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Do Proton Pump Inhibitors, Antidepressants, and Antihypertensives Affect Dental Implant Survival? A Target-Trial Emulation Protocol with Active Comparators and Negative Controls

Paper type
Study Protocol (observational causal inference)
Status
Original Work · Working Paper
Keywords:
dental implants · target trial emulation · proton pump inhibitors · selective serotonin reuptake inhibitors · antihypertensive agents · immortal time bias · negative controls
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. Retrospective cohorts report that proton pump inhibitor (PPI) users and selective serotonin reuptake inhibitor (SSRI) users lose more dental implants, and that users of antihypertensive drugs lose far fewer. Most of these estimates come from a small number of single-center cohorts that defined exposure as ever versus never, analyzed implants rather than patients, and did not address confounding by indication, exposure timing, immortal time, or healthy-user selection. Adjusted pooled estimates are weaker or null, and some effect sizes are implausibly large.

Objective/Hypothesis. To specify, for each drug class, the hypothetical randomized trial and the observational emulation that would separate a drug effect from its confounders. We hypothesize that under new-user, active-comparator, time-zero-aligned analysis the hazard ratio (HR) for biological implant failure will be below 1.5 for PPI versus H2-receptor antagonist initiators and for SSRI versus non-serotonergic antidepressant initiators, and that the reported antihypertensive benefit (HR at or below 0.6) will not persist.

Proposed approach. Three target-trial specifications (eligibility, strategies, assignment, time zero, follow-up, outcome, contrast, analysis); linked dental and pharmacy records; inverse-probability weighting with cluster-robust variance; cause-specific and subdistribution analysis for death; negative-control outcomes and exposures; E-values; and a time-to-event sample-size calculation. Under stated assumptions, 191 events are needed to exclude HR 1.5 at one-sided alpha 0.025 with 80% power (1:1 allocation), corresponding to roughly 1,900 patients at 10% failure risk. An illustrative simulation shows that ever/never exposure definitions can produce a spurious rate ratio near 0.4 under a true null.

Expected contribution. A registrable, falsifiable analysis plan with numbered predictions and refuting results, and an inventory of what current registries lack.

Conclusions. Existing evidence cannot distinguish drug effects from patient selection. The protocol states what data and analyses could.

1. Introduction

Clinicians planning implant therapy are often told that patients who take a PPI or an SSRI carry extra risk of implant loss, and that patients who take antihypertensive drugs carry less. These statements circulate through consent discussions, review articles, and, in psychiatry, through recommendations to educate antidepressant users about implant failure [1]. A 2026 scoping review of 51 studies concluded that prolonged PPI use and SSRI use are associated with implant failure or marginal bone loss, and that antihypertensive drugs have no effect on implant outcomes [2]. Those two conclusions about antihypertensives and about PPIs and SSRIs sit uneasily beside the primary studies, in which the antihypertensive literature reports the largest effects of all, but in the protective direction.

The common weakness is design, not data volume. A drug is a marker of a disease, and disease and its treatment are tangled with age, frailty, smoking, periodontal status, bruxism, and health-seeking behavior. Pharmacoepidemiology has well-developed tools for this problem: the target trial framework, which forces an observational analysis to state the randomized trial it imitates [3, 4]; new-user, active-comparator designs [5, 6]; recognition of time-related biases [7, 8]; negative controls [9]; and quantitative sensitivity analysis [10]. A reporting statement for studies that emulate a target trial was published in 2025 [11].

This manuscript is a study protocol. No data were collected or analyzed. We (a) appraise, at abstract level, the evidence behind the three drug-class claims; (b) test the novelty of the proposal by searching for implant studies that already used these designs; (c) specify three target trials and their emulations; (d) derive sample-size requirements from failure risks reported in the sources we read; (e) illustrate by simulation how an ever/never exposure definition can manufacture protection under a true null; and (f) state predictions and the results that would refute them.

The aim is limited. We do not claim that the drugs are harmless or protective; a modest effect could exist and be hidden by comparator choice or imprecision.

2. Background and critical appraisal of the evidence

Origin of the claims

The PPI and SSRI claims trace to cohorts from two research groups in the mid-2010s. A cohort of 490 patients and 916 implants, of whom 51 were SSRI users, reported more failures in users (10 of 94 implants versus 38 of 822), with dose and duration unavailable [12]. A companion cohort of 799 patients and 1,773 implants, with 58 PPI users, reported implant failure of 6.8% versus 3.2% and an HR of 2.73 (95% CI 1.10 to 6.78) [13]. A Malmö cohort of 999 patients and 3,559 implants treated between 1980 and 2014 reported 12.0% versus 4.5% and an HR of 2.81 (1.14 to 6.94) [14]. The two PPI cohorts agree closely, but their confidence intervals have lower limits near 1.1, and both defined exposure as use recorded in the chart. In the Malmö cohort, treatment began in 1980, before PPIs were in wide use; this is our inference from the study period, and it implies that much of the unexposed implant experience predates the exposure being studied.

The antihypertensive claim began with a cohort of 728 patients and 1,499 implants in which failure was 0.6% in users and 4.1% in non-users, giving an HR of 0.12 (0.03 to 0.49) [15]. A reduction of 88% in failure from antihypertensive drugs is a large effect for any drug class, and the same cohort’s magnitude deserves explanation before it is accepted.

