086 pp/yr, p = 0.024), still shrinking even within the tracking era. The box-out advantage sits at essentially zero throughout (−0.000, p = 0.78) and the second-chance-points advantage fades without reaching significance (+0.29, −0.016/yr, p = 0.30). The reading is that the offensive-glass advantage had largely collapsed before high-resolution tracking even began: by the time the cameras switched on, little advantage was left to measure. The window is too short to carry the 40-year story (Section 12 does that), so this section only confirms the modern mechanism.

Why this chart. Three small-multiple panels, one per tracking metric, each a home-minus-road line over the tracking era with a zero reference. The shared layout mirrors the box-score differential charts (Sections 4 and 12) so the eye reads them the same way, and the flat-to-declining lines hugging zero are the visual point: the advantage is already gone where the cameras can see it.

14. Rule-Change Eras (`run_era_analysis`)

The data. All games, split by the six rule-change eras (1984–94, 1995–01, 2002–04, 2005–17, 2018–22, 2023–26), run separately for regular season (49,107 games) and playoffs (3,292).

The approach. Raw win % per era, two-proportion z-tests between consecutive eras, then home_win ~ year + C(era) with a likelihood-ratio (LR) test against year-only.

Why. The question is whether the 40-year decline happened as a smooth drift or in discrete steps at specific rule changes. The z-tests find the candidate steps; the trend-controlled model asks whether any step is bigger than the underlying drift would predict. Because almost none of them is, this analysis lives in home_court_findings.md §4 (“What Didn’t Drive the Change”): rule changes are the most natural suspect, yet only one left a mark.

What the results mean. In the regular season, two boundaries show raw significant drops: 1994→95 (−4.9 pp) and 2017→18 (−3.2 pp). After controlling for the year trend, only the 1995–01 dummy survives (−2.6 pp, p = 0.010), and the era dummies are jointly significant (LR p < 0.001). So the regular-season decline is mostly smooth drift plus one genuine discrete drop at the 1994–95 hand-checking rules. In the playoffs, nothing survives: no z-test is significant and the LR test is p = 0.815: the playoff decline is pure drift, with no rule-change fingerprints. (Small samples mean limited power, but there is simply no signal there.) The same trend-vs-boundary logic recurs for the 2014 Finals format change in Section 28.

Why this chart. This section has no separate figure: the era structure it tests is already drawn as the shaded eras and the era-bar panel of the Section 1 decline chart. The discrete-drop question is about reading those era levels against the smooth trend, an inference the z-tests and LR test carry, not something a new picture would add.

15. Interrupted Time Series: 1994-95 Boundary (`run_its_test`)

Why this section exists. The rule-change era analysis (Section 14) finds one genuine discrete drop, at 1994–95. This section examines that single boundary in isolation, separating an immediate level drop from a change in the rate of decline, the two ways a rule change could leave a mark.

The data. The season-level home win % series (43 regular-season, 42 playoff seasons), weighted by games per season.

The approach. An interrupted-time-series (ITS) regression by weighted least squares:

home_pct ~ year + post95 + (year − 1994)·post95

where post95 = 1 from 1994–95 on (an immediate level shift) and the interaction is the change in slope after the break. The level term asks “did HCA step down the instant the rules changed?”; the slope term asks “did the rate of decline change?”

What the results mean. The regular-season fit (R² = 0.78) shows a steep pre-break trend (−0.52 pp/yr, p = 0.004), no significant immediate level drop (−0.62 pp, p = 0.597), and a borderline slope change (+0.34 pp/yr, p = 0.060) that flattens the decline from −0.52 to −0.18 pp/yr afterward. So 1994–95 reads not as a cliff but as a bend (the decline slowed over the following seasons rather than dropping in a single step), exactly consistent with the QLR break landing at 1999 (Section 2) rather than 1995. In the playoffs nothing is significant (level p = 0.55, slope p = 0.39): the postseason has no detectable 1994–95 signature, matching the era analysis’s finding of pure drift. (Section 14’s era model, which does flag a significant 1994–95 drop after partialling the year trend, and this ITS are two cuts at the same boundary; together they say the effect is real but gradual, not a clean discrete step.)

16. Placebo Tests: Is 1994-95 Uniquely Significant? (`run_placebo_tests`)

Why this section exists. Section 14 singles out 1994–95 as the one rule boundary that left a mark. A placebo test guards against a tempting error: test enough candidate years and some will look significant by chance. This asks whether 1994–95 stands out, or is just one of many “significant” boundaries.

The data. The season-level home win % series.

The approach. For every candidate year t from 1987 to 2010, fit pct ~ year + step_t, where step_t = 1 for seasons from t on. A significant negative step coefficient means a discrete drop at that boundary. The 1994–95 boundary is one of 24 placebos; the question is whether it is special.

What the results mean. 1994–95 is in the significant-negative window (−2.00 pp, p = 0.043), but so are the years 1990–1995 around it, and that is the subtle part. When a real break exists, any boundary placed a few years before the drop also tests significant, because it sweeps the decline into its “post” window. So the cluster of significant negatives in the early 1990s is the expected fingerprint of a genuine break in that period, not 24 independent findings. (The significant positive steps after ~2002 are the mirror image: post-1999 HCA sits “too high” relative to the steeper pre-1999 trend, the slope moderation QLR found in Section 2.) The placebo test therefore corroborates that something real happened in the early-to-mid 1990s but cannot isolate 1994–95 by itself; the trend-controlled era model (Section 14) is what pins the effect specifically to that boundary. In the playoffs no early-1990s boundary is significant at all (only a couple of positive steps in 2004–2006), reaffirming that the postseason decline carries no 1994–95 signature.

