Screen character names and US baby-name popularity, 1986–2025: a preregistered event study with matched control names

Summary

Strengths

1. Unfavourable pre-trend diagnostics are reported up front

   Abstract; Sec. 3.4; Sec. 4.1; Fig. 1a,b; Table 3 (R8, R13)

   Leads at $k=-6..-4$ are held out of matching and used as a diagnostic. The paper adds a fake-date benchmark (release date −8 years) and a long-trend matching variant (R13). It then puts the bad news in the abstract: leads ≈0.10 and a fake-date mean of 0.121. Many event studies in this area show only post-release curves. Here the reader is told directly that part of the raw gap predates release.

2. Departures and post hoc analyses are labelled in the tables

   Sec. 3.8; Tables 2 and 4; Abstract

   Sec. 3.8 lists the R13 addition and the three post hoc analyses P1–P3 with their motivation. P-rows carry an asterisk in Tables 2 and 4, and the abstract labels the P2 release-window estimate and the 81-name count as post hoc. This makes the confirmatory/exploratory boundary auditable, even though some summary sentences later blur it (weakness 3).

3. Reported numbers are internally consistent and reproduce from what is printed

   Fig. 1; Tables 1–5; Sec. 4.4; Sec. 4.7

   Digitising Fig. 1 reproduced all 12 quoted coefficients within 0.002 (check 05). Refitting the decay model to the digitised curve gives $\lambda=-0.1147$ vs the reported −0.115 (check 07). The state meta-analysis (FE mean, Q, p, $I^2$, $\tau^2$, $\sum n = 9{,}146$) recomputes from Table 5 (check 12), and so do all ten genre BH q-values (check 13). 31 of 32 count identities hold (check 10), and p-values agree with their bootstrap CIs (check 14). Nothing suggests fabricated or transcribed-wrong numbers.

4. Systematic sampling and careful matching

   Sec. 3.2–3.5

   Titles are drawn by a fixed rule (top 40 films and top 20 series per year), not hand-picked famous cases, so the much-cited Madison/Arya anecdotes are not selected on the outcome. Controls are matched by Mahalanobis distance on level and trend, with phonetic/spelling neighbours excluded and standardized balance of 0.013 (level) and 0.002 (trend). Inference uses a title-clustered bootstrap with BH correction within families.

5. Null and negative results are reported straight

   Table 1; Sec. 4.3–4.6

   The preregistered timing hypothesis (H4: peak in $k=1..3$; share of replicates 0.002), the decay hypothesis (H5, $\lambda<0$, p = 1), the sex, format and adaptation contrasts (H7–H9) and the failed 'made popular' rule are all reported as unsupported, not reframed. The contrast with the qualitative 'tsunami curve' literature [4, 11] is stated plainly.

6. Broad robustness battery

   Table 3; Fig. 3; Sec. 4.3; Table 2

   Thirteen specifications (R1–R13) are all positive, ranging from 0.153 (R7) to 0.301 (R10). Six stay within 0.005 of the primary estimate. Excess births are given with bootstrap intervals and their concentration across titles (median 33, mean 410 per title; 354,276/864 = 410.0 checks).

7. Accurate positioning against prior evidence

   Sec. 2.1–2.3; Sec. 5.2

   The figures attributed to Disdier et al. [9] check out against the source: about 10% at mean name age, 62% for new names, no effect beyond about 31 years, and 180/927/4,845 titles (check 18). The summary of the staggered-DiD literature [27–33] is correct in broad strokes. The industry figure of 98% [17] is rightly presented as an uncontrolled upper benchmark.

Weaknesses

1. 'About half reflects trajectories' rests on a post hoc estimator with an unstated assumption and is metric-dependent

   major · Abstract (last sentence); Sec. 1; Sec. 3.8; Sec. 4.1–4.2; Sec. 5.1; Sec. 5.5; Table 2 (P2 rows); Table 3 (R10, R13); Table 4 (P2)

   The closing sentence of the abstract, the contribution paragraph of Sec. 1 and Sec. 5.5 all state that about half of the raw gain reflects pre-existing trajectories. The basis is P2, a post hoc true-minus-fake-date difference (0.096 vs 0.180). Three problems follow.