Independent re-tests

PPI. A US veterans cohort of 284 patients and 933 implants found an adjusted odds ratio of 0.80 (0.56 to 1.15) [16]. A study of 270 patients and 1,118 implants found no association for PPIs, SSRIs, or antihypertensive drugs [17]. A cohort of 687 patients and 2,971 implants found significance at the implant level (5.4% versus 3.5%, p = 0.03) but not the patient level (19.3% versus 14.3%, p = 0.16) [18]; an earlier study showed the same split (p = 0.002 versus 0.094) [19]. Significance that appears when implants are treated as independent and disappears when patients are the unit is what unaddressed clustering produces. One study found more crestal bone loss in PPI users [20]. A 2025 meta-analysis of eight studies pooled crude data to an odds ratio of 2.71 (1.72 to 4.29; I2 = 63%) but adjusted data to 1.44 (0.92 to 2.24; I2 = 73%), with 1.71 (1.17 to 2.50) after excluding one outlier; the authors judged the results unstable [21]. An earlier International Team for Implantology review pooled two studies [22].

SSRI. A cohort of 931 implants in 300 patients found crude failure of 12.5% versus 3.3% in SSRI users, but multivariable analyses were null (generalized estimating equation p = 0.530; multilevel p = 0.125) [23]. A Mayo cohort of 5,456 patients followed for 20 years, with the best exposure timing among the studies we read, found an elevated HR only for a history of sertraline use (1.60; 1.15 to 2.23), not for active SSRI use [24]. A cohort of 771 patients and 1,820 implants reported 6.3% failure in SSRI users versus 3.9% in non-users, but 31.3% in SNRI users and 33.3% in tricyclic users (odds ratios 11.1 and 12.2) [25]. Effects that grow as serotonin selectivity falls do not follow from a serotonin-transporter mechanism, and cells were small. A 2025 report of 1,611 subjects described 18.6% versus 6.7% failure at one year with bivariate analysis only [26]. One study was non-significant [27], and another mixed screw loosening and fracture with biological failure [28]. A cluster analysis linked both antidepressant use and bruxism to clustered failures within patients [29]. Meta-analyses reported a risk ratio of 2.44 at the patient level and 2.34 at the implant level with I2 = 0% [30], and addressed antidepressants broadly [31]. A 2026 psychiatric commentary summarized unadjusted failure of 6% to 23% in users versus 2% to 8% in non-users and stated that cause and effect cannot be inferred from the designs reviewed [1].

Antihypertensives. A 2026 cohort of 655 analyzed patients (74 on antihypertensives, 40 on lipid-lowering drugs, 29 on antidepressants) reported an HR of 0.23 for antihypertensive users and, per the notes we used, 0.16 for lipid-lowering users [32]. A near-identical benefit for two unrelated drug classes suggests a shared selection process, not two pharmacologic effects. A cohort of 264 patients and 554 implants found an odds ratio of 0.26 (0.08 to 0.91) for early failure with antihypertensive use, but hypertension itself was associated with late failure (HR 2.1; 1.3 to 3.3) [33]. After sinus augmentation, beta-blockers were associated with higher early failure (odds ratio 4.05) and other classes were null [34], whereas a rat study found propranolol enhanced osseointegration [35]. Renin-angiotensin inhibitors were associated with slightly higher implant stability quotients (+3.6) [36]. A systematic review found only two survival studies, too few for drug-specific conclusions [37].

What the pattern tells us

The crude PPI and SSRI signals replicate; the adjusted signals mostly do not. The antihypertensive benefit has consistent direction but implausible magnitude. We offer five explanations, each testable.

First, confounding by indication. PPI users have reflux, polypharmacy, older age, and comorbidity; one cohort listed older age, ASA class 3, diabetes, and osteoporosis as more common among users [18]. SSRI users have depression, which carries its own risks, and the literature on SSRI effects in other outcomes already identifies confounding by indication and severity as a recurring explanation [38]. Bruxism and depression may both lie on the path from drug to mechanical overload.

Second, prevalent-user and selection bias. Statin and fracture studies show the pattern: pooled observational data suggested a 25% lower fracture risk (relative risk 0.75), adjusting for preventive service use barely moved it, yet moderate selection bias from prevalent users could eliminate the association [39]. That finding is from another field, but the mechanism of healthy-user and prevalent-user selection does not depend on the outcome. Antihypertensive drugs show class-specific fracture associations in observational data [40], which should caution against a single protective class effect.

Third, immortal and misclassified person-time. If a chart-review study classes patients as users when a drug appears anywhere in the record, person-time before initiation is credited to the exposed group, although failure there could not occur “on drug” [7, 8]. We searched Europe PMC full text for immortal time in the implant literature and found no applied analysis; one hit was a 2026 methods primer on cohort studies in periodontology [41].

Fourth, clustering: several studies analyzed implants as independent units, and the implant-versus-patient split above is the expected symptom. Fifth, outcome definition: studies mix early failure, late failure, bone loss, screw loosening, and prosthetic fracture.

