Do TV Shows Really Decline?

Decision & Deferred-Task Log

A running record of the design decisions we’ve locked in and the things we’ve consciously postponed. Update this whenever a decision is made or a deferred item is resolved, so nothing gets lost between phases.

Finalized inclusion filters

A show is included in the analysis dataset if all of the following hold:

Rule Value
titleType tvSeries or tvMiniSeries
Minimum episodes (with a rating) >= 13
Minimum seasons >= 2
Minimum mean votes per episode >= 50
Excluded genres any of Game-Show, Reality-TV, Talk-Show, News
Documentary special case Documentary-tagged is kept only if episode count < 100

Rationale, in short:

Deferred tasks (do not forget)

  1. Per-episode vote noise → handled at ANALYSIS stage, not in build. RESOLVED. Kept numVotes per episode in the processed table; episodes are weighted by sqrt(numVotes) when fitting each show’s trend slope. Full rationale and comparison of weighting schemes logged under “Phase 2 decisions” below.

  2. Ongoing shows (endYear empty) → flag, don’t drop. RESOLVED. ongoing boolean added in build. Ongoing shows are excluded from the final-season-curse analysis (data/processed/_phase2_finalseason_full.json, 2,710 ended shows only). Finding: no systematic curse — 50.5% of ended shows have a lower-than-usual final season, 49.2% higher (ten exactly level), median delta ≈ 0.00. Only 12.6% show a clear curse (final season ≥0.5 points below the rest), and those are disproportionately well-known flops (House of Cards -4.24, Game of Thrones -2.55, Master of None -2.54) — likely why the “final season curse” feels universal (availability bias) even though it isn’t the norm. Correlation between this delta and the overall trend slope is +0.80 — related but not the same metric, confirming they answer different questions (see “Overall trend slope is NOT a valid proxy…” below).

  3. Episode-level air-year precision (optional refinement). For a more precise “still active” signal we could pull each show’s latest episode air year from the tvEpisode rows in title.basics (currently unused; we only use the tvSeries rows). Deferred; only do it if the endYear proxy proves insufficient.

  4. Shows with missing genres — RESOLVED. Verified in phase0_final_filter_check.py: 0 shows in the final set have missing genres, so this edge case does not occur. No action needed.

  5. Very-long-running shows kept, handled at analysis stage. RESOLVED. Extreme outliers (Pokémon 1234 ep / 25 seasons, Detective Conan 1211 / 54, The Simpsons 806 / 37, etc.) stay in the dataset; they were NOT capped in build. As planned, Phase 2 normalizes every trajectory to a 0-1 episode axis so length can’t distort the fit, reports medians alongside means throughout, and analyses length explicitly as its own factor (see the cross-sectional section) rather than treating long shows as contamination. 485 shows have >100 episodes, 127 have >200.

  6. Non-narrative formats leaking through the genre filter — STILL OPEN, consciously not fixed. Some sketch/variety/web-review shows tagged only as Comedy/Music (not Talk-Show/Reality-TV) survive the genre exclusions — notably Saturday Night Live (1010 ep) and The Nostalgia Critic (935 ep). Phase 2 decision: no manual blacklist was added. A hand-curated exclusion list is a judgement call that would be hard to justify or reproduce, and the affected shows are few enough not to move any headline figure. Instead this is disclosed as a stated limitation in the report. Revisit only if a future analysis turns out to be sensitive to them.

  7. How ratings age over time — OUT OF SCOPE here, worth its own project. Every rating in this dataset is a present-day snapshot, not a contemporaneous reaction. IMDb’s public dumps carry one row per title with today’s average and today’s vote count — no timestamps, no history. A show that ran 2004-2010 is being scored in 2026, largely by people who watched it later and already knew how it ended.

    Considered and rejected: scraping Wayback Machine snapshots of IMDb pages to reconstruct a year-by-year series. Technically possible, but

    • one show’s finale would be an anecdote, and this project’s whole standard is that we don’t argue from anecdotes; a real sample means thousands of archived-page fetches across ~5 different IMDb layouts since 2010;
    • Wayback covers famous episode pages far better than obscure ones, so the achievable sample leans toward well-known shows — the exact availability bias this report is about, which would make any conclusion self-refuting;
    • it introduces a second, non-reproducible data provenance beside the official dumps that src/build.py rebuilds from scratch;
    • and even with perfect historical data, a rating that rose from 2010 to 2026 cannot separate “people changed their minds” from “a different set of people voted.” That needs per-voter data, which does not exist publicly.

