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How Long Do Dental Implants Really Last? Informative Dropout, Competing Mortality, and Bounds on Twenty-Year Survival

Paper type
Methodological Study (theoretical, with illustrative simulation)
Status
Original Work · Working Paper
Keywords:
dental implants · survival analysis · informative censoring · competing risks · loss to follow-up · partial identification · sensitivity analysis
Contents
  1. 1Introduction
  2. 2Background and critical appraisal of the evidence
  3. 3Hypothesis and theoretical framework
  4. 4Proposed methodology
  5. 5Competing explanations and how the design discriminates among them
  6. 6Clinical and engineering implications
  7. 7Limitations
  8. 8Conclusions

Abstract

Background. Twenty-year implant survival figures of roughly 90% or higher come from Kaplan-Meier or complete-case analyses of cohorts that lose a large share of patients. Published sensitivity meta-analyses show that plausible imputation for the lost patients lowers pooled survival materially, but no study identified in our search traced the dropouts or modeled the dropout mechanism. Kaplan-Meier assumes that censoring is non-informative, and it treats death as censoring rather than as a competing event.

Objective/Hypothesis. We set out what can and cannot be concluded from such cohorts. We hypothesize that dropout that depends on impending implant failure biases Kaplan-Meier survival upward, that death as a competing event produces a smaller and separate discrepancy, and that the true 20-year figure cannot be narrowed below worst-case/best-case bounds without information on the dropouts. The null hypothesis is that the net bias is below 2 percentage points.

Proposed approach. We derive Manski-type bounds as a function of the dropout proportion, define the Kaplan-Meier and cumulative-incidence estimands, run a Monte Carlo simulation (1,000 replicates, 1,000 patients each) under six stated dropout scenarios, and specify inverse-probability-of-censoring weighting, a tipping-point analysis and a design that combines registry linkage with tracing of a random sample of dropouts. Sample-size arithmetic for the tracing sub-study is given.

Expected contribution. The paper separates three estimands, maps the direction of each bias, and states numbered predictions with the results that would refute them. In the simulation, dropout that conceals 25% and 50% of failures lowers estimated 20-year failure by 2.4 and 4.9 percentage points, whereas independent dropout produces no bias and covariate-dependent dropout is corrected by weighting. These are illustrative values under assumptions, not empirical data.

Conclusions. Reported 20-year survival is best read as a point inside an interval whose width equals the dropout proportion. Only linkage plus tracing can place the true value inside that interval. The concern is falsifiable and may prove unfounded if traced dropouts have failure risk close to that of followed patients.

1. Introduction

Clinicians and patients ask how long an implant will last, and the answers come from long-term cohorts and their meta-analyses. A 20-year survival of 90% or more is a common summary. The number is trusted because the studies behind it are prospective and the follow-up is long. Yet long follow-up and low attrition are different properties. In a cohort of several hundred patients followed for two decades, a large fraction die, move, or stop attending. The survival estimate then rests on those who remain.

Two sensitivity meta-analyses have made this visible. For 10-year survival, one review of prospective studies reported 96.4% under complete-case analysis and 93.2% after plausible imputation for lost patients, with a wide prediction interval [1]. For 20-year survival, a later review reported 92% in 237 followed implants from three prospective studies, falling to 78% when the 422 placed implants were all counted [2]. These reviews establish that the figure depends on assumptions about the lost patients. They do not say which assumption is right, because neither had individual patient data and neither traced the dropouts.

This manuscript asks a narrower and more answerable question than “what is the true survival.” It asks what the existing data can support, in what direction each known bias pushes the estimate, and what study would identify the quantity. Three distinct problems are entangled in the usual analysis. First, dropout may be informative, meaning related to the implant’s impending fate. Second, death is a competing event that ends the possibility of implant failure; treating it as censoring changes the meaning of the estimate. Third, selection of cohorts by retention, as when only patients with at least 20 years of follow-up are analyzed, conditions on being observable [3].

The paper is a methodological study with an illustrative computation; no patient data were analyzed. Its contribution is a framework, not a new estimator: bounds, a map of bias directions, a simulation showing when conventional corrections work and when they cannot, and a design with sample-size reasoning.

2. Background and critical appraisal of the evidence

What the long-term cohorts report

Long-term implant literature is dominated by single-center prospective and retrospective series. A Swedish 20-year follow-up of edentulous patients treated in the early 1980s found that 19 of 48 patients were deceased at the 20-year point and 21 of the 29 survivors could be examined [4]. A recent prospective report on a single implant surface at 20 years noted that 20 patients with 25 implants were lost from follow-up, mostly because of death [5]. A retrospective study that included only patients followed for at least 20 years reported 87.8% cumulative survival at 36 years [3]; its design conditions on being observable at 20 years. A very large consecutive series of 4,585 edentulous arches over 30 years found that the failure rate did not reach a steady state [6]. The newest pooled estimate, from ten prospective studies, reports 20-year survival of 93.0% using a Kaplan-Meier approach, with 1,857 implants at baseline and 1,028 followed for at least 20 years; the cause of failure was stated for 44 of 115 failures [7]. We use these counts only as illustrative inputs below, because the abstract does not define precisely how the 1,028 were counted.