Originality check

We searched PubMed under several vocabularies for implant studies that used target-trial emulation, new-user or active-comparator designs, propensity scores with time-varying exposure, claims or registry replications, or time-varying exposure with competing risks. Queries combining implant terms with these methods returned no relevant implant study. Europe PMC queries (implant with target trial; implant with immortal time; PPI implant claims; SSRI implant active comparator) returned the 2026 methods primer and unrelated material [41]. A registry listing on ClinicalTrials.gov describes a retrospective case-control study of PPIs and implant survival with 54 participants (NCT06848855) and another observational listing concerns peri-implantitis and medications (NCT04783974). A nested case-control study with risk-set sampling, published in 2026, studied diabetes, periodontitis, and other risk factors for implant failure, with 550 failed implants in 328 subjects and 1,156 control implants in 502 subjects, and reported a periodontitis odds ratio of 12.82 [42]. It improves on the earlier cohorts in sampling but is a risk-factor study, not a drug-comparison emulation. Statin, antihypertensive, and antidepressant claims therefore remain untested by any design we found that addresses the biases above. This is a statement about our search (PubMed, Europe PMC, ClinicalTrials.gov; abstract level), not about the whole literature. Embase, Scopus, and Web of Science were not accessible.

Population registers exist that could support such analyses. Swedish data have been used to study early and late implant loss at the population level [43], and Korean national insurance data have been used to study implant removal rates in older adults [44]. A Korean multicenter study has also shown that PPI exposure and fracture outcomes can be analyzed across databases converted to a common data model [45]. These sources show that dental procedure data, pharmacy data, and common data models exist; we found no study linking them for the questions in this protocol.

Table 1. Pivotal studies, design, main bias, and evidence level (abstract-level appraisal). Evidence levels are operational categories used in this manuscript, not GRADE: A strong; B moderate; C preliminary; D mechanistic or theoretical; E speculative. CI, confidence interval; HR, hazard ratio; OR, odds ratio.
StudyDesign and sizeReported resultMain biasLevel
Wu 2017, PPI [13]Cohort; 799 patients, 1,773 implants, 58 usersFailure 6.8% vs 3.2%; HR 2.73 (1.10 to 6.78)Ever-use exposure; implant-level; indicationC
Chrcanovic 2017, PPI [14]Cohort; 999 patients, 3,559 implants, 1980 to 2014Failure 12.0% vs 4.5%; HR 2.81 (1.14 to 6.94)Study period precedes wide PPI use; indicationC
Rogoszinski 2022 [16]US veterans; 284 patients, 933 implantsAdjusted OR 0.80 (0.56 to 1.15)Selected population; user and non-user differences in smokingC
Masri 2023 [18]Cohort; 687 patients, 2,971 implantsImplant level 5.4% vs 3.5% (p = 0.03); patient level 19.3% vs 14.3% (p = 0.16)Clustering; indicationC
Tang and Xie 2025 [21]Meta-analysis; 8 studiesCrude OR 2.71; adjusted OR 1.44 (0.92 to 2.24)Heterogeneity; pooled confounded estimatesB
Wu 2014, SSRI [12]Cohort; 490 patients, 916 implants, 51 users10 of 94 vs 38 of 822 implants failedSmall numbers; no dose or durationC
Chrcanovic 2017, SSRI [23]Cohort; 300 patients, 931 implantsCrude 12.5% vs 3.3%; multivariable nullSingle center; SSRI-only usersC
Carr 2019 [24]Cohort; 5,456 patients, 20 yearsSertraline history HR 1.60 (1.15 to 2.23); active use not associatedNo active comparator; depression unmeasuredB
Hakam 2021 [25]Cohort; 771 patients, 1,820 implantsSSRI 6.3% vs 3.9%; SNRI 31.3%; tricyclic 33.3%Small cells; implant-levelC
Wu 2016, antihypertensives [15]Cohort; 728 patients, 1,499 implantsFailure 0.6% vs 4.1%; HR 0.12 (0.03 to 0.49)Healthy-user and immortal time suspectedC
Chidiac 2026 [32]Cohort; 655 analyzed patientsHR 0.23 (antihypertensive); 0.16 (lipid-lowering) per notesSame benefit for unrelated classesC
Vilela 2026 [33]Cohort; 264 patients, 554 implantsEarly failure OR 0.26 (0.08 to 0.91); hypertension late failure HR 2.1Disease and drug effects opposedC

3. Hypothesis and theoretical framework

Formal statement

Let A denote the treatment strategy assigned at time zero, Y^a the potential time to biological implant failure under strategy a, and D death before failure. For each drug question q we define the contrast

HR_q=(λ_1(t))/(λ_0(t))

where λ_a(t) is the hazard of implant failure at time t since time zero under strategy a, in the population that would be eligible for the target trial, and the hazard is a cause-specific hazard (death is a competing event). The marginal risk contrast over a horizon τ is Pr(Y^1≤τ)−Pr(Y^0≤τ), estimated with the subdistribution or cumulative-incidence approach described in Section 4.

Central hypothesis (H1). In emulations that use new users, an active comparator, and time zero aligned with treatment initiation, HR_(PPI vs H2RA)<1.5 and HR_(SSRI vs non-serotonergic)<1.5, where “below 1.5” means the upper limit of the 95% confidence interval is below 1.5 (Section 4.9). This is a non-inferiority-style hypothesis: it says that any harm is smaller than the magnitude suggested by the crude cohorts, not that harm is zero.