    What this changes in the current report: prose must say a finale is rated X today, never was rated X at the time — we do not know the latter. That rule is applied (see §9’s Lost closing).

    Deliberately NOT added to the report’s limitations section. Decision: the whole subject stays parked as a separate future project rather than becoming a fourth caveat in §8. The three caveats there are about what the ratings can’t tell us; this one is about what a different dataset could tell us, which is a different piece of work.

    If it is ever picked up, the cheap first step is an in-data proxy: does the finale premium grow with how long ago a show ended? Confounded with era effects, but computable from what we already have. Not run.

Phase 2 decisions

Per-show trend slope: weighting scheme

To measure whether a show “declines”, each show’s episodes are fit with a weighted least-squares trend line: average_rating ~ normalized_episode_order (episode order scaled 0-1 within the show). The slope of that line is the show’s decline/rise metric.

Episodes are weighted by sqrt(num_votes), not raw num_votes and not unweighted.

Rationale:

Overall trend slope is NOT a valid proxy for “final season curse”

Verified on Game of Thrones: season 8’s true mean rating is 6.40 (6 episodes), vs 8.95 for seasons 1-7 (67 episodes). But the fitted trend line’s value in the season-8 x-range is 7.6-8.3 depending on weighting scheme — all well above the true 6.40.

Cause: a straight line minimizes total squared error across all episodes. When ~92% of a show’s episodes sit at a consistently high rating and only the last few crash, the line stays anchored near the majority and understates the size of a late, sharp drop — a single linear slope cannot represent “flat-then-cliff” as accurately as “steady decline”.

Consequence: the per-show slope answers “does this show decline at a roughly constant rate overall” — a different question from “did the final season specifically tank”. The final-season-curse analysis (deferred item 2 above) must use a direct comparison instead: final_season_mean - rest_of_show_mean (ended shows only), not the overall slope.

Final-season-curse threshold: headline -0.5, plus a robustness check

The “clear curse” cutoff of delta <= -0.5 rating points is an intuitive, lay-readable choice (a half-point drop is human-perceptible), not a statistically-derived one. Decision: keep -0.5 as the headline number (it’s in the same units readers care about) but always report it alongside a robustness check so the conclusion doesn’t hinge on an arbitrary cutoff:

Slope vs final-season-delta: correlated (+0.80) but not redundant

The overall slope and the final-season delta correlate +0.80 (r^2 ~ 0.64), so ~36% of the variation is independent — they answer different questions. Concretely: “gradual decliners” exist (steep negative slope, delta ~0 — e.g. The Walking Dead slope -1.19 / delta -0.23; Fargo -1.27 / -0.12), but the pure “flat overall, only the finale crashes” case is essentially absent — all 32 big final-season crashers (delta <= -1.0, >=30k votes) also have a negative slope (least-negative is Scrubs at -0.57). Reason is mechanical: a final season sits at the end of the x-axis, so a late crash necessarily tilts the fitted line down. (Corrects an earlier loose description of Game of Thrones as “flat then cliff” — its slope is clearly negative too.)

Trajectory shape (C): peak location, curvature, volatility

Three shape measures beyond the single linear slope, all using sqrt(num_votes) weighting where a fit is involved.

1. Peak-season location — reported as “mid-run, scaling with length”, NOT “season 2”. An initial cut on 3-season shows alone made season 2 look like the modal best season (“sophomore surge”). That was an aggregation artifact: the dataset is dominated by short shows (1,101 two-season, 780 three-season), and in a short show the middle is season 2. Stratifying by season count shows the peak’s ABSOLUTE season number grows with length (mean best season: 1.6 at 2 seasons, 2.5 at 4, 3.1 at 5, 3.8 at 7, 5.8 at 8+) while its NORMALIZED position stays near the middle (~0.46-0.59 across all lengths). So the peak is emphatically not “season 2” — where it lands scales with how long the show runs. Phrase the positive claim carefully, per the caveat below.