Reporting of attrition is itself incomplete. A survey of randomized trials in periodontology and implantology found that reasons for loss to follow-up are often not fully reported in flow diagrams [8]. Without reasons, readers cannot separate death, relocation, and care elsewhere, which have different implications for bias.

Imputation meta-analyses

The two sensitivity reviews [1, 2] are the closest prior work. Their message is consistent in direction: assuming that lost patients fared worse than retained patients lowers the pooled estimate. Their limits are equally consistent. The imputation rules are assumptions, not measurements. A worst-case rule that counts every lost implant as failed overstates loss if some dropouts died with functioning implants, as the Swedish and 20-year TiUnite series suggest [4, 5]. A rule that counts all dropouts as surviving overstates success if failing implants prompt patients to seek care elsewhere. The truth lies between, and the reviews cannot say where.

Population-level and administrative estimates

Estimates from randomly selected or population-wide samples differ from clinic cohorts. In a randomly selected Swedish sample, 7.6% of examined patients had lost at least one implant by nine years [9]. A US general-practice network reported survival and success lower than academic reports [10]. In a veteran cohort, the prevalence of failure was 6.7% to 6.9% [11], and a Korean nationwide claims study of elderly patients reported fewer than 3.9 complication treatments per 1,000 implant-years [12]. These figures are not comparable with each other, because the denominators, the definitions of failure, and the ascertainment of removal differ. Their spread indicates that outcome ascertainment, not only attrition, shapes published figures. Whether administrative removal codes capture chart-verified losses is untested in the sources we found.

Competing risks and loss to follow-up in other fields

The idea that death as a competing event distorts Kaplan-Meier estimates is established in orthopaedics. A 2007 paper argued that the Kaplan-Meier estimator is designed for events that eventually occur in all patients and overestimates the probability of the event of interest when competing events are present; it proposed the cumulative incidence estimator as an alternative [13]. A meta-analysis of joint arthroplasty studies found that the pooled cumulative incidence of revision by Kaplan-Meier was 1.55 times that by the competing-risks method, and that the overestimation did not clearly rise with follow-up length or the proportion of competing events, a pattern the authors suggested might reflect limited numbers [14]. A 2016 analysis of tibial implant types showed how competing death can alter comparisons [15]. A 2026 registry-linked study of 2,920 knee replacements reported a 15-year revision estimate of 8.3% by Kaplan-Meier against 7.4% by competing-risk estimation, with larger relative overestimation in patients aged 85 or older [16].

The position is not unanimous. Analysts at the Norwegian arthroplasty register argued that classical Kaplan-Meier and Cox analyses are preferable for time to revision, that adding death as a competing risk always lowers the estimated probability of revision and does not correct dependence between death and revision, and that adjustment for age and sex nearly removed differences between models [17]. The disagreement is partly about the estimand: the net failure probability (what would happen if death were removed) versus the crude probability (what actually happens in a mortal population). Both are legitimate; they answer different questions.

Outside orthopaedics, tracing of patients lost to follow-up is an established technique. In HIV treatment programs in Zambia, a probability sample of patients lost to follow-up was traced and incorporated through weights, and the 2-year cumulative mortality estimate rose from 1.9% to a corrected 7.0% among all antiretroviral therapy users [18]. Multi-country tracing studies in southern Africa documented high unreported mortality among lost youth [19], and a comparison of tracing with linkage to a health information exchange examined how the two routes correct mortality estimates [20]. In the statistical literature, tracing designs with selection models for efficient sampling are available for cohorts with attrition [21]. These precedents show that tracing a sample of the lost and weighting it back works in other settings and that the corrections can be large.

Implant-specific searches

In the PubMed and Europe PMC searches described in the Declarations, we did not find an implant cohort that traced dropouts through registry linkage or a sampling-based tracing study, or an implant survival analysis that modeled death as a competing event alongside informative dropout. We did find a 2026 survival-modeling paper that treats implant failure and reimplantation as dependent events and uses inverse-probability-of-censoring weighting for validation [22]; it does not address dropout or death. Recent cohort analyses continue to report Kaplan-Meier and Cox estimates without a competing-risk treatment; one example gives cumulative survival of 82.6% at 180 months with a median follow-up of 85.5 months [23]. The search is not exhaustive (Embase, Scopus and Web of Science were not accessible), and absence from PubMed is weak evidence of absence.