   (i) The fraction is not robust to the metric. It is 0.47–0.56 on the unweighted log scale, but in the paper's own birth counts the fake-date excess is 14,170 against 240,444 at true dates, about 6% (Table 2). In names above chance it is about 12% (check 02).

   (ii) The paper's other pre-trend benchmarks point the other way. The leads show treated names falling relative to controls toward release (0.171, 0.111, 0.076). Linear de-trending (R10) raises the estimate to 0.301, and our extrapolation of the quoted leads reproduces 0.31–0.35 (check 03). R13 raises it to 0.197. The paper adopts the fake-date benchmark without arguing why it beats these.

   (iii) P2 is conservative only if selection bias at the fake date equals selection bias at the true date. The paper never states this assumption. In an illustrative simulation with zero true effect, P2 is biased in either direction depending on how writers pick names (check 04). Digitising Fig. 1b also shows the fake-date curve accelerating from 0.059/yr to 0.101/yr exactly at the true release years (check 05), so the difference mixes a long trend with a release-time kink.

   Fix: state the identifying assumption; report the share on all metrics; reconcile with R10/R13 or report a bracket (e.g. 0.10–0.30) rather than 'about half'; estimate a trend break at the true date directly; and label the sentence as post hoc wherever it appears.

2. 'Lasting gains' / 'persists for at least a decade' is not identified

   major · Abstract; Sec. 4.4; Sec. 5.5; Sec. 6; Fig. 1a,b

   The abstract ('lasting gains'), Sec. 5.5 ('the gain persists for at least a decade') and the plain-language summary ('The rise did not fade … still gaining') read the raw profile $\beta_k$ as a durable release effect. But the fake-date profile in Fig. 1b also rises steadily over ten years, to 0.750 at fake $k=10$ (about 0.06/yr before the true release, check 05). The trajectory-adjusted P2 estimate covers only $k=0..3$. The part of the $k=4..10$ rise that is release-related is therefore not separated from the pre-existing trend. Under the paper's own logic, the continued rise is at least partly trajectory.

   The decay test (H5) is computed correctly ($\lambda=-0.115$ reproduced, check 07). However, 'not identified' under the rule is read in Sec. 4.4 as 'beyond ten years', and in Sec. 5.5 as evidence against short-lived fads. With a trend-dominated average profile and staggered individual peaks, the test cannot show either.

   Fix: extend the true-minus-fake comparison to $k=4..10$ (feasible for event years ≤ 2015). Until that is done, replace 'lasting'/'persists' with a statement that the raw gap keeps widening, of unknown attribution.

3. Preregistration cannot be verified, and adherence is incompletely documented

   major · Title; Sec. 3.1; Sec. 3.8; Table 1 note; Abstract; Sec. 1; Sec. 5.5; Sec. 6; Code and data availability

   The title rests on 'preregistered'. The plan was frozen internally on 10 Nov 2026 at 04:32:17 UTC, the same date the paper carries. It was not deposited with a third-party registry (OSF, AsPredicted), and the plan, deviation log and code were not available for review (check 17). A reader therefore cannot confirm the freeze time, the plan's content, or that 'confirmatory analyses are reported exactly as planned'.

   Where adherence can be checked, there are gaps. Table 1 states BH 'within the ten hypotheses', but every q-value reproduces only with $m=9$, i.e. H6 was dropped (check 09). The result is harmless but it is an unlisted departure. Four of 15 headline claims are post hoc, and the abstract's closing sentence, Sec. 1 and Sec. 5.5 state the post hoc 'about half' without the label. The genre result in the abstract is exploratory (X4) and unlabelled (check 13). The plain-language summary says 'the plan for the analysis was fixed and locked before any results were looked at'. That sentence does not tell the lay reader that the central interpretation came afterwards.

   Fix: publish the frozen plan and the hash target with an independent timestamp. Add a plan-vs-paper table covering every hypothesis, list the $m=9$ change as a departure, and label every post hoc or exploratory claim in the abstract, introduction, conclusions and summary.