17. Channel Event Study: Which Changed First at 1994-95? (`run_channel_event_study`)

Why this section exists. Sections 14–16 establish that 1994–95 left a real mark on home court advantage. This section asks which mechanism moved at that boundary, and in particular whether the fingerprint matches the leading suspect, the hand-checking crackdown. If hand-checking is the cause, the foul differential should jump immediately while the other channels respond little or only gradually.

The data. The four mediation channels (Section 7) as season-level home-minus-away differentials: fouls, eFG%, turnovers, rebounds.

The approach. The same interrupted-time-series model as Section 15, run per channel: diff ~ year + post95 + (year − 1994)·post95. The level shift (post95) is the immediate response at 1995; a mechanism that changed the instant the rules did should show a significant level term. (Sign note: foul_diff = PF_home − PF_away is negative when the home team is favored, so a positive level shift means the home foul advantage shrank immediately.)

What the results mean. Only the foul channel shows a significant immediate response. In the regular season the foul-diff level shift is +0.44, p = 0.007 (the home foul advantage contracted the moment the hand-checking rules took effect), while eFG% (p = 0.33), turnovers (p = 0.18), and rebounds (p = 0.85) show no significant jump. That is exactly the signature expected if the hand-checking crackdown was the operative change: it acts directly on fouls and defense, while the other box-score edges drifted on their own slower schedules. The playoffs show no significant channel shift (small samples, and no 1994–95 break to begin with). This is the closest the data comes to naming a mechanism for the one rule change that mattered.

18. Travel Distance (`run_travel_analysis`)

The data. All games with arena coordinates for both teams; distance is the haversine (great-circle) miles from the away team’s home arena to the game arena.

The approach. Win % by distance bucket (0–500, 500–1000, 1000–1500, 1500+ miles), plus a bivariate logistic regression of home_win ~ distance_miles with cluster-robust standard errors clustered on season: games within a season share league-wide conditions, so treating them as independent would understate the standard errors.

Why. “The road team is tired from the flight” is one of the oldest HCA folk theories, and distance is cleanly measurable. Buckets show the shape; the logistic puts a per-mile number and CI on it.

What the results mean. Nearly nothing. The regular-season coefficient is statistically significant (p = 0.010) but practically trivial: −0.07 pp per 100 miles, so a 2,500-mile cross-country trip costs the visitor under 2 pp, and the buckets don’t even decline monotonically (500–1000 miles has the highest home win rate). With N = 49,107, significance is cheap; the effect size is the story. In the playoffs the effect is null outright (p = 0.888). Travel does not explain HCA’s existence or its decline.

19. Back-to-Backs (`run_b2b_analysis`)

The question. One popular theory for the HCA decline is “load management”: NBA schedules now include fewer back-to-back games (zero days of rest), so visiting teams are less often exhausted. Fewer tired visitors → a smaller scheduling advantage for the home team → lower home win rates. This section tests whether that story holds up quantitatively.

The data. Regular-season games with a computable prior-game date for both teams (48,424 games; back-to-backs are rare enough in the playoffs to be ignored).

The approach. Two layers:

Era-frequency table of visitor and home B2B rates, alongside the era home win %, to see whether the schedule shift and the HCA decline move together.
Shift-share decomposition of the 1984–94 → 2023–26 home-win change (−9.29 pp) into two components: (a) the frequency component, how much of the change is explained by the shift in B2B scheduling, holding per-situation win rates fixed at their 1984–94 values; and (b) the win-rate component, how much is explained by the home advantage within each rest situation fading, holding scheduling fixed.

The shift-share identity is exact: frequency + win-rate + interaction = total change.

Why. A pure frequency story would show the frequency component absorbing most of the −9.29 pp, with win rates within each situation roughly stable. A frequency component near zero would rule the story out. The decomposition separates those two possibilities cleanly without a regression.

What the results mean. The schedule shift is real (visitor B2Bs fell from 35.0% of games in 1984–94 to 18.8% in 2023–26) but its effect on the overall decline is trivial. When a visitor is on a B2B, the home team wins 64.7% vs. 59.1% when neither team is on one, a +5.6 pp lift. But that lift is modest and the frequency shift is partial, so the frequency component accounts for only −0.71 pp of the −9.29 pp total decline, about 8%. The remaining 92% is the win-rate component: the home advantage within every rest-situation category has simply faded, independent of scheduling. Load management did not drive the decline.

Why this chart. This section adds no figure of its own. The era-level B2B frequency and home win % are captured in the era table, and the shift-share is an exact arithmetic decomposition, two numbers that sum to the total. A chart would add no information the table doesn’t already carry.

20. Pace (`run_pace_analysis`)

The data. Per-game average possessions (pace_avg) and the leave-one-out expected_pace described in Section 0.

The approach. The same three-layer template as Section 10 (season correlations, game-level logit, within-era logit), plus a fourth layer: the same logits re-run on expected pace instead of realized pace.

Why expected pace matters. Realized pace is contaminated by reverse causality: blowouts inflate possession counts (garbage time, intentional fouling, no late-game stalling), and home blowouts are disproportionately home wins. So a positive realized-pace coefficient may mean “winning causes pace,” not “pace causes winning.” Expected pace, built only from each team’s other games, breaks that loop.

What the results mean. Pace is a clean rule-out, and a nice demonstration of why the LOO version was needed. Season-level correlations are weak and non-significant in both contexts (RS r = +0.24, p = 0.12; playoffs r = −0.14, p = 0.37), and note pace is U-shaped over time (fast 80s, slow 90s–00s, fast again now) while HCA fell monotonically, so the two can’t share a trend. Realized pace shows a significant positive game-level effect (+2.3 pp per 10 possessions, p < 0.001), but switching to expected pace cuts it to +1.5 and kills significance (p = 0.227; within-era p = 0.063), confirming the realized effect was substantially outcome-driven endogeneity. Playoffs: null everywhere. Pace did not drive the decline.