Table 1. Pivotal sources, their design, and the main bias for the present question. Evidence level (A-E) is an operational category for this manuscript, not GRADE: A strong, B moderate, C preliminary, D mechanistic or theoretical, E speculative.
SourceDesign and size (as seen in abstract)Main bias or limit for this questionLevel
Howe 2019 [1]Systematic review, 18 prospective studies; 10-year survival 96.4% to 93.2% with imputationImputation rules are assumptions; no individual dataB
Kupka 2024 [2]Three prospective 20-year studies; 92% in 237 followed vs 78% imputed to 422 placedFew small studies; imputation ruleB
Lupi 2026 [7]Ten prospective studies, 1,857 baseline implants, 1,028 followed at 20 years; 93.0%Dropout not modeled; counting of followed implants unclearB
Chrcanovic 2018 [3]Retrospective, patients with at least 20 years of follow-up; 87.8% at 36 yearsConditions on retentionC
Ostman 2024 [5]Prospective 20-year report; 20 patients (25 implants) lost, mostly deathsSingle implant type; smallC
Lacny 2015 [14]Meta-analysis in arthroplasty; Kaplan-Meier 1.55 times competing-risks estimateOther field; heterogeneityB
Lie 2022 [17]Norwegian register, 15,734 cemented and 7,867 uncemented THAsArgues against routine competing-risk correctionB
Holmes 2018 [18]Probability sample of lost patients, HIV program, Zambia; 2-year mortality 1.9% to 7.0%Other disease; death outcomeB

3. Hypothesis and theoretical framework

Notation and estimands

Consider a cohort of N patients, each with one index implant (the extension to several implants per patient requires cluster-robust variance and is described in section 4). For each patient define three latent times, measured in years from placement:

  • T: time to implant failure (removal or loss), the event of interest;
  • D: time to death;
  • C: time to dropout, meaning the patient is no longer observed for implant status.

The horizon is τ=20 years. The observed time is T=min(T,D,C,τ), and the observed event type is failure (ϵ=1), death (ϵ=2), or censoring (ϵ=0).

Three estimands answer three different questions.

  • Net failure probability F_(net)(τ)=P(T≤τ): the probability that an implant would fail within 20 years if death could not intervene. Net survival is S_(net)(τ)=1−F_(net)(τ). This is what Kaplan-Meier targets when death and dropout are independent censoring.
  • Cumulative incidence (crude failure probability) F_1(τ)=P(T≤τ, T<D): the probability that an implant fails within 20 years and before the patient’s death. It is estimated by the Aalen-Johansen estimator, which weights each failure by the overall probability of being event-free just before it [24, 25]. Subdistribution-hazard regression, introduced by Fine and Gray, models the same quantity [26].
  • Functioning implant in a living patient P(T>τ,D>τ) and the related quantity “implant in situ at death or at 20 years”, which are the figures a patient or payer may care about.

For a patient who might die, the second estimand is the more literal answer to “how likely is it that my implant fails during my life.” For comparing implant types in cohorts with differing age, the first, or a cause-specific hazard, is usually the more transparent summary, a point on which the arthroplasty literature divides [16, 17]. We therefore treat both and refuse to call either “the” survival.

With cause-specific hazards λ_1(t) for failure and λ_2(t) for death and overall event-free survival S(t)=exp{−∫_0^t (λ_1(u)+λ_2(u)) du},

F_1(τ)=∫_0^τ S(u^−) λ_1(u) du,  1−KM(τ)→1−exp(−∫_0^τ λ_1(u) du)=F_(net)(τ)

when censoring is independent. Because S(u^−)≤exp{−∫_0^u λ_1} whenever λ_2>0, F_1(τ)≤F_(net)(τ): 1 minus Kaplan-Meier exceeds the cumulative incidence by an amount that increases with the death hazard and the failure hazard. For small failure probability F and death probability M, and deaths spread evenly over the horizon, the gap is approximately F⋅M/2. With a 10% net failure probability and 35% death probability this gives 1.75 percentage points; because Gompertz deaths concentrate late, the simulation gives a smaller 1.27 (section 4.3). The competing-risk gap in implant cohorts is therefore modest when failure is rare, in contrast with arthroplasty settings of high age and high mortality [16].

Dropout and identification

Kaplan-Meier consistently estimates S_(net) only if, at each time, the hazard of censoring among those still at risk does not depend on the unobserved failure time (conditional independence of T and C, possibly given observed covariates). Two classes of violation matter.

Dependence on observed covariates (for example, smoking status recorded at baseline, which raises both failure risk and dropout risk). This can be corrected. Kaplan-Meier is itself an inverse-probability-of-censoring weighted average [27], and weighting by the covariate-specific censoring survival function restores consistency [28].