4. The preregistered 'made popular' rule was foreseeably near-unattainable, leaving RQ2 answered only post hoc

   major · Sec. 3.6; Sec. 4.3; Table 2 and note; Sec. 5.4

   With about 500 placebo stacks per baseline decile, the smallest attainable p is about 1/501. BH at $q<0.05$ over $m=1{,}332$ names then needs at least 54 names that beat every placebo in their decile before any single rejection is possible (check 08). The observed minimum q of 0.18 implies about 15 such names. The rule is thus not impossible 'at this sample size', as Sec. 4.3 and 5.4 say. It is underpowered by design. A pre-freeze power check on the synthetic stacks the plan already used (Sec. 3.5) would have shown this, and 20,000–50,000 placebo stacks would bring the requirement down to 6–14 floor names. One of the three research questions ('how many names do releases make popular') therefore rests entirely on the post hoc P1 count of about 81.

   Fix: state that this was a design flaw. Rerun the preregistered rule with a larger placebo reference, or use a parametric or extreme-value tail approximation, and report that alongside P1.

5. Control and placebo names come from a different population than character names

   major · Sec. 3.4; Sec. 3.6; Sec. 4.1

   The control pool excludes every name used by a main character in any major title from 1975 to 2025, and also excludes phonetic and spelling neighbours. The placebo pool is built the same way. Controls are therefore names that writers never chose. Character names, by the paper's own argument (Sec. 1), are chosen because they are fashionable or rising. Matching on a three-year level and trend does not remove differences in longer-run dynamics: the held-out leads differ by about 0.10, and R13 changes the estimate. The placebo distribution then measures noise among never-chosen names, not the selection process, which weakens both the 'made popular' calibration and the P1 count.

   Fix: add a not-yet-treated design (character names whose release falls 8 or more years later serve as controls), in the spirit of the staggered-DiD estimators the paper cites [29, 30]. Also report balance on the $k=-6..-4$ leads and on longer-run curvature.

6. Causal vocabulary in places outruns the associational design

   minor · Abstract; Sec. 4.3; Table 2; Sec. 5.5; Sec. 6

   Sec. 5.3 is careful: the estimate is 'an association … not an experimental effect'. Other places use causal framing. Examples are 'excess births' (Abstract, Table 2), 'attributes about 0.10 … to the release window' (Abstract), 'How many names were made popular' (Table 2 title, Sec. 4.3), 'how long the effect lasts' and 'the boost has no measurable half-life' (Sec. 6), and 'names that a release made popular' (Sec. 5.5). The abstract's closing verb 'coincide' is appropriate. Given weaknesses 1, 2 and 5, the estimand should be described consistently as a gap relative to matched controls.

   Fix: use 'births above the matched-control counterfactual' for excess births, and 'associated with' or 'coincides with' throughout, including the plain-language summary.

7. Data provenance is underspecified

   minor · Sec. 3.2; Sec. 4.7; Table 4 (X5); Code and data availability; Ref. [42]

   The title list cannot be reconstructed from Sec. 3.2. 2,148 films / 40 per year = 53.7 years and 944 series / 20 per year = 47.2 years, which are non-integer and mutually inconsistent, and the year range is not stated (check 15). No Wikidata snapshot or query date is given; the paper says only 'November 2026'. Selection uses present-day sitelinks, a survivorship criterion; Sec. 5.4 acknowledges this. SSA file checksums and release dates are deferred to documentation that was not provided, and [42] has no URL. The national row count (1,316,981) is plausible against the CRAN copy of the SSA data to 2017 (check 16), but the state file count could not be checked. 'Western states' (X5) is undefined; it matches the 13 Census West states exactly (check 12).

   Fix: give the title-year window, the exact SPARQL query and timestamp, the SSA file dates and checksums in the paper, and the region definition.

8. Several internal inconsistencies in counts and summaries

   minor · Sec. 3.3; Sec. 4.1; Sec. 4.2; Sec. 4.3; Table 1; Table 2; Sec. 6

   (a) Sec. 4.1 gives leads of 0.171, 0.111 and 0.076 and a 'mean over these three years' of 0.103. Their mean is 0.119 (check 06). The figures reconcile only if 0.103 is the full-sample mean and the leads are for the 1,172 balanced names, and this affects the diagnostic that motivated departure 1.