Why this chart. The same three-panel layout as Section 10 (dual-axis time series plus two season scatters), chosen for the same reason and to invite the side-by-side comparison. It also makes the rule-out visible two ways: the dual-axis panel shows pace is U-shaped while HCA fell monotonically, so the two can’t even share a trend, and the flat scatters show the weak season-level association, before the leave-one-out test in the text delivers the verdict.

21. Competitive Balance / Parity (`run_parity_correlation`)

The data. Season-level: the standard deviation of all 30 teams’ win percentages (the parity measure, lower = more equal league) and the season’s regular-season home win %, 43 seasons.

The approach. Four layers:

Pearson and Spearman correlations between parity SD and home win %.
An OLS slope of home win % on parity SD, plus era-bucketed averages.
First-differenced correlation: Δparity vs. Δhome-win% year over year.
Residual-on-year correlation: each series detrended by its own linear year fit, then the residuals correlated.

Why the detrending layers. Same trap as Section 10: any two series that both trend over 40 years will correlate spuriously. The raw correlation here happens to be near zero anyway, but the detrended checks are the proper test of the year-to-year relationship: first-differencing and residualizing are the two standard ways to remove a common trend, and they have different noise properties (differencing amplifies measurement noise), so both are run.

Cointegration note. In this case the formal test is reassuring for a different reason: parity (win% SD) is I(0) stationary (ADF p = 0.023), while home win % is I(1), so the classical spurious-regression concern does not directly apply. A stationary predictor correlated with a nonstationary outcome is not a cointegration problem; the raw and detrended correlations are interpretable without that specific worry. The near-zero raw correlation (r = −0.09) is simply a genuine null.

What the results mean. The raw, trend-level answer is a rule-out: r = −0.092 (p = 0.56), R² = 0.009, and the era table actively contradicts the parity hypothesis (the league’s most unequal era, 1995–01, had falling HCA; the most equal, 2002–04, saw HCA tick up). Parity cannot explain the 40-year decline. The wrinkle: both detrended checks turn up a modest negative association (first-differenced r = −0.330, p = 0.033; residual r = −0.345, p = 0.023): in years when the league gets more equal, HCA dips slightly that same year. That runs in the direction the parity hypothesis predicts, but it is a small year-to-year wobble on 42–43 data points, flagged in the output itself as “interpret with caution.” It coexists with, and does not overturn, the main conclusion that parity didn’t drive the structural decline.

Why this chart. Two panels. A dual-axis time series (home win% vs. parity) shows the two series don’t track; a season scatter with a near-flat fitted line shows the same null at the cross-section. The dual-axis form is chosen precisely because it tempts the shared-trend reading, the same setup as the 3PA and pace charts, so the detrended correlations in the text have something concrete to rule out.

22. Arena Attendance (`run_attendance_analysis`)

The data. Per-game attendance scraped from Basketball-Reference, which, unlike NBA.com, publishes the gate for every game. It is reliable only from about 1999–2000 on, so this is a ~25-season series (27 seasons cached), not the full 40. Two slices: (A) league average attendance per game per season vs. the season’s regular-season home win %; (B) every 2020–21 game’s attendance paired with its home_win, the one season when crowd size swung game to game.

The approach. Two questions, deliberately separated:

Part A: does crowd size track HCA? Same four-layer detrending battery as Section 21: Pearson and Spearman correlations, then a first-differenced and a residual-on-year correlation to strip the shared long-run trend.
Part B: what is crowd presence worth? A logistic regression of home_win on attendance (scaled per 1,000 fans) across the 2020–21 games, reported as a marginal effect in pp, alongside the raw empty-vs-present home win split.

Why split size from presence. They are different hypotheses and the data answers them differently. Season-level attendance is nearly constant (every arena runs near capacity), so it can rule a size effect in or out but can say nothing about what a crowd is worth: there is no variation to exploit.

Cointegration note. League-average attendance is I(0) stationary (ADF p = 0.005): arenas have operated near-capacity for two decades with little secular drift. Since one series is stationary, the classical spurious-regression concern (two I(1) series falsely correlating) does not apply here. The detrended checks are still run as a standard robustness step, but the raw correlation is interpretable directly. The 2020–21 season supplied that missing variation by accident: COVID rules left some buildings empty and others partly filled, a quasi-natural experiment that isolates presence from everything else. Part B is closer to causal evidence than anything else in the report; the trade-off is a single season and a binary-ish exposure, so it is read cautiously.

What the results mean. Part A is a clean rule-out: the raw correlation is weak and non-significant (Pearson r = +0.25, p = 0.21), and both detrended checks are null (first-differenced r = +0.07, p = 0.72; residual-on-year r = +0.33, p = 0.09). The lone significant number, Spearman ρ = −0.49 (p = 0.009), runs against the crowd-size story: attendance climbed to record highs in the 2020s exactly as HCA bottomed out, so by rank the two move opposite. Crowd size is not behind the decline. Part B is where the crowd shows up: with the arena empty, home teams won just 51.0% (n = 573); with any fans present, 58.5% (n = 591). The per-1,000-fans logistic slope is small and not significant (+0.51 pp, p = 0.18), which is the point: the effect rides on the presence of a crowd, not its exact size, and it vanished the moment arenas refilled in 2021–22. A real ingredient of home court advantage, but a switch, not the four-decade dial.

Why this chart. The two panels mirror the two hypotheses the section deliberately separates. Panel 1 (dual-axis time series) answers crowd size: attendance flat near capacity while HCA falls. Panel 2 is a dose-response bar chart of 2020–21 home win% by attendance bucket: a bar per dose is the natural way to show the accidental experiment, with the empty-arena bar sitting at a coin flip and the filled bars climbing above it. Two different questions, so two different chart forms.

23. What Explains the Regular-Season Decline? (`run_sequential_decomposition`)

The data. Regular-season games with complete features (48,424).