Dependence on the unobserved failure time, for instance a patient whose implant is failing but who has not yet been recorded and who stops attending or seeks care elsewhere. No weighting using recorded covariates can correct this, because the information needed is the very outcome that is missing. The problem is identified only by external information about the dropouts (linkage or tracing) or by assumptions.

Partial identification (Manski-type bounds)

Let π be the proportion of the cohort that is unresolved at τ (dropout before 20 years, no failure observed), and S_(obs) the survival proportion among resolved patients. With no assumption about the dropouts, the 20-year survival of the cohort lies in

S_(obs)(1−π) ≤ S(τ) ≤ S_(obs)(1−π)+π.

The interval has width exactly π. This simple form ignores partial information (failures observed before dropout, and the time at which patients dropped out). A time-refined version sets all dropouts to fail at the moment of dropout (lower bound) or to survive to τ (upper bound) in a Kaplan-Meier calculation and is narrower; it should be used with real data. The simple form is conservative and is used here because it requires only two published quantities.

If a known share d of the unresolved patients died with the implant in situ, and the estimand is “implant not lost before death or 20 years”, those patients are resolved for that estimand, so the lower bound rises to S_(obs)(1−π)+πd and the width falls to π(1−d). This captures the counter-argument in the candidate notes: worst-case imputation overstates loss when many dropouts are deaths with surviving implants. The bounds are about the estimand, not the data, which is why the competing-risk question and the dropout question cannot be separated.

Tipping-point (pattern-mixture) analysis

A pattern-mixture formulation writes the cohort survival as a mixture over observation patterns:

S(τ)=(1−π) S_(obs)+π (1−f),

where f is the unobserved 20-year failure probability among dropouts. The sensitivity parameter is f, or equivalently the ratio f/(1−S_(obs)) of failure risk in dropouts to that in followed patients. Setting S(τ)=S^* for a clinically meaningful threshold S^* gives the tipping point f^*=1−(S^*−(1−π)S_(obs))/π. The reader then judges whether f^* is plausible. This is a transparent way to present what must be believed for a claim (“survival exceeds 85%”) to fail, and it follows the logic of nonignorable-dropout sensitivity analyses in the statistical literature [29].

Hypotheses and numbered predictions

H1. In long-term implant cohorts, a material share of dropouts is related to impending implant failure, so that Kaplan-Meier and complete-case estimates of 20-year survival are biased upward by at least 2 percentage points.

H0. After linkage and tracing, the corrected estimate differs from the uncorrected one by less than 2 percentage points.

The threshold of 2 points is a pragmatic decision threshold, comparable to the width of reported confidence intervals in 20-year meta-analyses [2, 7]; the authors of a real study should justify their own.

Predictions:

  • P1. In any cohort with at least 30% unresolved dropout, the bounds in section 3.3 are at least 30 points wide, so the published point estimates cannot be distinguished from values below 85% without information on dropouts. (Mathematical consequence; refuted only by an error in the arithmetic.)
  • P2. In a cohort where traced dropouts have a 20-year failure risk at least 2.5 times that of followed patients, 20-year survival after correction will be at least 2 points lower than the Kaplan-Meier estimate. Refuted if the traced ratio is below about 1.5 at 30% dropout.
  • P3. Among dropouts, a substantial proportion (our expectation: at least one third in cohorts started before 2000) will be found to have died, and most of those deaths will have occurred with the implant in situ. Refuted if death accounts for under 10% of traced dropouts.
  • P4. Dropout is not uniformly adverse: some of it is “healthy attender” attrition in which patients without problems stop returning, which biases Kaplan-Meier downward. Refuted if the hazard of dropout is not lower among patients who never fail than among those who later fail, after adjustment.
  • P5. Inverse-probability-of-censoring weights built from baseline covariates will move the estimate by under 1 point while tracing moves it by more, in cohorts where dropout depends on impending failure. Refuted if weights recover the traced estimate.
  • P6. The gap between 1 minus Kaplan-Meier and the cumulative incidence will be under 2 points at 20 years when 20-year failure is under 15% and death before 20 years is under 40%. Refuted by a larger observed gap.

Results that would show the concern is unfounded. (a) Traced dropouts have failure risk statistically indistinguishable from followed patients, with a confidence interval excluding a 2-point shift in cohort survival. (b) Dropout is almost entirely death or documented relocation, with implants known to be in situ at the last contact. (c) The registry-linked estimate agrees with the complete-case estimate within 2 points. Any of these, with adequate precision, supports H0.

4. Proposed methodology

Overview and design logic

The methodology has two parts. The first is computational and was run for this manuscript: bounds, tipping points, sample sizes, and a Monte Carlo simulation of estimator bias. All code is in the paper folder (bounds.py, sim_dropout.py) and outputs are reproduced below. Every number in this section labelled “computed” is the output of that code. The second part is a proposed study that has not been performed: linkage of an existing long-term cohort to registries, tracing of a random sample of the remaining dropouts, and analysis with multi-state models and weighting (Figures 1 and 2).