2. Curvature (“jumped the shark”) — a per-show weighted quadratic fit (rating ~ a + b*x + c*x^2, x = normalized 0-1 episode order). A show is labelled by the sign of c when the parabola’s vertex is interior (0.15 <= vertex <= 0.85) and |c| > 0.05: c<0 = “jumped the shark” (rises then falls, peak in the middle), c>0 = “found itself” (dips then recovers), otherwise “linear/flat”. Result over 3,234 shows: 44.6% jumped-the-shark, 35.2% linear/flat, 20.3% found-itself. The peak-then-fall shape is the single most common trajectory. Clearest jumped-the-shark cases (>=20k votes): Top Gear, House of Cards, Game of Thrones, Master of None (vertices ~0.30-0.42). Clearest found-itself: SpongeBob SquarePants, Star Trek: Picard, Spy x Family.

3. Volatility — weighted RMSE of the linear fit’s residuals (how bumpy a show is around its own trend). Median 0.35 rating points. Most volatile (>=20k votes): Thomas & Friends (1.70), One Punch Man (1.54), Top Gear (1.40), House of Cards (1.22), Game of Thrones (1.10) — long-running animation plus hard-finale-crash shows. Most consistent: Shahmaran (0.09), Warrior Nun (0.10), Kim’s Convenience (0.19) — mostly short, even shows.

Cross-sectional cuts (A): era, length, genre — with confound controls

Raw cuts on the sqrt(votes)-weighted slope all look striking but are heavily confounded (newer shows are shorter and more often ongoing; the composition table: median seasons 5 in the 1950s -> 2 in the 2020s, ongoing 3% -> 41%). Disentangled results:

Regression to the mean, done properly — the “high shows decline” effect is TINY

The earlier -0.373 correlation (slope vs its own fitted intercept) is inflated by mathematical coupling (shared noise). Clean test: split each show’s episodes into disjoint first/second halves.

Popularity: the belief describes the famous shows better than the average one

Added after the report was finished, because a review pass asked a question the analysis had never cut on: the headline is a claim about the average show, but nobody forms the decline belief from the average show. §4 of the essay already answered this with availability bias, flagged there as interpretation rather than measurement. phase2_popularity.py checks whether it is measurable.

Cutting the same sqrt(votes)-weighted slope by a series’ total votes gives a monotone gradient:

Tier n Clear decline Median slope
under 5k votes 1,184 14.8% +0.224
5k - 50k 1,545 15.1% +0.078
50k - 500k 445 24.7% -0.041
over 500k (household names) 60 43.3% -0.392

The top tier declines at roughly three times the 16.9% base rate. Three checks were run to try to make that go away, and none did:

The caveat that must travel with this, and the reason it stays out of the headline: vote count is endogenous. This project documented the mechanism itself while choosing a weighting scheme — a final-season backlash inflates vote counts, which is why four of Game of Thrones’ six most-voted episodes are season-8 ones. Decline raises votes as surely as votes track decline, so the arrow cannot be pointed and no causal claim is available here. What survives is descriptive: the series the belief is drawn from do not behave like the typical series, and “about one in six” is not a statement about them.

Now reflected everywhere — RESOLVED. It was deliberately logged here first: §4’s availability-bias paragraph was hedged as interpretation, this result lets it be stated as measurement, and that is a prose decision about the strongest section of the essay which should not be made in the same pass that produced the number. A later pass made it, and it went further than the essay:

A second cut was added for §4.4’s sake. Parts 1-4 of phase2_popularity.py measure the SLOPE, and this log already establishes that the slope is not a proxy for the final-season question. §4.4’s fame claim is about the final-season delta, so it could not borrow those numbers and needed its own cut (part 5): 11.6% / 12.5% / 14.4% / 23.8% clearly cursed across the four tiers, median delta +0.063 → -0.209, against a 12.6% base rate. Monotone, same direction.

Wilson intervals on both tables, because the top tier is small by construction — 60 series by slope, 42 by delta. They changed the wording: the slope gradient is sharp (43.3%, CI 31.6-55.9, not overlapping the least-watched tier’s 12.9-16.9) while the delta gradient is suggestive but weakly powered (23.8%, CI 13.5-38.5, lower bound barely clearing the 12.6% base rate). §4.4 now says it is the weaker of the two instead of presenting them as equal evidence.