Antihypertensive hypothesis (H2). In new-user comparisons of renin-angiotensin inhibitors with calcium-channel blockers or thiazide diuretics, HR>0.6 (lower limit above 0.6), and negative-control drugs show comparable “protection” in naive ever/never analyses, which disappears under the same design.

The thresholds are decision values, not biological constants, and can be revised before registration. The value 1.5 excludes a doubling while remaining compatible with a modest effect; 0.6 keeps well away from the HR of 0.12 to 0.26 reported in single-center cohorts [15, 32] while allowing moderate benefit.

Causal structure

Figure 1 shows the structure we assume. An unmeasured or poorly measured set U (indication, frailty, depression severity, bruxism, smoking, periodontal status, health-seeking behavior) affects both treatment and failure. The drug may affect failure directly (the effect of interest) and may also increase mechanical loading indirectly (for example by altering bruxism), which we regard as part of the total effect, not as confounding. Death and loss to follow-up compete with the outcome.

Active comparison attacks the U→A path by choosing a comparator treated for the same indication. It does not remove it: patients started on a PPI instead of an H2-receptor antagonist (H2RA) differ in indication severity, and the difference is time-dependent (practice patterns changed as PPIs displaced H2RAs). Negative controls address residual U by asking whether a bias path predicts an outcome the drug cannot plausibly cause.

Assumptions

The causal contrast is identified under the following assumptions, each of which the protocol tests or bounds.

  • Conditional exchangeability. Given measured covariates, initiators of the two strategies have the same potential failure hazards. Threatened by unmeasured depression severity, bruxism, reflux severity, and hygiene. Addressed by active comparison, negative controls, and E-values.
  • Positivity. Every covariate stratum includes both strategies. Threatened for SSRI versus non-serotonergic comparators in elderly patients and for H2RA initiators in recent years.
  • Consistency and well-defined strategies. “Initiate a PPI” must correspond to a defined regimen. Dispensing records define initiation, not adherence; we therefore specify an intention-to-treat-like effect of initiation and a per-protocol effect of sustained use, estimated with censoring weights.
  • Outcome recorded independently of drug history. Threatened if clinicians remove implants earlier in patients on drugs perceived as risky, a mechanism by which published warnings could generate their own confirmation. Addressed by outcome validation and by separating early from late failure.
  • Correct time zero. Treatment assignment, eligibility, and start of follow-up coincide (Section 4.3).

Why immortal time arises, with a bound

Suppose implants are placed at time 0 and failure occurs at a constant hazard λ regardless of drug. A patient who starts the drug at time s>0 and is classed as an “ever user” contributes person-time [0,s) to the exposed group even though they were unexposed during it. Because the label required the implant to survive until s, the exposed group carries no failures in that interval. If a fraction π of patients start the drug at a time uniform on (0,T), the naive rate ratio falls below 1 even though the true ratio is 1. Section 4.8 reports a simulation that quantifies it under stated parameters. The mechanism is not a property of one drug and therefore predicts the same spurious “protection” for any drug class whose start dates are scattered through follow-up. That prediction is falsifiable, because the naive analysis can be run on negative-control drugs.

Quantitative bias bounds

The E-value is the minimum strength of association, on the risk ratio scale, that an unmeasured confounder would need to have with both treatment and outcome to fully explain an observed risk ratio, conditional on measured covariates [10]. For an observed risk ratio RR≥1 it is

E=RR+√(RR (RR−1))

and for RR<1 one first takes 1/RR. The same quantity is applied to the confidence limit closer to the null. We computed E-values for published estimates (Table 3); they are used in two ways: to ask how strong confounding would have to be to explain published crude estimates, and, in the future analysis, to report the robustness of the emulated estimates.

Predictions and refuting results

P1. In the PPI-versus-H2RA new-user emulation, the HR for patient-level biological failure will be closer to 1 than the crude ever/never HR (about 2.7 in the two original cohorts [13, 14]), and its upper confidence limit will be below 1.5. Refuted if the HR is at least 1.5 with a lower limit above 1.0 and a dose-duration gradient.

P2. In the SSRI-versus-bupropion/mirtazapine emulation, the HR will have an upper limit below 1.5. Refuted if the HR is at least 1.5 with lower limit above 1.0 and a dose-response, which is what a serotonin-transporter mechanism would predict.

P3. SNRI and tricyclic initiators will not show failure hazards of the magnitude reported in a single cohort (odds ratios of 11 to 12 [25]) once compared with other antidepressant initiators and analyzed at patient level. Refuted if the effect persists with confidence limits excluding 3.

P4. In the antihypertensive new-user emulation, the HR for renin-angiotensin inhibitors versus calcium-channel blockers or thiazides will exceed 0.6 (lower limit). Refuted if the HR is 0.6 or lower with an upper limit below 1.0 in new users with time-varying exposure and absent for negative-control drugs.

P5. Naive ever/never analyses of negative-control drugs in the same data will show HRs below 1, and the aligned analyses will not. Refuted if negative-control drugs show no naive “protection” (which would mean immortal time is not the main artefact) or show protection under the aligned design (which would mean residual healthy-user bias).

P6. Implant-level analyses without clustering adjustment will give narrower confidence intervals than patient-level analyses by a factor consistent with the design effect 1+(m−1)ρ, where m is implants per patient and ρ the within-patient correlation of failure. Refuted if the interval widths do not differ, which would mean clustering is not the explanation for the implant-versus-patient split seen in two PPI cohorts [18, 19].