Bounds and tipping points (computed)

Illustrative computation under stated assumptions — not empirical data. We applied the bounds of section 3.3 to published pooled figures. The inputs are the 93.0% survival and the 1,857 baseline versus 1,028 followed implants from the 2026 meta-analysis [7], which give a crude unresolved share π=1−1028/1857=0.446; the 92% survival and the 237 followed of 422 placed implants from the earlier 20-year meta-analysis [2], which give π=0.438; and, for context, the 10-year figures of 96.4% and 93.2% [1]. The crude π for the 2026 review treats every implant not counted as followed at 20 years as unresolved, which overstates π if some were resolved by failure or by documented death; it is an upper-end input.

Table 2. Computed bounds on 20-year survival and tipping-point failure risk among dropouts, using S_(obs)=0.93 except the last row. Simple bounds ignore failures observed before dropout.
Dropout share πLower boundUpper boundWidthTipping failure risk f* among dropouts for S=0.85
0.100.8370.9370.100(not computed)
0.200.7440.9440.2000.470
0.300.6510.9510.3000.337
0.446 (from [7] counts)0.5150.9610.4460.249
0.438 (from [2] counts, Sobs=0.92)0.5170.9550.438not computed

Three readings follow. First, the 78% figure obtained by imputation in the earlier review [2] lies inside the simple interval [0.517, 0.955], as expected, and the 93.0% figure sits near its upper end. Second, at a dropout share near 0.45 the worst-case lower bound is 0.515, which is uninformative, so published point estimates cannot be defended on the data alone. Third, the tipping point is more usable: for the 85% threshold to fail at π=0.446, dropouts need a 20-year failure risk of 0.249, about 3.6 times the 0.07 failure risk among followed patients; at π=0.30 the multiple is about 4.8. The 85% threshold is therefore robust to moderate informative dropout and not robust to strong informative dropout. The deaths-with-implant-in-situ adjustment narrows the intervals: at π=0.446 and a share d=0.5 of deaths among dropouts, the bounds on the “implant not lost before death or 20 years” estimand become [0.738, 0.961]; at d=0.75 they become [0.850, 0.961]. Whether a cohort’s dropouts are mostly deaths is therefore decisive, and it is knowable by linkage to a death register.

Monte Carlo simulation of estimator bias (computed)

Illustrative computation under stated assumptions — not empirical data. The simulation uses one implant per patient and 1,000 patients per replicate, 1,000 replicates, and a 20-year horizon. Assumed parameters: failure times are exponential with a 2.5-fold hazard ratio in a high-risk stratum (25% of patients), calibrated so that the net 20-year failure probability is 10.0%; death follows a Gompertz hazard with shape 0.10 per year, calibrated to 35% death before 20 years (computed truth: 34.99%); death is independent of failure. Baseline dropout is exponential, calibrated to 30% over 20 years before accounting for other events. Six scenarios were run:

  • S0: no dropout (administrative censoring only), a control that checks the estimators.
  • S1: non-informative dropout.
  • S2: dropout depends on the baseline stratum (2.5-fold higher hazard in the high-risk stratum), an observed-covariate mechanism.
  • S3: impending-failure dropout: 25% of patients whose implants fail before year 20 stop being observed, on average one year before failure (exponential lead time), on top of baseline dropout.
  • S4: as S3 with 50% of failures concealed.
  • S5: healthy-attender dropout: patients who never fail within 20 years drop out at twice the baseline hazard.

Estimators: 1 minus Kaplan-Meier with death and dropout censored (target: net failure, computed truth 10.00%); the Aalen-Johansen cumulative incidence (target: crude failure, computed truth 8.73%); Kaplan-Meier within baseline strata standardized to the baseline stratum distribution, which is equivalent in effect to weighting by the stratum-specific censoring probability (cf. [27, 28]); and a complete-case proportion defined as failures divided by patients with resolved status at 20 years or an observed failure (patients who died or dropped out intact are excluded).

Table 3. Simulation output: mean estimated 20-year failure probability in percent (bias in percentage points against the relevant computed truth) over 1,000 replicates. Illustrative computation under stated assumptions — not empirical data. Mean dropout before failure or death was 0% (S0), 25.2% (S1), 31.3% (S2), 26.9% (S3), 28.8% (S4), 42.2% (S5).
Scenario1 - Kaplan-Meier (truth 10.00)Cumulative incidence (truth 8.73)Stratified Kaplan-MeierComplete-case
S0 no dropout9.99 (-0.01)8.70 (-0.03)9.99 (-0.02)12.97 (+2.97)
S1 non-informative9.97 (-0.03)8.71 (-0.03)9.97 (-0.03)15.36 (+5.36)
S2 covariate-dependent9.53 (-0.47)8.34 (-0.39)9.99 (-0.01)15.51 (+5.50)
S3 25% failures concealed7.64 (-2.36)6.65 (-2.08)7.66 (-2.34)12.07 (+2.06)
S4 50% failures concealed5.10 (-4.91)4.44 (-4.29)5.12 (-4.88)8.27 (-1.73)
S5 healthy-attender11.85 (+1.85)10.22 (+1.49)11.82 (+1.82)20.68 (+10.68)