Sixteen genre tests at once: Biography did not survive the correction

The genre model screens 16 non-exclusive genre dummies in one regression and the first version reported significance per coefficient at |t| > 2. At α = 0.05, 16 simultaneous tests are expected to produce about 0.8 false flags — so “six genres reach significance” could not be reported as six findings, and the weakest names on the list are exactly where the expected false positive lands.

phase2_rtm_genre.py now computes two-sided p-values (normal tail via erfc; with 3,214 residual df the t-distribution is indistinguishable from the normal, so this avoids a scipy dependency) and applies both corrections over the genre family only. Era, length and ongoing status are pre-specified single hypotheses and are deliberately NOT members of the family.

Screen Threshold Genres surviving
Raw α = 0.05, |t| > 1.96 6
Benjamini-Hochberg reject p <= 0.0129 5 (adds Documentary, Romance, Thriller)
Bonferroni α = 0.0031, |t| > 2.96 2 — Animation, Adventure

What this changed in the prose. Biography (-0.244, t = -2.25, and only 53 series) was named in the essay, the technical report and the outline as a genre that genuinely declines. It clears the raw 5% bar and neither correction. It is now dropped from all three, and the essay’s genre sentence says so explicitly rather than quietly omitting it — a reader who saw an earlier draft deserves to know the claim was withdrawn, not lost.

Two smaller consequences worth recording:

References added for the methods now used: Benjamini-Hochberg (1995), Wilson (1927) for the score intervals in the popularity tables, and Efron-Morris (1975) for the shrinkage in §5.6.

Estimation error in the headline split

The headline sorts every series into bands cut at ±0.5, but each slope is an estimate, and nothing had checked what that costs. phase2_slope_precision.py does. Two results, both reported because either alone misleads:

  1. A per-series label is soft. Median slope SE 0.189 against a band half-width of 0.5. Of 545 “clear decline” series, 285 (52%) have a 95% CI still touching -0.5; only 55% of series have a slope distinguishable from zero. The bands are a reporting convention over a continuous quantity, so no claim is made about an individual series from its band.
  2. The population split is barely distorted. Variances add, so observed 0.6049 = real 0.5434 + error 0.0614: a tenth of the spread is noise. Noise inflates the apparent decline share by about a point. Detail in technical report §5.6.

The script asserts its refitted slopes match _phase2_slopes_full.json to 1e-9 before computing anything, so it cannot measure the precision of a different fit than the one published.

The first version of that correction was wrong, and it is the same mistake a third time

Worth recording at length because the pattern is now established. The first draft of §5.6 corrected the split with empirical-Bayes shrinkage and reported 15.2 / 61.3 / 23.5. An external review pass challenged it and the challenge held up on re-derivation.

The error: posterior means are over-shrunk as a set by design. Their variance here is 0.4238 against a true between-series variance of 0.5434 — 22% too narrow. Counting how many fall past a fixed cut therefore understates both tails mechanically, whatever the data. Shrinkage is the right tool for estimating each series’ slope and the wrong tool for estimating the distribution of slopes.

This is the third instance in this project of an estimator quietly answering a different question than the one asked:

The lesson generalises better than any of the three fixes: when a number is computed for one purpose and reused for another, re-derive what it estimates.

A second trap was found while fixing the first, and is recorded because it points the opposite way. Reading the same normal model parametrically — true slopes ~ N(0.073, 0.543) — gives 21.9% decline, i.e. higher than the published 16.9%. Two estimators, one assumption, opposite signs. That model is rejected outright: it predicts an observed share of 23.1% against the 16.9% we see, so it cannot reproduce the data it is fitted to. The slopes are skewed (-0.64) and fat-tailed (excess kurtosis +5.60; 0.53% beyond 4 SD against 0.006% expected). Normality was not a harmless technicality here — it determined the sign.

What replaced it. A scale-family deconvolution: solve for the scale c at which the expected share of noisy estimates past the cut, mean(Phi((cut - t_i)/se_i)), equals the observed share. c = 0.927, corrected split 15.6 / 60.4 / 23.9. It assumes normal estimation error (already assumed by every SE in the report) but nothing about the shape of the true slopes beyond scaling. Deliberately deterministic — no simulation, no seed — because a published number in this project must be reproducible exactly. It is fitted on the decline share alone and predicts the rise share at 25.0% against 25.7% observed, which is a real out-of-sample check.

And the claim was narrowed. Only the DIRECTION is now asserted, because only the direction is assumption-free: noise smooths a density peaked inside the middle band, and the middle is the only class with two edges to lose mass across. Demonstrable without any deconvolution — feeding the estimates back as if they were the truth predicts 18.1% observed decline against the 16.9% seen. The magnitude (~1 point) carries a shape assumption and is stated as such.