The approach. Two decompositions of the same full model (home_win ~ era + rest_diff + altitude_home + tz_diff + covid), fitted by logistic regression with cluster-robust SEs (clusters = season):

Sequential ΔR²: five nested models, adding one block at a time (era first), recording how much McFadden pseudo-R² each block adds. McFadden R² = 1 − llf/llnull; its typical values are far smaller than linear R², so only relative shares are interpreted, never the absolute level.
Shapley decomposition: all 2⁵ = 32 subset models are fitted, and each block’s contribution is its average marginal R² across every possible order of entry (weighted by the Shapley formula). This removes the arbitrary “era goes first” advantage that sequential decomposition gives.

Why both. Sequential decomposition is intuitive but order-dependent: whatever enters first soaks up shared explanatory power. Shapley is the order-free correction. Reporting them side by side shows how much the ordering mattered.

What the results mean. The full-model coefficients confirm everything is simultaneously real: each era dummy is significantly negative and monotonically deepening (down to −9.0 pp for 2023–26 vs. 1984–94), rest +1.5 pp/day, altitude +7.8 pp, COVID seasons −2.3 pp, time zone −0.6 pp (significant but tiny). The decomposition splits the model’s explanatory power roughly 50/50: era (the structural decline) gets a 53% Shapley share (58% sequential, modestly inflated by going first), altitude 24%, rest 18%, with time zone and COVID under 5% each. Reading it back: the situational factors (rest, altitude) explain which games home teams win, but the era structure, the thing that changed over 40 years, is half the story, and none of the situational factors changed (Sections 8, 24), so they can’t be what drove the decline.

24. Pre/Post-2014 Coefficient Stability (`run_stability_analysis`)

The data. Regular-season games with complete features, split at 2014 (32,975 before, 15,449 after).

The approach. The logit home_win ~ rest_diff + altitude_home + tz_diff fitted separately on each half, comparing coefficients; then a formal pooled interaction model (rest + altitude + tz) * post2014, where each interaction term tests whether that factor’s effect changed and the post2014 main effect captures the level shift.

Why. The post-2014 window contains the steepest part of the recent decline. If rest, altitude, or time-zone effects had weakened in that window, they would be candidate explanations for it. Stable coefficients plus a falling intercept means the decline operates through some other channel.

What the results mean. That is largely the pattern. The rest and time-zone interactions are not significant (rest p = 0.142, tz p = 0.917); the altitude interaction is (p = 0.026), with Denver/Utah’s home advantage roughly halving after 2014. But the headline is the post-2014 level shift, which is large and unambiguous (−4.7 pp, p < 0.001) and dwarfs any factor-specific change. Home teams kept their rest advantage at full strength and most of their altitude advantage; they simply started winning less for reasons those factors don’t capture, pointing to the foul-bias and shot-selection channels in Sections 4 and 6. (Altitude’s −4.3 pp interaction is the one situational effect that has measurably weakened with the added seasons, though it touches only two teams.)

25. Playoff Series Structure (`run_series_breakdown`)

The data. All playoff games with a parseable game number, G1 through G7 (509 down to 188 games as series lengths thin out).

The approach. Home win % per game number; a chi-square contingency test of whether home win % is uniform across game numbers; and a weighted OLS trend of home win % on game number (weights = games per game number).

Why. Two distinct hypotheses live here. The chi-square asks “does game number matter at all?” The trend line asks the specific popular theory that road teams adapt as a series progresses (which would show as a negative slope, home win % falling in later games).

What the results mean. Game number matters enormously (χ²(6) = 84.5, p < 0.001) but there is no monotonic trend (−1.07 pp/game, p = 0.55). The pattern is entirely venue alternation: G1/G2/G5 at the higher seed run 69–75% home win rates; G3/G4/G6 at the lower seed run 55–56%. G7, back at the higher seed, is 63.8%. The “road teams figure it out by game 6” story has no support: what looks like series dynamics is just which arena the game is in, plus the fact that the higher seed is usually the better team.

Why this chart. Two panels. A bar chart of home win% by game number (G1–G7) with sample-size labels makes the venue-alternation sawtooth obvious (bars, because game number is a discrete category, not a continuous axis). The companion per-era line panel shows the sawtooth is stable across eras, ruling out the “teams adapt over a series” story visually before the trend test confirms no monotonic slope.

26. Playoff HCA: Seeding Quality Decomposition (`run_playoff_quality_decomposition`)

The data. All 3,292 playoff games with quality_diff = home team’s regular-season win % minus the away team’s, same season.

The approach. Three pieces:

Year-trend comparison across three logits (year only, quality only, year + quality_diff) to see how much of the playoff decline is absorbed once the team-quality gap is in the model (reported as “% of the year coefficient retained”).
A trend test on mean quality_diff over seasons: has the seed-quality gap itself narrowed over time, which could mimic a home-court decline?
A lower-seed-at-home check: home win % in G3/G4 games where the home team is objectively the weaker side (quality_diff < 0), which strips team quality out entirely and leaves only the venue.

Why. The playoff decline could be an artifact rather than a real weakening of home-court advantage: if top seeds no longer outclass their opponents as much, the playoff home team (usually the better team) would win less without home-court advantage itself changing. quality_diff is the control that separates “home-court advantage is genuinely weakening” from “seeds are more evenly matched.” This is the playoff counterpart to Section 23’s regular-season decomposition.

What the results mean. The decline is genuine home-court weakening, not seed compression. Adding quality_diff barely moves the year coefficient (−0.225 → −0.229 pp/yr; 102% retained, ≈ −2% absorbed), even though quality_diff itself is a massive predictor of any single game (+112 pp per unit of win-% gap, p < 0.001). The seed-quality gap has trended down slightly (−0.00026/yr, p < 0.001), but that drift doesn’t account for the home-win decline. The clincher is the lower-seed-at-home check: when the objectively weaker team hosts G3/G4, it still wins 51.5%, a pure venue effect with quality stripped out. This dovetails with Section 7 (playoff channels carry only 67% of the decline) and Section 9 (playoff rest is confounded with quality, but the decline is not).