The simulation yields five readings, each conditional on the assumptions. (1) With no dropout and with non-informative dropout, 1 minus Kaplan-Meier recovers the net failure probability, so the estimator is sound when its assumption holds. (2) Dropout that depends on a baseline covariate biases the naive estimate by about half a point and weighting removes it. (3) Dropout that hides failures biases the estimate downward in proportion to the share concealed, by about 2.4 points at 25% and 4.9 points at 50%; stratified weighting does not help because the concealed information is not in the covariates. Failure was 10% by construction, so a 4.9-point bias halves the apparent failure risk. (4) Reversing the mechanism, with well-functioning implants dropping out, biases Kaplan-Meier upward in failure (survival downward) by 1.85 points. Both directions are therefore plausible and the net direction in a real cohort is an empirical question. (5) The competing-risk gap is the difference between the two truths, 1.27 points (10.00 minus 8.73), below the approximation in section 3.1; it is smaller than the dropout bias in S3 and S4 but not negligible compared with the 2-point decision threshold.

The complete-case column excludes patients who died with an intact implant, and so overstates failure even with no dropout (+2.97 in S0); its apparent improvement in S3 and S4 reflects two biases cancelling. Such figures can be wrong in either direction depending on mechanism. The simulation is not calibrated to any cohort, assumes independence of death and failure, one implant per patient, exponential failure times (implants do not necessarily have a constant hazard [6]), and fully known mechanisms. It demonstrates logic, not magnitudes in practice.

Proposed empirical study

Population. An existing cohort of implant patients with at least 20 years of potential follow-up and a documented attrition share above 30%, with identifiers permitting linkage. Examples are university or private-practice cohorts in countries with national personal identifiers and death registers; the proposal does not depend on a specific one. A parallel registry or insurance population in which implant removal is recorded (for example, reimbursement data) would serve as a comparison, subject to the validity of removal codes, which has not been established in the sources we found [12].

Step 1: linkage. Link all patients, including dropouts, to the national death register and to emigration records, and where available to national insurance or claims data to detect implant removal or replacement care elsewhere. Record for each dropout the date of last contact, the linked vital status and any removal code.

Step 2: tracing. Draw a simple random sample of dropouts who remain unresolved after linkage (alive, no removal code, no clinical contact), stratified if needed by year of dropout and by baseline risk (smoking, periodontitis history, implant location). Contact them and arrange examination or, if refused, obtain the treating dentist’s records with consent. The design follows precedents in other fields in which a probability sample of lost patients is traced and weighted back [18, 19], and efficiency can be improved by oversampling with a selection model [21].

Step 3: analysis. Implement the following in the order stated.

  • Estimands. Report net failure, cumulative incidence of failure with death competing, and the probability of a functioning implant in a living patient, each with 95% intervals, in line with recommendations for reporting competing-risk analyses [30]. Because Fine-Gray models can yield total failure probabilities that exceed one when used for several event types [31], absolute risks for the full set of events should come from cause-specific hazards or the multi-state model rather than from separate subdistribution models.
  • Multi-state model. States: functioning and attending; implant lost (observed); death with implant in situ; death after loss; unresolved. Transition intensities may depend on time since placement, age, and baseline covariates. Dropout enters as a transition to “unresolved” whose intensity is modeled jointly with failure; the tracing sample provides the information that identifies the link [25].
  • Inverse-probability-of-censoring weighting. Model the censoring hazard with baseline and time-varying covariates (for example, interval since last visit, last recorded probing depth or bone-loss measure, recorded complications) and weight patients by the inverse of the probability of remaining uncensored [27, 28]. Compare weighted Kaplan-Meier, weighted cumulative incidence and the tracing-based estimate. Prediction P5 states the expected pattern. Kaplan-Meier-based weighted regression methods offer alternatives for regression targets [32].
  • Tracing-sample weights. Each traced dropout carries a design weight equal to the number of unresolved dropouts it represents in its stratum divided by the number traced, adjusted for non-response among the sampled. The estimate is S=(1−π)S_(obs)+π (1−f) in the simplest case, with f the weighted failure proportion in traced dropouts (or its Kaplan-Meier analogue if tracing finds dates).
  • Tipping-point analysis for non-respondents. Tracing will not reach everyone. For the sampled dropouts who cannot be resolved, vary the assumed failure risk from the followed value up to a multiple of it, and report the multiple at which the conclusion changes (section 3.4).
  • Cluster handling. Patients with several implants contribute correlated outcomes; use patient-level clustering with a robust variance and report both implant-level and patient-level survival.