P7. The mechanical-complication outcome will track bruxism and depression indicators more than drug class. Refuted if it is unrelated to bruxism, in which case it fails as a pathway indicator.

P8. The association between prevalent drug use at implant placement and failure will exceed that for new users, in the direction of the crude literature (prevalent-user selection). Refuted if the prevalent-user and new-user estimates agree.

P9. Future-initiation falsification: drug initiation after the failure date will show no association with failure. Refuted if it shows an association, which would indicate unmeasured confounding by patient characteristics.

P10. E-values for the emulated estimates will be lower than the E-values of the crude published estimates (4.9 and 5.1 for the two PPI cohorts, by our calculation in Table 3), reflecting attenuation. Refuted if the emulated E-values are as large.

A pre-specified combined reading follows. If P1, P2, and P4 hold and P5 and P8 hold, the original associations are more plausibly artefacts of selection and exposure definition. If P1 or P2 fail with a dose gradient and a null negative-control result, a drug effect is credible and warrants a randomized or mechanistic test.

Mechanisms are not the focus

Proposed mechanisms (for example altered mineral absorption with PPIs, serotonin signaling in bone cells with SSRIs, renin-angiotensin and adrenergic effects on bone remodeling) are conceivable and have been reviewed, including whether SSRIs cause fractures [46] and serotonin and bone [47]. We did not appraise the primary mechanistic literature, and the design does not depend on it. Mechanism matters only for choosing comparators, for dose-duration predictions, and for the outcome window: a drug that impairs osseointegration should act early, one that promotes bone loss should act late.

4. Proposed methodology

Overall design

We propose three parallel target-trial emulations in one linked data platform, sharing a common implant cohort, covariate dictionary, and analysis code. The questions are PPI versus H2RA (Q1), SSRI versus non-serotonergic antidepressants (Q2), and renin-angiotensin inhibitors versus calcium-channel blockers or thiazide diuretics (Q3). The framework follows the structure recommended for target-trial emulation, which states the protocol of the trial first and then the way each component is emulated [3, 4], and the study would be reported against the TARGET statement [11]. Table 2 gives the specification.

Table 2. Target-trial specification and emulation for the three questions. H2RA, H2-receptor antagonist; IPW, inverse-probability weighting; RAS, renin-angiotensin system; CCB, calcium-channel blocker.
ComponentQ1: PPI versus H2RAQ2: SSRI versus non-serotonergic antidepressantQ3: RAS inhibitor versus CCB or thiazide
Eligibility (trial)Adults with at least one osseointegrated or newly placed implant; indication for acid suppression; no PPI or H2RA in prior 365 daysAdults with at least one implant; new depressive or anxiety episode needing pharmacotherapy; no antidepressant in prior 365 daysAdults with at least one implant; newly treated hypertension; no antihypertensive in prior 365 days
Treatment strategiesInitiate and continue a PPI for at least 1 year versus initiate and continue an H2RAInitiate and continue an SSRI versus initiate and continue bupropion or mirtazapineInitiate and continue an ACE inhibitor or ARB versus a CCB or thiazide
AssignmentRandomized, unblinded in trial; emulated by IPW on baseline covariatesSameSame
Time zeroFirst qualifying dispensing (post-loading variant); implant placement date with recent-initiator definition (placement variant)SameSame
Follow-upFrom time zero to failure, death, last dental contact, strategy deviation (per-protocol), or 10 yearsSameSame
OutcomePatient-level biological failure: removal for loss of osseointegration or peri-implantitis; early (<1 year after placement) and late separatelySameSame
Causal contrastIntention-to-initiate HR and per-protocol HR; 5-year risk differenceSameSame
AnalysisCox and pooled logistic models with IPW; cause-specific hazards and cumulative incidence for death; cluster-robust varianceSameSame

Why two variants of time zero

Implants are placed once, but drug starts occur at any time. A single “time zero” cannot serve both questions the literature has asked. The first question is whether a drug on board at placement impairs osseointegration (early failure). The second is whether starting a drug after loading increases late failure through bone loss or peri-implantitis. We therefore specify two variants.

Placement variant. Time zero is the implant placement date. Patients are eligible if they initiated one of the two strategies within a fixed window before placement (for example, first dispensing 30 to 365 days earlier) with no use in the 365 days before that first dispensing, and are still on treatment at placement. This defines “recent initiators at placement”, all of whom were at risk of the outcome only after time zero, so no outcome-free time is credited. Early failure (first year) is the primary outcome.

Post-loading variant. Time zero is the first dispensing of the study drug in patients who already have a functioning implant at least 3 months after loading. Because implants have different ages at time zero, implant age is handled as a stratification factor or as delayed entry. Late failure and peri-implantitis-related removal are the outcomes.

Both variants avoid defining exposure from information that arrives after time zero. Figure 2 shows the alignment.

Immortal-time and prevalent-user control

Three rules prevent the misalignment described in Section 3.4. First, eligibility is assessed only with information available at or before time zero. Second, exposure is defined at time zero as the strategy initiated, not as use observed over follow-up. Third, a prevalent-user analysis (patients on the drug for more than 365 days at implant placement) is run separately and compared with the new-user estimate; the difference is a direct measure of prevalent-user selection, in line with published guidance on new-user designs [6] and on time-origin definitions [8]. A grace period of 90 days after time zero is used for per-protocol analyses in which patients may switch.