26a. Regular-Season Quality Split (`run_regular_season_quality_split`)

The data. All 46,612 regular-season games with a quality_diff_prior, home team’s prior-season win % minus the away team’s, same-name teams only (see Related Work companion for the López-García et al. (2024) paper that prompted this test).

Why prior-season, not same-season. Section 26’s quality_diff (same-season win %) is a clean control for playoffs, because playoff outcomes never feed back into the regular-season win % it’s built from. Applying that same construction within the regular season would be circular: a team’s own home record is part of what makes up its season win %, so a team’s home wins would partly be predicting themselves. quality_diff_prior breaks that loop at the cost of a noisier proxy (a roster can change over an offseason).

The approach. Two pieces:

An era table restricted to games with at least a 10-point prior-season win % gap (so “stronger”/“weaker” means a real quality difference, not a near-coin-flip pairing mislabeled by sign), reporting home win % for the stronger-team-hosts and weaker-team-hosts splits by era.
Two significance tests on the full sample (every game with a valid quality_diff_prior, no 10-point restriction): an omnibus likelihood-ratio test comparing quality_diff_prior + C(era) against quality_diff_prior * C(era) (does the quality effect differ across eras at all), and a continuous quality_diff_prior * year interaction (does the size of the effect trend up or down linearly).

What the results mean. The omnibus era interaction is significant (χ²(5) = 64.68, p < 0.001): the quality effect is not constant across eras. The continuous interaction pins down the direction: a coefficient of −0.0281 per year (p = 5.91e-12), meaning quality’s effect on who wins at home has been shrinking, not growing, across 40 seasons. The era table shows the same thing in raw terms: the stronger-vs-weaker-home win % gap ran 34.9 points in 1984–94 and sits at 28.2 points in 2023–26, narrower rather than wider. That is the opposite direction from Section 26’s playoff seeding gap, which widened sharply over the same 40 years. Guard: rs_quality_diverges_from_playoffs.

27. Team Quality Fixed Effects Robustness (`run_team_quality_robustness`)

The question. The sequential decomposition (Section 23) identifies how much the era structure explains, but it does not control for which specific franchises happen to be home or away. Could the era coefficients be confounded by systematic changes in home-team composition: for example, if the 1984–94 era had the league’s dominant teams disproportionately hosting games, inflating the measured HCA?

The approach. Two logistic models, both with cluster-robust SEs on season:

Baseline: home_win ~ era + rest_diff + altitude_home + tz_diff + covid, the Section 23 full model.
With team fixed effects: the baseline plus C(TEAM_NAME_home) + C(TEAM_NAME_away), one binary indicator per franchise in each role. With 30 current and historical franchises, this adds ~58 dummies to the logistic.

The comparison focuses on the era dummy coefficients. If they shift substantially, the era structure was absorbing roster/venue composition effects rather than a genuine change in home-court dynamics.

Why team FE instead of quality scores. Pre-game quality scores require per-team season win% computed separately per game (to avoid look-ahead), which adds complexity without adding much for a league-wide trend question. Team fixed effects remove any time-averaged franchise-level advantage, a cleaner and simpler check of the composition confound. (Section 26a builds exactly this look-ahead-free quality score, quality_diff_prior, for a different question: not composition robustness, but whether quality’s own effect on who wins at home has changed over time.)

What the results mean. Era coefficients shift by at most 0.5 pp across all five eras (max |Δ| = 0.5 pp). The team fixed effects explain additional variation (McFadden R² rises from 0.005 to 0.027): individual franchises do have persistent home-win tendencies, but they are absorbed into the franchise intercepts, not into the era structure. The era decline is not an artifact of which teams happen to host games in which decades.

28. Playoff Format Periods (`run_format_period_analysis`)

The data. Playoff games only (3,292), grouped by the league’s playoff scheduling formats: 1984, 1985–02, 2003–13, and 2014–26 (the 2014 change moved the Finals from 2-3-2 back to 2-2-1-1-1).

The approach. Three layers:

Raw home win % per format period.
Two-proportion z-tests between consecutive periods, the simplest test of whether the win rate actually moved at each boundary.
A logistic regression of home_win ~ year + format_period, plus a likelihood-ratio (LR) test comparing it against home_win ~ year alone.

Why. The raw comparison (step 2) shows a big, significant drop at the 2014 boundary (−6.8 pp, p = 0.002). But HCA was also declining smoothly throughout, so any late-period dummy would look negative even if the format change did nothing. Step 3 separates the two stories: if the format dummies still matter after the year trend is in the model, the change had its own effect; if not, the drop is just the trend passing through the boundary.

What the results mean. Once the year trend is controlled, no format dummy is significant (all p between 0.24 and 0.30) and the LR test for the dummies jointly is p = 0.197. The post-2014 playoff drop is fully consistent with the secular decline; the format change itself is exonerated.

Why this chart. The format periods are shown as paired regular-season/playoff bars: discrete periods call for bars, not a line. The bars make the raw post-2014 drop look alarming on purpose; the section’s whole point is that the drop is just the secular trend passing through the boundary, which is why those bar levels are read against the year-trend model in the text rather than taken at face value. This is the canonical example in this project of why “raw difference between periods” and “effect of the boundary” are different questions: the same logic the era analysis (Section 14) applies to rule changes.

29. Franchise Home Court Advantage (`run_team_hca_analysis`)

The data. Per-franchise career totals across all 43 seasons: home win %, road win %, and HCA = home% − road% (subtracting road win % controls for the franchise just being good). 39 regular-season franchises (≥50 home games) and 32 playoff franchises (≥20).