   (b) 1,714 − 71 − 350 = 1,293 ≠ 1,332. The gap is explained only by an undocumented overlap of 39 names, which the R5/R6 sample sizes imply (check 10).

   (c) Set B is defined in Sec. 3.3 as names listed in at most two pre-years (1,530 events). Sec. 4.3 analyses 1,211 Set B names that had no listed pre-year, with 319 unaccounted for. Set B names also reach 5 births less often than placebo names (122 vs 176.3), which is unexplained.

   (d) The plain-language summary's '12% boost' converts 0.121 log points as 12% rather than 12.9%, unlike the 0.180 → 19.7% conversion elsewhere (check 01).

   (e) H1 carries two CIs ([0.147, 0.214] vs [0.148, 0.211]).

9. State estimates average well below the national estimate without comment

   minor · Sec. 4.7; Table 5; Fig. 5

   The fixed-effect mean of the Table 5 state estimates is 0.121 (n-weighted 0.123; reproduced, check 12), about two-thirds of the national 0.180. Possible reasons include restriction to names common in a state, different matching, or composition. The paper does not discuss the gap, although it bears on whether the national estimate is driven by a subset of names.

10. Some cited evidence is misstated or unverifiable

    minor · Sec. 1; Sec. 2.1; Sec. 5.2; Refs. [6], [10], [11], [17], [18]

    [10] La Ferrara et al. is cited as Globo areas being '18 to 24% more likely' to have a novela name in the 1994 top 20. In the source these are linear-probability coefficients, i.e. 18–24 percentage points on a base of about 0.085, which is a much larger relative effect (check 18). [11] supports a rise-and-fall within five years, not specifically a peak 'within about three years'. The comparison in Sec. 5.2 against an uncontrolled 98% rests on [17], a commercial blog with no URL. [6] and [18] are grey literature that could not be located.

11. The 'short-lived fads' conclusion over-generalises from an average profile

    minor · Sec. 5.5; Sec. 4.4; Table 2

    Sec. 5.5 says claims that screen media 'routinely create short-lived naming fads are not supported'. An average over 1,332 names with staggered and heterogeneous individual peaks can rise monotonically even if many individual names spike and fall. The paper's own Table 2 shows the gains concentrated in a few titles. Answering this needs name-level profiles, for example the share of P1 names whose own series peaks within 3 years.

Questions for the authors

1. Under what assumption is the true-minus-fake-date difference (P2) a conservative estimate? Why should it be preferred over the linear de-trended (R10, 0.301) and long-trend matched (R13, 0.197) estimates, which imply that the raw estimate understates the release-window change?

2. Does 'about half reflects trajectories' survive when measured in births (fake-date 14,170 vs true-date 240,444 excess births, about 6%) or in names above chance? If not, which metric does the abstract refer to?

3. Can the frozen plan, its hash target, and the deviation log be made public with an independent timestamp? Which pre-release analyses (including the leads test that motivated R13) were run before the 04:32 UTC freeze, and when were the SSA and Wikidata files downloaded relative to it?

4. What is the true-minus-fake-date difference at $k=4..10$? Without it, what supports 'the gain persists for at least a decade'?

5. Is the lead mean of 0.103 (0.079–0.127) computed on all 1,332 names while the three quoted leads use the 1,172 balanced names? What is the mean lead in the balanced sample?

6. How do the estimates change with not-yet-treated character names as controls, instead of names that never appeared on screen?

7. Why was the BH correction in Table 1 applied over nine hypotheses rather than the ten stated, and was this specified in the plan?

8. What happened to the 319 Set B events not in the 1,211-name Set B analysis? Why do Set B names reach 5 births less often than the placebo expectation?

Verification

References

43 references checked

• [10] La Ferrara, Chong, Duryea (2012), Soap Operas and Fertility: Evidence from Brazil, AEJ: Applied 4(4)

  Cited in Sec. 2.1 as Globo areas being '18 to 24% more likely' to have a novela character's name among the 1994 top-20 names. In the source (working-paper Table 9), 0.18-0.24 are linear-probability coefficients, i.e. 18-24 percentage points on a base probability of 0.085 (covered areas: 0.329). The relative increase is far larger than 18-24%. The unit is misstated, though the direction of the claim is supported (work/verify/18_refs_spot.log).