Controls. (a) A cohort with administrative follow-up and negligible attrition, to check that estimators agree when assumptions hold; (b) a negative-control outcome, such as death timing relative to dropout, to test whether dropout aligns with deteriorating health independent of the implant; (c) a positive control by simulating concealment of failures in the complete linked data, to confirm that the pipeline recovers a known bias.

Measurements and validity. Implant failure is defined as removal (the only outcome ascertainable from claims, linked records and telephone contact), with reasons recorded where possible; this does not capture implants with peri-implantitis that remain in function, so the study addresses survival, not success. Death is validated by register. Misclassification of removal in administrative data is a threat; a validation subsample with clinical examination estimates sensitivity and positive predictive value of removal codes.

Sample size for the tracing sub-study (computed)

Illustrative computation under stated assumptions — not empirical data. Let m be the number of sampled dropouts with resolved status, π the unresolved share, and p the failure proportion among traced dropouts. The variance of the overall estimate attributable to the traced fraction is approximately π^2p(1−p)/m (ignoring the variance of π, S_(obs), and finite-population correction). For a 95% half-width h on overall 20-year survival,

m=(z_0.975^2 π^2 p (1−p))/(h^2),  z_(0.975)=1.96.

Multiplying by a design effect of 1.5 for several implants per patient (assumed) and dividing by an assumed 70% success in resolving sampled dropouts gives the number to sample. Computed values (design effect 1.5 and resolution rate 70% assumed): for π=0.30, p=0.15, h=0.02, m=110 resolved patients, 165 after the design effect, and 237 to sample; for π=0.40, p=0.15, h=0.02, 196, 294 and 420; for π=0.40, p=0.15, h=0.01, 784, 1,175 and 1,680; for π=0.40, p=0.25, h=0.02, 288, 432 and 618; and for π=0.40, p=0.07, h=0.02, 100, 150 and 215.

A study that must decide whether dropouts differ from followed patients (rather than estimate the overall figure to a given precision) needs more: to detect a failure proportion of 0.12, 0.15 or 0.20 among dropouts against 0.07 among followed patients, with a two-sided 5% test and 90% power, the computed number of resolved patients per group is 721, 320 and 144; the implied shift in cohort survival at π=0.40 is 2.0, 3.2 and 5.2 points. Because the shift equals π times the excess failure risk among dropouts, a 2-point shift at π=0.40 corresponds to an excess of only 0.05 (5 percentage points of failure risk), and at π=0.20 to an excess of 0.10. These figures set the practical scale: a tracing study of a few hundred resolved dropouts can estimate the overall figure within about 2 points, but cannot reliably detect a 2-point shift as a difference between groups unless the excess risk among dropouts is large. The estimate-based design (precision on overall survival) is the more efficient framing.

Ethics, feasibility and bias control

Linkage and tracing require ethics review, a legal basis for use of identifiers, and in most jurisdictions consent or a waiver for contacting patients who have left a practice. Contact may itself change behavior (a prompted visit may detect failures earlier than otherwise), a known limitation of tracing designs. Bias control includes pre-specification of estimands and thresholds, blinded outcome assessment of traced patients where possible, documentation of all contact attempts, and reporting of the proportion of the sample that could not be resolved.

5. Competing explanations and how the design discriminates among them

Several mechanisms can produce the same pattern of published survival figures, and the design is built to separate them.

Dropout because of death or relocation unrelated to the implant. This produces little bias and a wide but unhelpful worst-case bound. Linkage to the death register separates death from other dropout and, through section 3.3, narrows the bounds. Prediction P3 is the test.

Dropout because of impending failure, with care elsewhere. This produces upward bias in survival. It is distinguished from the previous mechanism by tracing: the traced failure proportion among unresolved dropouts exceeds that among followed patients. Claims data on removal or replacement elsewhere add direct evidence.

Healthy-attender attrition. Patients without problems stop returning. It produces the opposite bias (S5) and can partly offset the previous mechanism; in the simulation the two have different signatures only when traced data are available. A cohort-level test is whether the dropout hazard is lower in patients whose records later show no failure, which requires tracing or linkage to know the later outcome.

Selection on baseline risk. High-risk patients (smokers, severe periodontitis) may drop out more. This is the observed-covariate mechanism, corrected by weighting (S2), and testable by comparing weighted and unweighted estimates.

Informative reintervention. Patients with a failing implant may receive a replacement and remain in the cohort, so retention rises after failure. This is also a risk of reverse dependence: retention becomes informative in the other direction, as in dependent failure and reimplantation processes [22]. The multi-state model includes a post-failure state to track it.