Prevalent-user estimates remain informative about a patient who has long taken the drug and arrives for implant planning, so we treat them as a second estimand.

Active comparators

Active comparators are chosen to share indication and to differ in the pharmacologic feature under test.

  • Q1. H2RAs treat acid-related disease but lack the profound acid suppression of PPIs. A drawback is that H2RA initiators are now few and may be milder cases. Sensitivity analyses restrict to patients with objectively documented upper-gastrointestinal indication codes in both arms and to calendar periods when both drugs were widely used.
  • Q2. Bupropion and mirtazapine lack primary serotonin-transporter inhibition, but each carries its own confounding (mirtazapine is sedating; bupropion is used for smoking cessation), so we run them separately and pooled. SNRIs and tricyclics are reported as separate secondary contrasts. A contrast with diagnosed depression treated by psychotherapy only addresses depression itself, at the cost of confounding by treatment choice.
  • Q3. Renin-angiotensin inhibitors versus calcium-channel blockers or thiazides, common first-line alternatives. Hip-fracture associations differ among antihypertensive classes [40], so comparator-specific results are reported. Beta-blockers are analyzed separately given discordant human and animal reports [34, 35]. Statin versus ezetimibe is a secondary lipid-lowering contrast.

Data-source requirements and registry gaps

The analysis needs, for each patient: (a) pharmacy dispensing records with date, drug, strength, and days supplied; (b) dental procedure records with implant placement, loading, and removal dates, and tooth or site; (c) a unique patient identifier across both; (d) enough covariate detail to approximate U; and (e) mortality data. Such sources exist in some national insurance and register systems, as the Swedish study of implant loss [43], the Korean analysis of implant removal in older adults [44], and common-data-model work on PPI exposure and fracture [45] indicate. We did not find a study that links dental implant events to drug dispensing for the questions here.

What current sources are likely to lack:

  • Reason for implant removal: claims record removal, not whether the cause was failed osseointegration, peri-implantitis, fracture, or patient choice; chart validation of a sample is needed.
  • Periodontal and hygiene status, the strongest known confounders (periodontitis odds ratio 12.82 in one study [42]).
  • Bruxism and depression severity, relevant to Q2, and smoking, often missing in claims.
  • Over-the-counter PPI and H2RA use, missed by dispensing records and biasing toward the null.
  • Dental coverage: where implants are not reimbursed, the cohort is selected by income.

Where implants are not captured in claims, a linked clinic network or university hospital system with electronic dental records and prescription feeds is the alternative. A pilot in such a system is a necessary feasibility step.

Confounding control and clustering

Baseline covariates are selected a priori from causal reasoning (Figure 1), not from significance: age, sex, calendar year, comorbidity index, diabetes, osteoporosis therapy, immunosuppressive medication, smoking, periodontitis history, bruxism, depression or reflux severity proxies, number and site of implants, jaw, surgeon or clinic, polypharmacy, and health-service use in the prior year (a proxy for health-seeking). We estimate propensity scores for the initiated strategy, use stabilized weights, and examine overlap before trimming.

Patients with several implants contribute correlated outcomes. The primary analysis is at the patient level (time to first biological failure). Secondary implant-level analyses use marginal models with a cluster-robust variance estimator at the patient level, and include implant covariates (site, length, loading protocol). The expected variance inflation is described by the design effect 1+(m−1)ρ. With m=2.2 implants per patient, which is the ratio in one PPI cohort (1,773 implants in 799 patients [13]), the factor is 1.12 at ρ=0.1 and 1.36 at ρ=0.3; at m=3.6 (3,559 implants in 999 patients [14]) and ρ=0.3 it is 1.78 (python-checked; see Section 4.9). The within-patient correlation ρ is an assumed value, not an estimate from the sources.

Competing risk of death and censoring

Death removes implants from risk without failure and is common in elderly patients treated for reflux, depression, or hypertension. We estimate the cause-specific hazard of failure (the biological question) and the cumulative incidence of failure accounting for death (the prognostic question). Austin and colleagues show that cumulative failure probabilities from separate Fine-Gray models for several event types can exceed 1 [48]; we therefore use the cause-specific hazard ratio as the etiologic contrast and subdistribution models only for risk-scale summaries. Loss to follow-up is handled with censoring weights.

Negative controls and falsification

Negative controls (outcomes or exposures that cannot plausibly be affected by the drug) detect residual bias [9]. We specify four.

Negative-control outcomes. (i) Non-implant dental events unrelated to bone biology, for example restoration of unrelated teeth or routine prophylaxis attendance, as indicators of health-seeking behavior. (ii) Prosthetic complications (screw loosening, veneer fracture). This is not a clean negative control: such complications track bruxism and loading, and in cluster analyses bruxism was associated with clustered failure [29]. We therefore treat it as an indicator of the bruxism pathway. If SSRI users have more prosthetic complications than the comparator, that points toward residual confounding or mediation by bruxism rather than toward a bone effect.

