The Threshold Fallacy: Cutting the Evidence to Fit the Bed

Dear Editor,

Systematic reviews should distill, not distort, primary data. Done rigorously, they guide practice and policy. But when methods alter original findings, they create false certainty, spread error, and mislead clinicians.

1. The Threshold Fallacy

A central problem is the threshold fallacy: inventing cut‐offs absent in primary studies to fabricate comparability. Continuous variables, such as albumin or BMI, can only be dichotomized using thresholds chosen by each study, which are embedded in its design and population. Each cut‐off point carries distinct prognostic meaning, context, and parameters (sensitivity and specificity). Creating new thresholds post hoc does not harmonise evidence—it rewrites it. Liu et al.'s recent work (‘Risk factors for surgical site infections after orthopaedic surgery: a meta‐analysis and systematic review’) [1] illustrates this.

1.1. Distortion of Serum Albumin Thresholds

Example 1: Lau et al. [2]

Lau et al. stratified patients into ≤ 20, 21–30, and > 30 g/L. They reported adjusted odds ratios (ORs) of 3.07 (95% CI, 0.96–9.80) for ≤ 20 vs. > 30 and 0.70 (95% CI, 0.37–1.35) for 21–30 vs. > 30—estimates that point in opposite directions and are not statistically significant. Rather than extracting crude data, Liu et al. imported these adjusted ORs directly. They entered both into the same meta‐analysis as if they were independent studies, which breaches the assumption of independence required in meta‐analysis. The cohort, which contributed about one‐quarter of the pooled weight, was thus duplicated. Worse, they re‐labelled these comparisons as if Lau et al. had used a threshold of ‘< 35 g/L’, a cut‐off that never existed. Collapsing ≤ 20 (OR ≈3) and 21–30 (OR ≈0.7) into one artificial ‘< 5 g/L’ group destroys the meaning of risk stratification.

Example 2: Namba et al. [3]

Namba defined hypoalbuminemia as < 3.2 g/dL (≈32 g/L) and reported an adjusted OR of 6.24 (95% CI, 1.82–21.35). In the meta‐analysis, this was rewritten as ‘< 35 g/L’, erasing the study's specific design choice and creating the false impression of equivalence with other, differently defined cohorts.

Example 3: Ren et al. [4]

Ren conducted a multicenter geriatric study in which hypoalbuminemia was defined using a threshold of 32.6 g/L. Here too, Liu et al. disregarded the original definition and recoded the exposure as ‘< 35 g/L’. This manoeuvre ignored the tailored prognostic cut‐off derived for an elderly population and further enforced the illusion of homogeneity across studies with incompatible definitions.

Taken together, these cases show how thresholds that never existed in the primary literature were retrofitted into a fictitious common category. Such practice results in a substantial misrepresentation of the evidence: serum albumin levels of 20, 30, 32, and 32.6 g/L may carry very different prognostic implications, and no analytical shortcut can justify collapsing them into an invented ‘< 35 g/L’ threshold. A valid approach would have been to apply a bivariate diagnostic test accuracy model, which is specifically designed to accommodate multiple thresholds without collapsing them into an artificial category.

2. Pooling Heterogeneous Populations

Liu et al. combined arthroplasty, trauma fixation, oncologic reconstructions, spine surgery, and geriatric cohorts, among others, and without any stratified design. These differ in baseline risks, infection profiles, and prophylactic strategies, making pooled estimates meaningless. The very studies discussed as albumin case examples already illustrate this: Lau et al. [2] studied hip hemiarthroplasty in elderly patients (mean age 77–78 years), Namba et al. [3] studied spinal surgery in a middle‐aged cohort (mean age 55), and Ren et al. [4] studied multicenter geriatric orthopaedics (mean age 67). They stem from radically different surgical contexts that should never be merged into a single category labelled ‘orthopaedic surgery’.

3. Misapplied Statistical Methods

The meta‐analytical model was switched between fixed and random effects based solely on whether I ² exceeded 50%, a rule that the Cochrane Handbook explicitly cautions against [5]. Between‐study variance (τ ²), the fundamental measure of heterogeneity, was never reported. The outdated DerSimonian–Laird estimator was used, despite well‐documented limitations in small or heterogeneous sets. Confidence intervals appear to be Wald‐type, with no indication that more robust approaches such as the Hartung–Knapp–Sidik–Jonkman adjustment were considered. Contemporary guidance recommends variance estimators, such as REML or Paule–Mandel, coupled with robust confidence intervals, like HKSJ, especially in small or heterogeneous evidence bases.

The authors further state: ‘Risk estimates in each study were presented as odds ratios (OR) without distinguishing between OR, relative risks or hazard ratios’ [1]. ORs were imposed across all studies, ignoring the greater interpretability of relative risks in cohort designs and hazard ratios in time‐to‐event data. This decision is not trivial: ORs systematically exaggerate effect sizes when events are common, as in the case of surgical site infections, and are less meaningful for clinical risk communication.

Sensitivity analysis was limited to a leave‐one‐out procedure, with no subgroup exploration, influence diagnostics, or meta‐regression. Finally, the review mislabeled its analyses as ‘multivariate meta‐analysis’. In reality, it simply pooled adjusted ORs from multivariable primary studies, which are not equivalent to a true multivariate or multi‐outcome meta‐analytic model. This misnomer risks misleading readers about the level of methodological sophistication applied.

4. Outdated Standards and Missing Transparency

The review cited PRISMA 2009 instead of the updated 2020 Statement [6], disregarding more than a decade of improvements in reporting standards. Moreover, there are clear inconsistencies with its PROSPERO registration (CRD42024550661), which specified a stratified design with planned subgroup analyses by age, sex, procedure, and region—none of which were ultimately performed.

5. Conclusion

Systematic reviews must safeguard, not distort, the evidence base. A meta‐analysis that rewrites thresholds, duplicates data, conflates populations, and relies on obsolete methods falls short of synthesising evidence and instead risks reshaping it. Given the severity and demonstrability of these flaws, I believe editorial action is warranted to prevent this misrepresentation from standing unchallenged in the scientific record.

Conflicts of Interest

The author declares no conflicts of interest.

Arredondo Montero J., “The Threshold Fallacy: Cutting the Evidence to Fit the Bed,” International Wound Journal 22, no. 11 (2025): e70783, 10.1111/iwj.70783.

Data Availability Statement

Data sharing not applicable to this article as no datasets were generated or analysed during the current study.