True differences in survival by cohort origin. Academic and general-practice cohorts differ in the mix of patients and procedures [10]. A difference between a retention-selected cohort [3] and a population sample [9] could reflect this rather than dropout. Linkage within a single cohort, comparing resolved with unresolved patients, removes this confounder.

Competing-risk artifact. Part of the discrepancy between 1 minus Kaplan-Meier and cumulative incidence is definitional, not bias. The paper reports both and states which question each answers, so a reader who prefers the net estimand, as argued in the Norwegian register analysis [17], and a reader who prefers the crude estimand can each find their number.

6. Clinical and engineering implications

These implications are conditional on the hypothesis being supported by traced data.

Reporting. Long-term implant papers could report, beside the Kaplan-Meier estimate, the share of patients unresolved at each horizon, the reasons for loss, the cumulative incidence with death as a competing event, and the simple bounds of section 3.3. A single figure with no attrition statement gives readers no way to judge its fragility. The reporting gap noted for trial flow diagrams [8] suggests that this is not standard practice.

Counseling. If the traced figure falls near the complete-case figure, clinicians can continue to quote 20-year survival with confidence; if it is materially lower, the wording should reflect an interval. Pending evidence, a defensible statement is that reported 20-year survival is 92% to 93% among patients who remain under observation [2, 7], and that the figure for all patients treated is lower by an amount that has not been measured.

Comparisons between implant types and techniques. Dropout that differs between arms would bias comparisons of survival even when the overall figure is little affected. Differential attrition should be tested and, where present, handled by weighting or tipping-point analysis. The Kaplan-Meier product-limit estimator [33] remains the right tool for net comparisons when censoring is non-informative; the point here is to check that condition, not to abandon the method.

Registry and payer design. Population registers with linkage to death and removal records would remove most of the attrition problem at source. A registry that records implant removal is a precondition; validity of claims-based removal codes against charts has not been established in the sources we found and would need a dedicated substudy [12].

Device and material evaluation. For engineering endpoints such as fracture or screw loosening, patients who return with a mechanical complication to another clinic are missing from the original clinic’s records. Cause-specific analysis separates biological from mechanical loss, which was reported for fewer than half of failures in the most recent pooled analysis [7].

7. Limitations

  • No data. The paper contains no empirical analysis. The simulation uses assumed values and cannot show the size of the bias in any real cohort.
  • Simulation scope. One implant per patient, independent death and failure, exponential failure times, a single dropout mechanism at a time, and no time-varying covariates. Real cohorts have clustered implants, age-dependent death associated with oral health, and non-constant hazards [6].
  • Crude inputs for bounds. The dropout share from the 2026 meta-analysis was computed from two counts whose definitions we could not verify from the abstract [7]. Summary bounds applied to pooled figures ignore between-study heterogeneity and the fact that studies differ in attrition.
  • Simple bounds are conservative. Time-refined bounds would be narrower. We report the simple form because it needs only published quantities.
  • Abstract-level appraisal. Full texts were not read. Claims about the content of cited studies are limited to what their abstracts state. Statements about the arthroplasty literature depend on abstracts that may omit nuance.
  • Search limits. PubMed, Europe PMC and ClinicalTrials.gov were searched; Embase, Scopus and Web of Science were not accessible. Dropout-tracing work in implant cohorts may exist in the grey or unindexed literature.
  • The threshold of 2 points is arbitrary and the hypothesis H1 is conditional on it. A different threshold changes the verdict, though not the structure of the argument.
  • Mechanism unproven. There is no direct evidence that patients with failing implants stop attending. The opposite mechanism, in which failure increases attendance, is plausible and could produce bias in the other direction.
  • Tracing itself can bias. Contact can trigger visits and detect failures that would otherwise be missed; non-response among the traced remains informative.
  • Estimand disagreement. Whether the cumulative incidence or the net probability is the right target is disputed [17] and the paper does not settle it.

8. Conclusions

Twenty-year implant survival figures are conditional on who remains under observation. Simple bounds from published attrition give intervals that are wide (more than 40 points at the attrition seen in pooled 20-year analyses), and the tipping-point calculation shows what must be believed about the dropouts for an 85% claim to fail. Informative dropout can bias Kaplan-Meier in either direction, weighting by recorded covariates cannot repair dependence on unobserved impending failure, and the competing-risk discrepancy is a separate, smaller effect when failure is rare. Only linkage and tracing of a sample of dropouts can identify the figure. A tracing sample of a few hundred resolved dropouts would estimate overall survival to within about 2 points under the stated assumptions. The concern would be unfounded if traced dropouts fail at close to the rate of followed patients.

Cite this paper

Jain S, Gupta A. How Long Do Dental Implants Really Last? Informative Dropout, Competing Mortality, and Bounds on Twenty-Year Survival. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/long-term-survival-informative-dropout

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