Two pieces of overclaiming were removed at the same time. The report had said the error “was working against it, not for it”, and the essay had said “Every number in this piece is the version that flatters our conclusion least” — a sentence that invites exactly the audit that then failed it. The essay paragraph was also the fourth copy of the same content (script docstring, decisions log, report §5.6, essay) and is now two sentences, which is what it was worth.

Phase 3 decisions (figures)

Colour is computed, not eyeballed

Figure colours come from a validated categorical palette rather than matplotlib’s defaults. The checks (lightness band, chroma floor, Machado-2009 protan/deutan colour-blind separation, normal-vision floor, WCAG contrast against the chart surface) were run rather than reasoned about — the reference checker is a Node script and Node isn’t installed here, so it was ported to Python and confirmed against the reference palette’s published numbers (worst adjacent CVD ΔE 9.1, normal-vision 19.6) before being trusted.

Results for what the report actually uses:

Two conscious deviations, both allowed by the palette’s own rules and recorded in notebooks/figstyle.py: the aqua slot sits at 2.74:1 contrast (below 3:1), so every aqua mark carries a visible direct label; and grey is used as a de-emphasis ink (the flat middle of a diverging scale, insignificant coefficients), which fails the categorical chroma floor by construction because it is not a series colour.

A real defect the check caught: orange and red cannot share a figure. #eb6834 and #e34948 separate by only ΔE 5.6 under simulated deutan vision (floor 6.0) and — worse — ΔE 7.1 under normal vision against a floor of 15. Full-colour readers cannot reliably tell them apart either. The first version of fig02 used both (orange fitted line, red/blue quartile bars). Fixed by making the quartile bars a single colour, which is independently the right call: the quartiles are nominal categories and the sign is already carried by the bar’s direction and its signed label. Every other pair in use clears both floors. The rule is now written into figstyle.py so it is not re-broken.

Roles, assigned so that orange and red never meet:

Colour Role
blue #2a78d6 data points / single series, and the “rise” pole
red #e34948 the “decline” pole — only in figures with no orange
orange #eb6834 the fitted trend the analysis actually uses (fig02, fig08, fig09)
aqua #1baf7a a rejected alternative or third class — always directly labelled
grey #898781 de-emphasis: reference lines, the flat middle, insignificant estimates

Consistency this buys: the sqrt-weighted trend line is orange in every figure it appears in. An earlier version drew that same estimator orange in fig08 but blue in fig09, which would have made the two figures hard to read together.

Dark mode — DONE

Built as a third render mode, --dark, alongside --paper. Nine dark plates in figures/dark/, and every markdown image is now a <picture> that serves them to readers whose browser reports a dark preference:

<picture>
  <source media="(prefers-color-scheme: dark)"
          srcset="../figures/dark/fig01_slope_distribution.png">
  <img alt="…" src="../figures/fig01_slope_distribution.png">
</picture>

The point worth recording, because it is the question that stalls people: we never choose the theme. The reader’s own setting does, through the browser’s prefers-color-scheme. Both files ship; each visitor’s browser picks one. The <img> keeps the light file so anything that does not understand <picture> still shows a figure.

Scope is narrower than it first looks. The dark set covers the essay and the README only. The technical report is a PDF, which has no theme, so the paper plates stay light — and figstyle enforces that: --dark is ignored when --paper is passed.

One implementation note. The palette flag is read at import time rather than inside apply_style(), because phase3_figures.py binds the colours with from figstyle import BLUE, … before any function runs. Setting them later would leave the imported names pointing at the light values.

This decision was originally recorded as deferred, with the reasoning below. The deferral held until the essay’s own home was settled; the dark palette had already been validated at that point, so the work was only ever a flag away.

Why it was deferred first

The figures are drawn on a light surface (#fcfcfb). Both primary deliverables are documents (the essay and an arXiv-style technical report), where light is the convention, so this is right for the deliverable. The open question is GitHub: the repo is public, most people browse it in dark mode, and a light-background figure reads as a bright block there.

Decision: keep light only for now, revisit at packaging. It is an aesthetic mismatch, not a functional one — the figures stay perfectly legible on a dark page because they are opaque. (Transparent backgrounds are the case that actually breaks, since dark text lands on a dark page; savefig.facecolor in figstyle.py is what keeps us out of that.) Figures will keep changing through the prose passes, and maintaining two sets now would double that churn for a surface that is not the deliverable.