Negative-control exposures. Chronic drugs without an established bone mechanism, started for conditions of similar chronicity and prevalence (candidates to be vetted by a clinical pharmacologist before registration, for example tamsulosin or allopurinol). The same naive and aligned analyses are run for them. If a negative-control drug shows “protection” in naive ever/never analysis, as P5 predicts, the artefact is shown in the data themselves.

Future-initiation falsification. Drug initiation after the failure date cannot cause the failure; an association points to patient characteristics.

Positive control. Smoking or periodontitis as exposures should reproduce the known direction of effect [42]; if they do not, the outcome ascertainment is inadequate.

Sample size and power

Question: how many events and patients are needed to exclude an HR of 1.5 in favor of equal hazards? For a two-arm comparison with allocation fraction p to the exposed arm, a one-sided type I error α, and power 1−β, Schoenfeld’s approximation gives the number of events

D=((z_(1−α)+z_(1−β))^2)/(p(1−p) (lnHR_m−lnHR_a)^2)

where HR_m is the margin (1.5) and HR_a the assumed true HR (1.0). The number of patients is N=D/r, where r is the average cumulative probability of patient-level failure over follow-up, inflated by 1.25 for propensity-weighting variance and divided by 0.9 to allow for 10% loss to follow-up or competing death.

Failure risks come from the sources we read, with the caveat that they are crude and population-specific: 14.3% at the patient level in PPI non-users at 687 patients [18]; implant-level failure of 3.2% to 4.5% in non-users in the two PPI cohorts [13, 14]; and 6.7% at one year in SSRI non-users in one report [26]. We therefore compute the requirement for average patient-level risks of 5%, 10%, and 15%. We computed these values with the script calc35.py, saved with this manuscript; Table 3 reproduces its output.

Table 3. Illustrative computation under stated assumptions, not empirical data. Events and patients needed to exclude HR 1.5 (true HR 1.0; one-sided alpha 0.025; power 0.80), and E-values for published estimates. N inflated by 1.25 and divided by 0.9. CI limit E-value is for the confidence limit nearer the null (1.00 if the interval includes 1).
ScenarioEvents requiredN at 5% riskN at 10% riskN at 15% risk
1:1 allocation1915,3052,6521,768
1:3 (exposed:comparator)2557,0733,5362,358
1:42988,2894,1442,763
1:1, power 0.90256not computednot computednot computed
1:1, margin HR 1.25631not computednot computednot computed
Published estimatePoint estimateE-value (point)E-value (CI limit)Source
PPI, Wu 2017HR 2.734.901.43[13]
PPI, Chrcanovic 2017HR 2.815.071.54[14]
PPI crude pooledOR 2.714.862.83[21]
PPI adjusted pooledOR 1.442.241.00[21]
Sertraline historyHR 1.602.581.57[24]
SSRI pooledRR 2.444.31not computed[30]
Antihypertensive, Wu 2016HR 0.1216.153.50[15]
Antihypertensive, Chidiac 2026HR 0.238.16not computed[32]
Antihypertensive early failure, Vilela 2026OR 0.267.151.43[33]

Excluding HR 1.5 with equal allocation requires 191 events: about 1,910 patients at 10% patient-level risk before inflation and 2,652 after. With 1:4 allocation (as for bupropion or mirtazapine initiators), 298 events and about 4,144 patients are needed; excluding a margin of 1.25 more than triples the events to 631. These are large for one clinic but modest for a national register. The E-values for crude PPI and SSRI estimates (4.3 to 5.1) mean a confounder associated with drug and failure by about fivefold could explain the point estimate, but only about 1.4 to 1.6 is needed to move the confidence limit to 1. An E-value of 16 for the Wu 2016 point estimate is hard to attribute to a single confounder, which supports exposure definition, not a covariate, as the driver; the limit E-value of 3.5 shows moderate bias could still explain the interval’s upper end.

The power calculation assumes proportional hazards, a true HR of 1.0, independent patients, and the stated risks; non-proportionality would call for separate early and late analyses with fewer events each.

Immortal-time illustration

To make Section 3.4 concrete, we ran a Monte Carlo simulation (script calc35.py; seed 35; 200,000 simulated patients per scenario). Illustrative computation under stated assumptions, not empirical data. The assumptions were: constant failure hazard equal to −ln(0.90)/10=0.0105 per year (10% failure at 10 years), identical for everyone; no drug effect; follow-up of 10 years with administrative censoring; a fraction of patients (10%, 30%, or 50%) starting a drug at a time uniform over the 10 years; and a patient counted as an “ever user” only if the implant was still in place when the drug was started. In the naive ever/never analysis, all person-time from implant placement was assigned to the group by final label. The simulation gave naive rate ratios of 0.481 (10% starters), 0.418 (30%), and 0.335 (50%), against aligned rate ratios of 1.012, 1.007, and 0.985, where aligned means that time before drug initiation was assigned to the unexposed group. The naive values are an upper-bound mechanism, since real studies often record exposure for a window around placement and not uniformly across follow-up, and they should not be read as estimates for any published cohort.

Statistical analysis plan

Primary estimand: per-initiation (intention-to-initiate) cause-specific hazard ratio for patient-level biological failure, weighted by inverse probability of treatment, with cluster-robust variance. Secondary: per-protocol hazard ratio with inverse-probability-of-censoring weights for deviation; 5-year cumulative incidence difference accounting for death; dose and duration categories (defined daily dose tertiles, cumulative exposure); separate early and late analyses; implant-level marginal models; prevalent-user comparison; quantitative bias analysis using E-values for each estimate and its limit; and heterogeneity by age, smoking, and periodontitis. Missing covariates are handled by multiple imputation under stated assumptions, with a complete-case sensitivity analysis.