• [17] Little Sleepies (2025), Characters vs. Celebrities: Who's the Inspiration for Baby Names?

  Commercial blog/industry report with no URL or access date; Crossref returns an unrelated work. It is load-bearing in Sec. 5.2: the 'uncontrolled mean of 98%' and the film-vs-series and sex-difference comparisons rest on it alone. Not verifiable as cited.

• [18] BeenVerified (2024), BeenVerified Study Finds Impact of Disney Movies on Baby Names

  Press release/grey literature with no URL; Crossref match is an unrelated 2010 article. Not verifiable as cited (used only as context in Sec. 2.1).

• [6] Verma and Bhardwaj (2020), Game of Thrones: Impact on U.S. Baby Names and Network Analysis, B.Tech. project report, Jaypee University

  Unpublished student report with no URL or repository; Crossref best match is an unrelated FFT-architecture paper. Existence could not be confirmed. Cited in Sec. 1 for the rise of names such as Arya.

• [11] Napierski-Prancl (2016), Brandy, You're a Fine Name, Studies in Popular Culture 38(2):41-54

  Exists (confirmed via web search; Crossref best match is an unrelated 2009 article because the journal has no DOIs). Publisher listing gives pp. 41-53, not 41-54. The paper uses it to support 'peaks within about three years and then falls' (Sec. 1, 5.2); the source tracks girls' names five years before and after a Billboard chart year, which roughly supports 'rise and fall within five years' (Sec. 2.1) but not specifically a three-year peak.

• [19] Ludwig, Hightower, Engels, McGee (2019), Analyzing Influences on U.S. Baby Name Trends, SMU Data Science Review 2(3)

  No Crossref record (best match is a different title with no year); the journal is not DOI-registered. Existence not confirmed in this review. Context-only citation.

• [42] Social Security Administration (2026), Background Information: Popular Baby Names

  Web page cited without URL or access date. It is the primary data source for the whole study, so the exact file, download date and version (the national and state files are revised over time) should be given for provenance.

• [1] Lieberson (2000), A Matter of Taste, Yale University Press

  Crossref matched only a 2002 book review (Language, doi:10.1353/lan.2002.0063). The book itself is well known and exists; no problem with the content attributed to it. Listed for completeness.

• [23] Varnum and Kitayama, Psychological Science 22(2), 2011; [25] Candia et al., Nature Human Behaviour 3(1), 2019; [39] Chen and Roth, QJE 139(2), 2024

  Minor: Crossref gives 2010, 2018 and 2023 (online-first dates) vs the cited print years. The volume/issue cited matches the print year, so this is not an error, only a date-convention difference.

Suggestions

• Rewrite the abstract's last sentence and Sec. 5.5 to report the release-window change as a bracket across the paper's benchmarks (fake-date P2 ≈ 0.10; R13 0.197; R10 0.301). Label the fake-date-based fraction as post hoc and metric-dependent.

• Estimate a trend break at the true release date directly (e.g. a kink in the slope of $\tau$ around $k=0$, using $k\le -1$ for the pre-slope). Fig. 1b already suggests a 1.7× acceleration there.

• Extend the true-vs-fake comparison to $k=4..10$ before claiming persistence, and replace 'lasting' in the title-level summary until it is done.

• Deposit the frozen plan, hash target, code and deviation log in a public registry with a DOI. Add a plan-vs-paper table that also records the $m=9$ BH family.

• Add a not-yet-treated control design and report balance on held-out leads and longer pre-trends.

• Rerun the preregistered 'made popular' rule with 20,000–50,000 placebo stacks per decile, or with a tail approximation, so that RQ2 has a confirmatory answer.

• State the title-year window, the Wikidata query and snapshot time, the SSA file dates and checksums, and the West region definition in the paper itself.

• Fix the internal inconsistencies: lead mean, the 39-name overlap, the Set B definition and n, 12% vs 12.9%, and the two H1 CIs.

• Correct the description of [10] to percentage points, and replace or support the grey-literature comparison [17] in Sec. 5.2.

• Add an authorship and accountability statement naming the system, its operator, and a contact for the preregistration and data.

Ethics and integrity

Scope of this review