The TriNetX Global Collaborative Network snapshot queried on May 3, 2026, served as the data source. From a source population of 82,364,945 female patients aged 20 years or older, the study applied a 12-month washout and excluded carcinoma in situ only. The three operational definitions produced markedly different cohort sizes: the single-diagnosis-code rule (Dx1) identified 1,450,233 patients; the repeated-diagnosis rule within 90 days (Dx2) identified 678,739 patients; and the diagnosis-plus-treatment rule (DxTx) identified 578,576 patients. Simple arithmetic does not capture the analytic consequence: increasing confirmation requirements reduced cohort yield and altered the pool available for matching and outcome estimation.
Dx1, Dx2, and DxTx all used ICD-10-CM C50.* codes to define invasive breast cancer, with D05.* codes excluded. The DxTx requirement for treatment evidence (surgery, chemotherapy, breast cancer-related medication within 90 days, or radiotherapy within 180 days) reduced the cohort relative to diagnosis-only rules, but the authors explicitly note that additional requirements were not assumed to confer greater diagnostic validity; treatment capture may reflect care-setting differences as much as disease certainty.
The study team constructed three pairwise propensity-score matched samples: DxTx versus Dx1, Dx2 versus Dx1, and DxTx versus Dx2. Each model included 13 prespecified baseline covariates: age at index, five race categories as recorded in TriNetX (White, Black or African American, Asian, other race, and unknown race), hypertension, diabetes mellitus, stroke, dyslipidemia, chronic kidney disease, body mass index, and serum albumin. The investigators used TriNetX's built-in greedy nearest-neighbor matching with a caliper of 0.1 pooled standard deviations.
Matching reduced measured imbalances. After one-to-one matching, standardized mean differences for all covariates were under the prespecified 0.10 threshold across comparisons. Matched pair counts were 565,417 (DxTx vs Dx1), 678,739 (Dx2 vs Dx1), and 555,617 (DxTx vs Dx2). The study acknowledges that the underlying platform implementation is proprietary and that individual-level matching assignments could not be independently verified by the authors.
All-cause mortality was analyzed as time-to-event starting 180 days after the index date, with assessment windows of day 180–1 year, day 180–3 years, and day 180–5 years. Across all matched comparisons and windows, the more restrictive phenotype tended to have higher mortality hazard. The reported hazard-ratio ranges for mortality were: 1.26 to 1.32 for DxTx versus Dx1, 1.13 to 1.14 for Dx2 versus Dx1, and 1.13 to 1.17 for DxTx versus Dx2. Those hazard ratios represent relative differences between phenotype-defined populations after matching on the prespecified covariates.
The authors caution that these associations should be interpreted as differences arising from selection and ascertainment mechanisms inherent to phenotype definitions, rather than as treatment effects or causal effects of being classified under one phenotype versus another. The study did not evaluate cause-specific mortality, cancer progression, recurrence, or stage at diagnosis because pathology, stage, and receptor-status data were not used to determine cohort membership.
Time to first emergency department encounter was evaluated using the same follow-up windows and the same matched samples. Emergency department visit estimates followed a similar pattern to mortality: the more stringent phenotype definitions (Dx2 and DxTx) were associated with higher hazards of a first emergency department visit after matching, but the effect sizes were smaller than for mortality and attenuated across windows. The outcome definition captured only time to first recorded emergency department encounter within each window and did not measure recurrence or frequency of visits.
Appendicitis and femoral neck fracture were prespecified as negative-control outcomes and analyzed as time-to-first-event within each assessment window. These outcomes were chosen because they are not expected to be causally affected by how invasive breast cancer is defined in EHR data. Data indicated that negative-control estimates were generally close to the null. Small associations for appendicitis appeared in analyses involving Dx1, but those did not remain statistically significant after Holm adjustment for multiple testing across the 18 negative-control tests. The authors used E-values to quantify the minimum strength of unmeasured confounding required to explain observed associations, though detailed E-value figures are reported in the manuscript and supporting materials rather than reproduced here.
This study benchmarked analytic consequences rather than establishing diagnostic gold-standard validity. The authors did not have access to patient-level TriNetX data for public sharing; aggregate results and operational definitions that can be legally shared are provided in the manuscript and supporting information. Several limitations were reported explicitly: pathology, tumor stage, grade, and receptor status were not used to define cohorts; cause-specific mortality and progression outcomes were not assessed; the TriNetX matching algorithm and implementation are proprietary and could not be independently audited by the investigators; and cohort counts reflect the data snapshot on May 3, 2026. The study did not perform a formal sample size calculation because it analyzed all eligible patients in the network.
These results leave specific unanswered questions that warrant further work: how do phenotype-driven differences map to underlying tumor stage or biologic risk, and how would chart validation or linkage to cancer registries alter cohort performance? The authors recommend treating phenotype specification as a core analytic decision with transparent reporting and sensitivity analyses, and they provide operational coding criteria and aggregated results in supporting materials for replication and scrutiny.