The approach. Three pieces:

Binomial confidence intervals on each franchise’s raw HCA.
A method-of-moments variance decomposition: the observed variance of HCA across franchises = true between-franchise variance + average sampling variance. Subtracting the (computable) sampling part estimates how much real spread exists.
Empirical-Bayes shrinkage: each franchise’s estimate is pulled toward the league mean in proportion to how noisy it is: weight = true_var / (true_var + sampling_var). Noisy estimates (few games) get pulled hard; precise ones barely move.

Why. Raw franchise HCA tables are leaderboard bait: small-sample franchises land at the extremes purely by luck (the Kansas City Kings’ +35.4 raw HCA rests on 82 home games). Shrinkage produces rankings you’d actually bet on, and the variance decomposition says upfront whether any real franchise differences exist before ranking them.

What the results mean. The two contexts give opposite answers. In the regular season, true between-franchise spread is real: observed SD 4.9 pp, only 30% of it sampling noise, true SD ≈ 4.1 pp. Denver (+26.8 shrunken) and Utah (+25.7) genuinely top the table, consistent with the altitude finding in Section 9. In the playoffs, sampling noise accounts for 101% of the observed spread: true between-franchise SD ≈ 0, and shrinkage collapses every franchise to the league mean (+26.9 pp). Utah’s raw +39.7 playoff HCA and the Clippers’ raw −3.6 are both indistinguishable from the same underlying value. No franchise has demonstrably special playoff home court advantage.

Why this chart. Two panels. A horizontal bar chart of franchise HCA, sorted and carrying 95% confidence whiskers, shows both the ranking and how much of it is noise: the whiskers are the visual antidote to leaderboard-reading. A reg-vs-playoff scatter with a y=x line shows whether the same franchises lead in both contexts (Section 30’s question), and the points’ error bars make the playoff cloud’s collapse to noise visible.

30. Franchise HCA Consistency (`run_hca_consistency_analysis`)

The data. The 32 franchises that appear in both tables from Section 29.

The approach. Pearson and Spearman correlations between regular-season and playoff HCA across franchises, computed on raw values and (where defined) on shrunken values: shrinkage reduces the attenuation bias that measurement noise inflicts on correlations.

Why. If home court advantage is a stable property of an arena/fanbase, the same franchises should top both lists. The two correlation flavors check robustness: Pearson for the linear relationship, Spearman for rank agreement (insensitive to outliers).

What the results mean. The raw Pearson correlation is positive and just significant (r = +0.362, p = 0.042) but Spearman is not (p = 0.128), weak evidence that regular-season home-court strength carries into the playoffs. The shrunken correlation is undefined because playoff true variance is zero (Section 29), which is itself the deeper finding: there is no reliable franchise-level playoff signal to correlate. One solid descriptive fact: playoff HCA runs about +7.2 pp higher than regular-season HCA for the same franchises: home court is worth more in the postseason on average, though the gap varies widely by franchise (SD 7.4 pp, larger than the mean itself).

Why this chart. Like Section 14, this section adds no figure of its own: its reg-vs-playoff question is exactly the scatter (with the y=x diagonal) in the Section 29 franchise chart. The correlation reported here is what the spread of those points around the diagonal amounts to numerically.

31. Win Margin Trends (`run_margin_analysis`)

The data. Home point differential per game, available from 1996–97 onward (35,536 regular-season and 2,357 playoff games), split three ways: all games, home wins only, home losses only.

The approach. Era-bucketed means for each of the three columns, plus a simple OLS trend of margin on year per column, with significance stars.

Why. Win % is a coarse summary; margins show how games are changing. The all-games column tracks the average home advantage in points. The conditional columns (wins-only, losses-only) test the “polarization” idea: are home wins getting bigger even as home wins get rarer?

What the results mean. In the regular season the average home margin shrank (−0.057 pts/yr, from ~+3.0 to ~+2.0 points) while home wins got bigger (+0.048 pts/yr) and home losses got worse (−0.095 pts/yr), all three trends significant. The playoffs show the same conditional divergence (wins +0.149 pts/yr, losses −0.101) with a flat overall margin. But conditional-on-outcome means have a built-in artifact: as the home win rate falls, games near zero margin flip from narrow wins to narrow losses, which mechanically pushes both conditional means apart. Section 32 exists to test whether the divergence is real or just that artifact.

Why this chart. Win percentage is a coarse 1/0 summary, so the margin figure plots the size of the home advantage instead: mean margin per season (how big the average advantage is), a win-only vs. loss-only panel, and era bars. Lines are the right form because the question is direction-over-time, and the two diverging win/loss lines make the polarization claim visible to the eye before Section 32 tests it formally.

32. Win Margin Polarization (`run_quantile_margin_analysis`)

The data. The same margin data as Section 31.

The approach. Quantile regression of margin on year at q = 0.10, 0.25, 0.50, 0.75, 0.90, fitting a separate trend line through each part of the margin distribution, unconditional on who won.

Why. This is the clean test of the artifact problem in Section 31. Quantiles of the full distribution don’t condition on the outcome, so they can’t be fooled by games switching sides. Two diagnostic patterns: if all five quantile slopes are parallel, the distribution is just shifting down (a pure level effect, and the Section 31 divergence is a composition artifact). If the bottom quantile falls while the top rises, the distribution is genuinely widening: polarization is real.

What the results mean. Polarization is real in both contexts. In the regular season, Q10 falls at −0.167 pts/yr while Q90 rises at +0.050 (both significant); the Q90−Q10 spread widens by +0.22 pts/yr. The playoffs widen even more (+0.33 pts/yr), driven by the top of the distribution (Q75 and Q90 rising significantly; the bottom tail, Q10 −0.104, p = 0.062, is flat). In the regular season both tails move: home blowout wins and home blowout losses are both becoming more common; in the playoffs the widening is one-sided, driven by the growing blowout wins alone. Either way it is a genuine change in the shape of game outcomes, not a bookkeeping artifact.