The deferral was de-risked by validating the dark palette up front, so this cannot fail later:

When it is done: add a theme parameter to figstyle.py (all colours already route through it, so this is one switch plus a re-run), write the dark set to figures/dark/, and reference both from GitHub-facing markdown with a <picture> element keyed on prefers-color-scheme.

Uniform figure width

All nine figures are drawn at the same width (12 in / 2400 px), varying only in height. Widths previously ranged from 9.5 to 13.5 in; since every figure is scaled to the same column in the report, that made identical 9.5pt labels render visibly larger in some figures than others. Same width = same apparent text size throughout.

Two silent clipping bugs, found by checking every hard-coded axis limit

Manually set axis limits hide anything outside them. Checked all of them against the data they must contain:

Both were invisible in the rendered image — the figure looked fine, which is exactly why the limits had to be checked against the data rather than by eye.

Shape classification audited (fig06) — it holds up

The jumped_the_shark / found_itself / linear/flat split was re-derived from episodes.parquet and checked against the stored _phase2_shape_full.json: 0 label mismatches across all 3,234 shows, max curvature difference 5e-11. The file and the code agree.

Three things the audit settled:

  1. The label “climbs, then falls” is earned. Within the jumped_the_shark class the vertex (the peak) sits at a median of 0.50 of the run; only 6.2% peak in the first 0.15-0.25 stretch, while 41.9% peak in the middle fifth. The class is not “declines from the start” wearing an arc’s name. Median rise to the peak is 0.37 rating points and median fall from it 0.33 — a real but small arc, which is what licenses the “it is gentle” headline. (13.6% climb by less than 0.1 points, so a minority barely rise at all.)
  2. The +/-0.05 curvature cut-off does almost no work. Shares are 44.6 / 35.1 / 20.3 at a threshold of 0, and 43.7 / 36.6 / 19.8 even at 0.20. The binding condition is whether the vertex falls inside the run, not the curvature size — so the result is not an artifact of an arbitrary cut.
  3. “linear/flat” was a misleading name and the figure no longer uses it. The class means “no turning point inside the run”, i.e. monotone over the show’s own length — it includes steep straight-line decliners (The Walking Dead, slope -1.19) and steep risers alike. The figure now labels it “Straight line (no turn mid-run)” and states that the class holds both directions, so its average arc is a net of the two.

fig06 also now carries the found_itself caveat that was already logged above (about a fifth of those recoveries rest on thinly-voted late episodes), which the first version of the figure omitted.

fig08 reframed: direction, not curvature class

fig08 originally showed one show per curvature class (∩ / straight / ∪). That framing kept producing trios where two of the three declined, which required a “not a representative sample” disclaimer to stop the figure contradicting the report’s own headline. A disclaimer that has to argue with its own figure is a sign the figure is wrong, not the reader.

Reframed to direction, matching the three groups fig01 already establishes — clearly declining, essentially flat, clearly rising. Now the figure illustrates the headline instead of fighting it, and no disclaimer is needed:

Show Group Slope Votes
Stranger Things (2016-2025) clearly declining -0.87 2.6M
Friends (1994-2004) essentially flat +0.12 1.4M
Breaking Bad (2008-2013) clearly rising +0.99 4.5M

They also span 1994-2025 and 42-234 episodes, which incidentally shows the method working across eras and very different show lengths.

Rejected along the way: The Office (US), the outline’s original pick, classifies as jumped_the_shark (slope -0.64) — the same class as Game of Thrones, so the panel label would have contradicted the data. M*A*S*H was genuinely flat but too old and US-centric to pull a reader in. The Walking Dead is a vivid straight-line decliner but made the trio two-thirds declining. Game of Thrones is deliberately not reused here because it already anchors fig09.

Figure numbers are recomputed, not transcribed

Every figure recomputes its inputs from data/processed/ and prints the values it annotates. All nine reproduce the Phase 2 findings exactly — GoT sqrt slope -1.55 and the -2.21 / -1.55 / -1.02 weighting spread, OLS -0.0261 (t = -6.8), peak-season means 1.6 / 2.5 / 3.1 / 3.8 / 5.8, the threshold sweep 29.2 / 22.4 / 12.6 / 6.8 / 3.7 — so the plots and the prose cannot drift apart.