The analysis would be registered, with code and the target-trial table, before data access; analyses outside the plan would be labelled exploratory.

Ethics and feasibility

No patient data were used for this manuscript. A real study would need ethics or data-governance approval, a data-protection assessment for linked records, and, where applicable, a consent waiver; none has been obtained or registered.

5. Competing explanations and how the design discriminates among them

The protocol is only useful if its results differ under different explanations. Explanation A: true drug effect. The HR stays elevated (PPI, SSRI) or reduced (antihypertensive) against active comparators, with a dose-duration gradient, and is absent for negative-control drugs and future initiation. This would justify a randomized or mechanistic follow-up.

Explanation B: confounding by indication. The crude HR is elevated, the active-comparator HR attenuates toward 1, prosthetic complications correlate with depression and bruxism indicators, and the emulated E-value is low. The drug is a marker.

Explanation C: healthy-user and prevalent-user selection. Naive ever/never analyses of negative-control drugs also show protection; prevalent users differ from new users; protection disappears when exposure starts at time zero. The statin-fracture literature shows the mechanism in another outcome [39].

Explanation D: immortal and misclassified time. The naive-versus-aligned contrast is large and is reproduced in negative-control drugs (P5); Section 4.10 shows the size attainable under assumptions.

Explanation E: clustering and outcome definition. Implant-level analyses give narrower intervals than patient-level analyses (P6), and effects shrink when mechanical complications are excluded from the outcome.

Explanation F: clinician behavior and a hidden comparator effect. Clinicians who believe a drug is harmful may remove or avoid implants in users, creating or hiding an association; separating early failure from removal timing and validating the outcome partly addresses this. If the comparator shares the effect (for example if H2RAs also affect bone), the HR would be near 1 despite harm relative to no drug. We therefore state conclusions about the contrast actually emulated.

6. Clinical and engineering implications

If the predictions hold, three consequences would follow, conditional on external verification. Medication history would be a weaker reason to alter implant plans than the crude literature suggests, with attention shifting to periodontal status, smoking, hygiene, and bruxism [42]. Consent materials quoting a doubling of risk from crude cohorts would need revision, since the adjusted pooled PPI estimate is not significant and is unstable [21]. Antihypertensive “protection” would leave prognostic discussions, since hypertension itself was associated with late failure in one cohort [33].

If the predictions fail for one drug class, a bone-targeted trial would be justified, and prescribers would need to weigh the effect against the indication, since stopping an antidepressant or antihypertensive for implant surgery carries its own risk. The protocol makes no recommendation to change prescribing.

7. Limitations

  • Abstract-level appraisal. We read abstracts and the notes’ verified summaries, not full texts; exposure definitions, adjustment sets, and follow-up may differ from our inferences.
  • Search limits. PubMed, Europe PMC, and ClinicalTrials.gov were searched; Embase, Scopus, and Web of Science were not accessible. The claim that no implant target-trial emulation exists applies to these sources on 17 November 2026.
  • No data. Every figure comes from published estimates or stated assumptions. The simulation and power calculation use constant hazards and independent patients.
  • Assumed parameters. The 1.5 and 0.6 thresholds, the 1.25 inflation factor, the 10% loss allowance, and the within-patient correlations are assumptions.
  • Residual confounding. Active comparators trade confounding by indication for confounding between similar indications. Depression severity, bruxism, periodontal status, and smoking are poorly recorded in routine data.
  • Exposure misclassification. Dispensing is not ingestion, and over-the-counter PPI and H2RA use is missed, biasing toward the null.
  • Outcome validity. Removal codes do not distinguish causes; chart validation is mandatory and costly.
  • Positivity and sample size. Small comparator groups may limit analyses.
  • Generalizability. Drug formulations and dental practice differ across systems.
  • Negative-control choice. A negative-control drug may have unrecognized bone effects.
  • Framework limits. Target-trial emulation clarifies assumptions but cannot create exchangeability; its authors discuss when it is helpful [49].
  • Evidence-level labels are operational categories chosen by us, not a formal grading.

8. Conclusions

The reported links between PPIs, antidepressants, and antihypertensives and implant survival rest mainly on ever/never comparisons in single-center cohorts, with weaker adjusted results and, for antihypertensives, effect sizes that are difficult to attribute to drug action. We searched for, and did not find, an implant study that used a target-trial emulation, a new-user active-comparator design, or a time-aligned exposure with negative controls. We specify three such emulations, a power calculation (191 events to exclude HR 1.5 with equal allocation under stated assumptions), a bias analysis plan, and ten predictions with refuting results.

Cite this paper

Jain S, Gupta A. Do Proton Pump Inhibitors, Antidepressants, and Antihypertensives Affect Dental Implant Survival? A Target-Trial Emulation Protocol with Active Comparators and Negative Controls. Working paper. Center for Implant Dentistry; 2026. Available from: https://bayareaimplantdentistry.com/clinician-research-and-publications/drug-implant-failure-target-trial-emulation

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