Why this chart. This section adds no figure of its own. The polarization it formalizes is already what the win-only/loss-only panel of the Section 31 margin chart shows to the eye: two lines pulling apart. A separate quantile-fan chart would just duplicate that picture; here the unconditional quantile slopes are what make the claim airtight, and those live in the table, not a new plot.

33. Net Rating Split by Venue (`run_net_rating_analysis`)

The data. Per-game home point differential divided by average possessions, scaled to per-100-possession terms, available from 1996–97 onward (when OREB and TOV columns became reliably available in the cached game logs). Possessions are estimated per team as FGA − OREB + TOV + 0.44 × FTA; pace is the average across both teams in the game. Games with zero estimated pace are excluded.

The approach. Season-mean net rating (home team points per 100 possessions above zero, where zero is a tie), era-bucketed means, and an OLS trend on year. Run separately for regular season and playoffs, skipping the same lockout/COVID/playoff-gap years as the rest of the analysis.

Why. Win percentage and raw point margin are the headline measures of HCA, but both are sensitive to pace. Net rating, the standard measure of team quality in basketball analytics, normalizes for pace and puts home court advantage in units (points per 100 possessions) that are directly comparable across eras. It is also the familiar metric for readers who follow mainstream NBA analytics.

What the results mean. The regular-season net rating gap is real and declining: from roughly +3.2 pts/100 in the late 1990s and 2005–17 era to about +2.0 pts/100 in recent seasons (trend −0.067 pts/100/yr, p < 0.001; overall mean +2.86). The playoff gap is substantially larger (+4.58 overall) and shows the same direction (trend −0.036 pts/100/yr) but does not reach significance on the noisier 80-game playoff seasons, consistent with the playoff decline being harder to detect in any single metric. The net rating picture agrees with the win-rate and margin stories: a real, persistent home advantage that has been narrowing for decades.

Why this chart. Net rating is displayed as the fourth panel of the margin analysis figure (a 2×2 layout alongside overall margin, wins-only margin, and losses-only margin), rather than as a standalone figure. The margin panels are the simplest evidence that the home advantage is narrowing in points; net rating adds the pace-normalized view. Grouping them together lets a reader see that the pace-adjustment barely changes the story: the absolute margin and the possessions-adjusted margin track together.

34. Multiple Comparisons: BH FDR Correction (`run_multiple_comparisons_summary`)

The problem. The report runs roughly 14 primary hypothesis tests across sections. At α = 0.05, I expect 0.7 false discoveries by chance even if every null is true. Reporting each test against its own α = 0.05 threshold is defensible when tests are pre-specified and have independent scientific rationale, but it is worth checking whether any findings are fragile.

The approach. Benjamini–Hochberg (BH) FDR correction at q = 0.05. The procedure: (1) rank the 14 p-values from smallest to largest; (2) the BH threshold for rank i is (i/14) × 0.05; (3) find the largest rank where p ≤ threshold; (4) all tests at or below that rank “survive.” BH controls the false discovery rate, the expected fraction of surviving tests that are false positives, at q = 5%. It is less conservative than Bonferroni (which controls FWER, the probability of any false positive) and is the standard choice when a small number of false positives is acceptable.

The 14 tests cover: the two overall HCA trends (RS and PO binomial GLMs); rest differential (RS and PO); altitude (RS); time zone (RS); 3PA within-era (RS and PO); pace LOO within-era (RS); travel distance (RS); parity first-differenced (RS); OREB rate vs. rebound share advantage (RS); era dummies LR test beyond year trend (RS and PO).

What the results mean. 11 of 14 tests survive BH correction: - Survive: both HCA trends, rest effect RS and PO, altitude RS, 3PA RS and PO, RS era dummies LR test (p = 0.002), travel RS, parity first-diff RS, OREB rate vs. rebound advantage RS. - Do not survive: time zone effect (p ≈ 0.05, marginal), pace LOO within-era (p ≈ 0.06), PO era dummies LR test (p ≈ 0.64).

The “ruled-out” findings remain correct descriptions of the data (the time zone and pace effects exist) but they are too small and marginal to be called reliable when multiple comparisons are accounted for. The core findings (structural decline, rest, altitude, three-point shooting) survive comfortably. Travel (p = 0.010) also survives, though the effect size is trivially small (Section 18).