Incidental confirmation: §2’s “57.4% rise” and “57.4% essentially flat” are two genuinely different quantities that round to the same number. It looks like a copy-paste error in the outline and is not one.

Phase 3b decisions (prose ↔ figure pass)

Figures go where their numbers are, not at the end of a section

Two figures had been parked after their section’s closing line, which deflated the closing. Rule adopted: a figure follows the paragraph that states its numbers; a section’s last line is its last line. §6 was re-ordered for the same reason — the two myths were swapped so each figure sits beside the claim it supports, which also gave the section a better progression (shape → where the peak is → which season wins).

The inclusion criteria were missing from the essay entirely

§8 referred to “our filters” and no earlier section had ever described them — the reader was told what leaked through a net they’d never been shown. §7 now opens with What counts as a show (the joins, ≥13 episodes, ≥2 seasons, ≥50 mean votes, genre exclusions, and the resulting 3,234 / 192,720). This was in the outline’s plan for §7 and had simply never been drafted.

House of Cards restored to §8

The outline deliberately held House of Cards back from the §1 hook — its −4.24 crash is a lead actor written out amid scandal, not a show losing its way — and assigned it to §8 as the flagship off-screen-shock example. The draft had dropped it, so §8 was making its argument without its strongest case. Restored, with the season-length detail verified against the data (final season cut from 13 episodes to 8; season mean 4.19 against ~8.4 for seasons 1–5).

Claims about named shows are verified, not remembered

Every named-show claim in the essay was re-checked against the parquet rather than trusted: the finale flops and saves, HIMYM’s 7.56 → 5.5, GoT’s 6.40 vs 8.95, Scrubs’ season 9 at 6.21 against ~8.1, SNL’s 1,010 episodes. All held. Two claims did not survive contact and were changed:

Typography and terminology match the prose

Figure text now uses real em dashes rather than --, so figures and prose look like one document. Jargon that had leaked into figure labels was replaced with the words the essay itself uses: r = +0.79 → “correlation +0.79”, By sqrt(votes) → “By the square root of votes”. A |t| threshold stays in fig05’s footnote because a plain-language gloss sits right beside it. (That footnote now names two thresholds, one per panel — see the multiplicity decision above.)

Phase 3c decisions (the technical report’s own figure set)

Why the essay figures could not be reused in the paper

Compiling the report and looking at the pages — rather than at the source — exposed four faults that all had one cause: the figures were designed as standalone editorial graphics.

  1. Labels were unreadable. Drawn on a 12-inch canvas and scaled into a 6.4-inch column, a 9 pt axis label arrives at 4.8 pt and an 8 pt footnote at 4.2 pt, against 11 pt body text. Below roughly 6 pt, print stops being readable.
  2. Every figure had two titles. The in-image headline plus the LaTeX caption underneath. Papers give that job to the caption alone.
  3. A figure referred to itself. The in-image footnote of the example-trajectories plate says “the three groups in Figure 1” — true in the essay, where that figure is number 8, and wrong in the report, where it is Figure 1. Baked-in cross-references cannot survive renumbering.
  4. The off-white surface (#fcfcfb) read as a grey pasted-in block against the page.

One script, two rendering modes

Resolved with a --paper switch on notebooks/phase3_figures.py rather than a second set of figures. The data, the fits and every printed number are shared; only presentation branches:

This is deliberately not the dual-maintenance pattern rejected for the dark-mode figures and the duplicated documents: there is one source of truth, and the two outputs cannot disagree about a number. Verified after the change — the essay figures are byte-identical, so the paper branch cannot silently alter them.

What the paper plates drop, the captions must carry. Removing the in-image footnotes would have deleted the axis-clipping disclosures and the sample sizes. Those were moved into the LaTeX captions rather than lost: Figure 3 states that 18 series fall outside its clipped axis, Figure 6 that 6 do, Figure 9 that the middle panel is restricted to the 915 series with at least five seasons.

Layout fixes the rendered PDF exposed

The compiled PDF is committed — and can go stale

docs/technical_report.pdf is in the repository rather than left as a build artifact. The usual rule against committing build output assumes something that changes often and is cheap to rebuild; this is neither. The report is finished, and there is no LaTeX toolchain on this machine, so rebuilding means an Overleaf round trip. Without the PDF the technical report is effectively invisible: a visitor has no way to read .tex, while GitHub renders a PDF in the browser.

