Reviews/Osteoporosis Fracture Prevention/Fracture liaison service secondary fracture prevention
Fracture Prevention Services · ostfrac_17 · v2
Across several countries, hospitals that ran a fracture liaison service tended to see fewer repeat fractures than hospitals or earlier periods without one. In Australia, the Netherlands and Korea the reduction reached statistical significance ([1], [2], [11]), and a Swedish study linked the extra osteoporosis treatment such services deliver to fewer repeat fractures ([3]). But one Spanish hip-fracture study found no difference in second fractures after the service was introduced ([5]), and every study was an observational comparison rather than a randomised trial, so other changes over time could explain part of the benefit. The panel judged the signal real and repeated but still clouded by confounding and one contradicting result, placing it short of the top tier.
Three studies with a non-service comparator report significantly lower repeat-fracture risk with a fracture liaison service: [1] (any re-fracture HR 0.67, 0.47-0.95; major re-fracture HR 0.59, 0.39-0.90), [2] (subsequent nonvertebral fracture HR 0.44, 0.25-0.79 at 24 months), and [11] (refracture 5.7% vs 10.7% at 1 year, 2.8% vs 7.1% at 6 months). [3] shows the mechanism, with DXA investigation rising from 7.6% to 39.6% and treatment from 12.6% to 31.8%, and treated patients carrying a 51% lower re-fracture risk (HR 0.49, 0.37-0.65). Against this, [5] found a second fracture in 4.6% after versus 3.6% before implementation (p=0.50) and states the service did not affect second-fracture risk. The corpus spans multiple countries but every design is a historical-control or before-after observational cohort with no randomised trial. The contested point: The evidence divides on whether the benefit holds for all patients and designs: [1], [2] and [11] show significant reductions while [5], a before-after hip-fracture cohort, is a clean null (p=0.50). Whether the effect is the service itself or the osteoporosis treatment it triggers is unsettled, since [3]'s 51% reduction is a treated-versus-untreated contrast, not service-versus-no-service.
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One reviewer's only job is to attack the finding. The challenges below were weighed before the grade was set.
All supportive evidence is observational — historical-control or before-after cohorts ([1], [2], [3], [5], [11]). No RCT in the corpus isolates the FLS effect from secular trends in osteoporosis prescribing or from selection into FLS follow-up.
[5] directly contradicts the claim: FLS implementation did not change second-fracture risk (4.6% vs 3.6%, p=0.50), and its only benefit was mortality in the drug-treated subgroup — not fracture incidence.
Where it remains uncertain. [5] found no change in second-fracture incidence after implementation (4.6% vs 3.6%, p=0.50), and all supporting designs are observational, so secular treatment trends cannot be ruled out.
Aleatory
[11] (n=273) and [5] (n=724) are small single-centre hip-fracture cohorts, so event counts are low and estimates carry wide sampling variability.
Epistemic
Every study is observational before-after or historical-control ([1], [2], [3], [5], [11]); no RCT in the corpus isolates the service effect from secular prescribing trends or selection into follow-up.
Inferential
[3]'s 51% reduction (HR 0.49) is treated-versus-untreated, not service-versus-no-service, so crediting it to the service conflates the pathway with the drug.
The load-bearing papers from a corpus of 11, each classified by what it does to the claim. Every DOI is taken from the corpus the claim was graded on.
Primary supportive cohort: significant re-fracture reduction, FLS vs non-FLS hospital, NNT 20 over 3 years.
“there was a ∼30% reduction in rate of any re-fracture at the FLS hospital (hazard ratio (HR) 0.67, confidence interval (CI) 0.47-0.95, p value 0.025) and a ∼40% reduction in major re-fractures (hip, spine, femur, pelvis or humerus) (HR 0.59, CI 0.39-0.90, p value 0.013)”
Panel auditInternal validity: medium · scope of inference: Patients ≥50 years presenting with minimal trauma fracture to emergency departments; 3-year re-fracture risk.Key limitations: non-randomised · single FLS vs single non-FLS hospital · residual confounding possible
Large cohort showing significant 24-month reduction, but null at 12 months — effect is time-dependent.
“The subsequent nonvertebral fracture risk was also significantly lower in the patients in the FLS group, but this effect was time-dependent, with a hazard ratio of 0.84 (95% CI: 0.64 to 1.10) at twelve months and 0.44 (95% CI: 0.25 to 0.79) at twenty-four months.”
Panel auditInternal validity: medium · scope of inference: Patients ≥50 years with a nonvertebral fracture; subsequent nonvertebral fracture over two years.Key limitations: non-randomised · time-dependent effect not significant at 12 months · two-hospital comparison
Supports mechanism (FLS raises treatment uptake; treatment lowers re-fracture) but contrast is treated-vs-untreated, not FLS-vs-no-FLS.
“Treated patients had a 51 % lower risk of any re-fracture than untreated patients (HR 0.49, 95 % CI 0.37-0.65 p < 0.001).”
Panel auditInternal validity: medium · scope of inference: Patients >50 years with hip, vertebra, shoulder, wrist or pelvis fracture; investigation/treatment uptake and re-fracture by treatment status.Key limitations: re-fracture contrast is treated vs untreated, not FLS vs control · historic control · confounding by indication
The model estimates that 18 fractures were prevented in the FLS arm versus usual care, directionally supporting the claim, though this is a modelled estimate not an observed outcome.
Panel auditInternal validity: low · scope of inference: UK hypothetical cohort of fragility-fracture patients; modelled cost-effectiveness and fractures avoided.Key limitations: modelled not observed · based on audit-derived assumptions · no statistical testing
4 of 11 papers shown. The full review lists all of them, with the panel’s arbitration →
Claims are graded at each quarterly release, and re-graded between releases only when a pivotal trial lands. Every change is a new version of the claim.
Replicated, independent, direction-consistent cohort evidence supports the claim but confounding-prone non-randomised designs and one contradicting study hold it below the Established band.
Release 2026-q4 re-graded every claim from its corpus under protocol v0.19. An earlier release's grade is shown for the record; it came from an earlier protocol and is not a movement.
Assumptions that carry weight but are not themselves established.
The panel records the gap that would most move the claim, and the study that would close it.
No randomised evidence. All supportive cohorts ([1], [2], [11]) are observational, so secular prescribing trends and selection into follow-up could explain part or all of the signal. The panel rates this the highest-importance open gap for the claim, and names the study design that would close it: A cluster-randomised trial allocating hospitals or regions to a fracture liaison service versus usual care with re-fracture as the primary outcome.
Open question: Does a fracture liaison service reduce secondary fracture incidence when tested against usual care under randomisation? Why it is still open: Every supporting study in the corpus ([1], [2], [11]) is an observational cohort; there is no RCT to rule out secular trends and selection.
Priors is a sceptical first reader, not peer review, and not medical advice.
Release 2026-q4 · graded 21 Oct 2026 · protocol v0.19