Recurring Methods: Quick Reference

Logistic regression / logit: the workhorse for the binary home_win outcome. Coefficients are in log-odds; the code converts them to approximate percentage points via the marginal effect at the mean, pp ≈ coef × p̄ × (1−p̄) × 100.
Linear probability model (LPM): OLS with a 0/1 outcome, used in the mediation decomposition (Section 7) because its coefficients are additive: the only way to make channel contributions sum exactly to the HCA level and trend. Logits can’t deliver that identity.
Cluster-robust SEs (clusters = season): used whenever game-level models pool many seasons; games within a season share league conditions, violating independence.
LR (likelihood-ratio) test: compares nested logits; 2×(llf_big − llf_small) is χ² with df = added parameters. Used to test whether a block of dummies (eras, format periods, interactions) jointly earns its place.
McFadden pseudo-R²: 1 − llf/llnull. Only relative comparisons are meaningful; values look tiny compared to linear R² even for strong effects.
Two-proportion z-test: the simple raw comparison of win rates between two periods, used before trend-controlled models to show what the trend control changes.
Empirical-Bayes shrinkage + method-of-moments variance decomposition: used for any “ranking of noisy means” (franchises, referees). Decomposition asks “is there any true spread?”; shrinkage weights each estimate by its reliability before ranking.
HAC (Newey–West) SEs: autocorrelation-robust standard errors for season-level time-series OLS.
Benjamini–Hochberg (BH FDR): false-discovery-rate control when running many simultaneous hypothesis tests. Used for the 47 referee t-tests (Section 5) and the 14 primary tests in the multiple-comparisons summary (Section 34). The threshold for test at rank i (sorted by ascending p-value) is (i/m)×q, where m is the total number of tests and q is the desired FDR level (0.05 here).
ADF unit-root test (Augmented Dickey-Fuller): tests whether a time series has a unit root (I(1), nonstationary). H0: unit root; p < 0.05 means the series is stationary (I(0)). Used before any season-level correlation between two trending series to check for the spurious-regression risk.
Engle-Granger cointegration: when two series are both I(1), this test asks whether they share a genuine long-run equilibrium relationship (cointegration) or merely happen to trend in the same direction. H0: no cointegration. If both series are I(1) but not cointegrated (as found for 3PA-HCA and OREB-HCA), their Pearson r is likely spurious and within-era controls are the reliable evidence.
Granger causality: a time-series test of temporal ordering. “X Granger-causes Y” means lagged X improves forecasts of Y beyond what Y’s own lags predict. Run on first differences when series are I(1). A null result means the two series move contemporaneously; they may still be mechanically linked within the same season (as 3PA and HCA appear to be, per Section 10’s within-era game-level test).
QLR supremum Chow test: the structural-break test for an unknown break year. A Chow F-test is run at each candidate year; the maximum (supremum) F is the QLR statistic. Because I maximize over many years, Andrews (1993) asymptotic critical values are used rather than a standard F-table (k=2 parameters, 15% trimming: 10% → 7.12, 5% → 8.85, 1% → 12.37).

Limitations

What this design can and cannot establish.

Observational, not experimental. Every model runs on historical game outcomes with no randomization. The causal reading of the 1994-95 drop rests on a natural experiment (a rule change at a known date) backed by the placebo tests (Section 16) and the interrupted-time-series boundary (Section 15), not on experimental control.

Confounding is controlled, not eliminated. Game-level models adjust for team quality (quality_diff), season clustering (cluster-robust SEs), and pace endogeneity (leave-one-out expected_pace). Residual confounding from unmeasured factors is bounded by the mediation sensitivity analysis (Section 7b), which reports how strong an unmeasured confounder would have to be to overturn the result, rather than ruling one out.

Decomposition is accounting, not mechanism. The mediation and sequential decompositions (Sections 7, 23) attribute the decline to box-score channels that sum to the total by construction. They show where the decline shows up, not a proven causal pathway; the LPM is chosen precisely for that additive identity.

Trending series risk spurious correlation. Any cross-era correlation between two drifting series is checked with ADF unit-root and Engle-Granger cointegration tests, and leaned on only within-era; a raw Pearson r between trends is treated as suggestive, not evidence.

Many tests inflate false positives. With dozens of simultaneous tests, Benjamini-Hochberg FDR control (Section 34, and the 47 referee tests in Section 5) governs which survive; individual p-values are not each independently reliable.

0. The Game-Level Dataset (build_game_dataset)

1. The Overall Decline (run_decline_trend)

2. Structural Break Test (run_structural_break_test)

3. CUSUM Test: Parameter Stability (run_cusum_test)

3a. Bayesian Change-Point Model (compute_bayesian_changepoint)

4. Foul & Shooting Differentials by Era (run_differential_analysis)

5. Referee Crew Home Foul Bias: Playoffs (run_referee_analysis)

6. Shot Zone Differentials by Era (run_shot_zone_analysis)

7. Mediation: Box-Score Channels (run_mediation_analysis)

7a. Out-of-Sample Forecast (run_out_of_sample_forecast)

7b. Mediation Sensitivity to Unmeasured Confounding (run_mediation_sensitivity)

8. Rest Differential: Buckets and Era Stability (run_rest_bucket_analysis)

9. Rest, Altitude, and Time Zone (run_factor_summary)

10. League-Wide 3-Point Shooting (run_3pa_analysis)

11. Granger Causality: Does 3PA Lead HCA? (_run_granger_3pa)

12. Rebounding Decomposition (run_rebounding_decomposition)

13. Player-Tracking Rebounding Mechanism (run_tracking_rebound_analysis)

14. Rule-Change Eras (run_era_analysis)

15. Interrupted Time Series: 1994-95 Boundary (run_its_test)

16. Placebo Tests: Is 1994-95 Uniquely Significant? (run_placebo_tests)

17. Channel Event Study: Which Changed First at 1994-95? (run_channel_event_study)

18. Travel Distance (run_travel_analysis)

19. Back-to-Backs (run_b2b_analysis)

20. Pace (run_pace_analysis)

21. Competitive Balance / Parity (run_parity_correlation)

22. Arena Attendance (run_attendance_analysis)

23. What Explains the Regular-Season Decline? (run_sequential_decomposition)

24. Pre/Post-2014 Coefficient Stability (run_stability_analysis)

25. Playoff Series Structure (run_series_breakdown)

26. Playoff HCA: Seeding Quality Decomposition (run_playoff_quality_decomposition)

26a. Regular-Season Quality Split (run_regular_season_quality_split)

27. Team Quality Fixed Effects Robustness (run_team_quality_robustness)

28. Playoff Format Periods (run_format_period_analysis)

29. Franchise Home Court Advantage (run_team_hca_analysis)

30. Franchise HCA Consistency (run_hca_consistency_analysis)

31. Win Margin Trends (run_margin_analysis)

32. Win Margin Polarization (run_quantile_margin_analysis)

33. Net Rating Split by Venue (run_net_rating_analysis)

34. Multiple Comparisons: BH FDR Correction (run_multiple_comparisons_summary)