The rule that comes with it: if technical_report.tex changes, the PDF must be recompiled and re-committed in the same change. A stale PDF is worse than no PDF, because it looks authoritative while being wrong. This project has already hit that failure twice during drafting, when an older .tex was compiled by mistake and the mismatch had to be caught by diffing the output against the source. Do not commit intermediate compiles — only when the source meaningfully changes.

Tests: the conventions this project relied on, made enforceable

Added at the end, which is late, and the lateness is the point worth recording.

The README claims a figure “cannot quietly drift away from the numbers in the text”, because every figure recomputes its own inputs and prints them. That was true, and it was still only a habit — nothing checked it. The same held for the palette rule in figstyle.py (“HARD RULE: ORANGE and RED must never appear in the same figure”), which is a comment, and which the first version of fig02 broke anyway. Habits and comments do not survive a change made six months later by someone who did not write them.

Three files under tests/, runnable with pytest from the repository root:

Tests run against the committed data/processed/, so a fresh clone can verify every published number without downloading the 274 MB of raw IMDb dumps. pytest is in requirements-dev.txt, not requirements.txt — the latter stays the minimum needed to run the analysis.

What the first run caught: the final-season split was 49.4%, and it is 49.2%

phase2_finalseason.py counted the risers as len(res) - declining instead of counting them, which folds the six ended series whose final season lands exactly level with the rest of their run into the “stronger” column. So the published pair did sum to 100 — by absorbing the ties.

Corrected at the time to 50.6% / 49.2% / six level. The 12.6% clear-curse share was and is untouched.

That correction was itself incomplete, twice over, and both parts were found by reading the compiled PDF rather than the source.

First: this entry claimed “no figure plotted the number”, and that was false. fig04’s left-panel title read “Almost a coin flip: 50.6% down, 49.4% up” directly above prose saying 49.2%. The figure had written 100 - pct_down independently, so fixing the script never touched it. Grepping for the value could not have caught it either — the figure computed the number rather than containing it.

Second, and larger: “six exactly level” was wrong too, and so was the 8 that the figure’s data file reported. A tie means two means of one-decimal ratings are equal as rationals, which float arithmetic often cannot represent: four such series land on ±1e-15 rather than 0.0. So delta == 0 counted 6; pandas to_json then rounded a different subset to zero at its default 10 decimals, so anything reading _phase2_finalseason_full.json saw 8; and the true count at the data’s own precision is 10. Three answers to one question, all artifacts of how zero was compared. Both scripts now use an explicit 1e-9 tolerance, and the published pair moves to 50.5% / 49.2% / ten level.

Three lessons, in increasing order of how much they generalise:

It is worth being clear about how small this is, and about why it was still worth chasing. A handful of series in 2,710, a couple of tenths of a percentage point, and no conclusion depends on it. But §7 of the essay makes an argument about exactly this class of mistake — “headline findings get scrutinised; it’s the confident little sentences around them where mistakes survive” — and the error was a derived-instead-of-counted share sitting one line away from a headline. The essay had already been through a verification pass over its named-show claims; this number was never in that pass because it did not look like a claim. That is the case for tests over care: care is what checks the things that look like they need checking.

The headline’s gloss was wrong: “fewer than one in six” is above one in six

Found while preparing the repository for a wider audience, which is the first time anyone asked what the front page’s first sentence actually asserts.

The clear-decline share is 16.9%, and every document glossed it as “fewer than one in six”. One sixth is 16.67%. The share is 545 shows out of 3,234 against a one-in-six mark of 539 — six shows above the fraction it claimed to be below. Corrected to “about one in six” in the README, the essay (twice — the claim and the later self-quote), the technical report in both formats, and this log.

The number was never wrong. Nothing recomputes, no figure changes, no conclusion moves. What was wrong was the sentence that carries the number when the number is not present — and that sentence had the widest distribution of anything in the project: the README’s first screen, the repository description, and the text of every link preview the essay would ever generate.

Two things this says that the earlier corrections did not:

test_the_headline_gloss_is_about_one_in_six_not_fewer now checks the count against n/6 and greps the five published documents for the old phrasing. If a filter or threshold ever moves the share back under one sixth, the test fails and the wording gets revisited on purpose rather than being right by accident.

Language convention

All code, comments, function/variable names, filenames and figure labels are in English. Turkish is used only for discussion and (optionally) the final blog narrative.