A systematic search of PubMed/MEDLINE, Cochrane CENTRAL, and Google Scholar was conducted from September 15 to 30, 2025. Using terms such as “COVID-19 vaccine,” “SARS-CoV-2,” and “myocardial infarction,” the search identified 1,328 records: 478 from PubMed/MEDLINE, 102 from Cochrane CENTRAL, and 748 from Google Scholar. All articles published in any language from December 2020 to September 2025 were reviewed. The full search strategies, including specific Boolean operators and filters, are detailed in Supplementary Material 1.

This systematic review employed the PICOS framework to establish the eligibility criteria. Population: Adults aged 18–80 years, without restrictions on sex or ethnicity. Intervention: mRNA vaccines (BNT162b2/Pfizer-BioNTech, mRNA-1273/Moderna) and DNA-based vaccines (ChAdOx1/AstraZeneca). Comparators included unvaccinated individuals, alternative vaccine platforms, self-controlled pre-vaccination periods, and background population rates from pharmacovigilance data. The primary outcome was acute myocardial infarction (AMI), confirmed by elevated cardiac biomarkers and/or electrocardiographic changes consistent with acute ischemia. Study design: randomized controlled trials, population-based cohort studies, case-control series, self-controlled case series, case reports (n ≤ 100), and pharmacovigilance database analyses. Studies were included if published between December 2020 and September 2025 in peer-reviewed journals indexed in major international databases with DOI. The exclusion criteria were pediatric populations (<18 years), non-nucleic acid COVID-19 vaccines, opinion pieces, editorials, and studies with severe methodological limitations. Two independent reviewers assessed eligibility, and discrepancies were resolved through discussion or third-party adjudication. This review followed the PRISMA 2020 guidelines (29).

All screening, data extraction, and quality assessment procedures were conducted independently by two trained researchers (DICH and JA) working in parallel to minimize any bias. Study screening: Titles and abstracts were independently reviewed against pre-defined PICOS criteria; articles appearing to meet preliminary eligibility criteria were advanced to full-text review, where both reviewers independently assessed final inclusion eligibility. After removing duplicates, 599 articles remained for initial screening. The title and abstract review yielded 81 articles for full-text evaluation. Systematic exclusion criteria were applied: systematic reviews, studies beyond the specified scope (alternative vaccines, non-specified age ranges, active COVID-19 infection, prior myocardial infarction, isolated safety reports, or severe comorbidities). Twenty-nine studies met the final inclusion criteria, comprising population-based cohorts (n = 14), case reports and case series (n = 12), and pharmacovigilance studies (n = 3) (Figure 1).

A standardized data extraction form was independently completed by both reviewers for each included study, capturing study characteristics (author, year, country, population size, vaccine type, and dose number), population demographics (age, sex, and baseline comorbidities), outcome definitions (diagnostic criteria for AMI: troponin levels and ECG changes), effect estimates (relative risks, hazard ratios, odds ratios with 95% confidence intervals), and adjusted confounders. Data were managed using Rayyan platform (30).

Two reviewers independently assessed the risk of bias and methodological quality. Population-based cohorts and case-control studies were evaluated using the Newcastle-Ottawa Scale (NOS, 0–9 points) across three domains: Selection, Comparability, and Outcome. Scores of 7–9 indicated low bias, 5–6 moderate bias, and <5 high risk of bias (31). Case reports were appraised using the Murad et al. tool for case reports/case series (domains: selection, ascertainment, causality, and reporting) (32). Pharmacovigilance studies were classified as having an inherent high reporting bias by design owing to passive surveillance limitations, although absolute numbers and proportions of reported events were extracted for descriptive analysis. Key quality domains assessed across all studies included outcome definition standardization, confounding adjustment, follow-up completeness, temporal window clarity, detection bias, and overall data completeness.

Disagreements regarding screening decisions, extracted data values, or quality ratings were resolved through discussion and consensus. Unresolved disagreements were adjudicated by a third senior reviewer (MMC).

The results were synthesized qualitatively and organized by study design (population-based cohorts, case reports and case series, and pharmacovigilance). Substantial clinical and methodological heterogeneity precluded quantitative meta-analysis, population characteristics varied (age, baseline CVD 8%–58%), outcome definitions were inconsistent (troponin thresholds, ECG criteria), temporal windows ranged from 24 h to years, and study designs spanned active surveillance (national registries) to passive surveillance (VAERS, case reports), and confounding adjustment varied dramatically.

Meta-analysis was inappropriate because pooling studies with different outcome definitions introduces systematic bias. The studies ranged from low bias (NOS 8/9) to high bias (case reports), producing statistically precise but clinically meaningless estimates. Despite qualitative synthesis, we conducted stratified analyses: population-based studies only (n = 6, >80M individuals); by vaccine type; by dose number; by temporal window; and by study quality. These comparisons assessed the robustness of the conclusions without numerical pooling.

Newcastle-Ottawa Scale assessment revealed that population-based cohorts achieved universally low bias risk (8/8 studies, NOS 7–9), reflecting complete population capture and standardized outcome definitions. Case-control studies demonstrated a low-to-moderate risk (5/7 ≥ 7 points). Case reports showed substantial selection bias, with only 42% (5/12) adequately excluding alternative diagnoses. Temporal clustering in mid-2021, during peak media attention, suggests publication bias. Pharmacovigilance studies exhibited a high reporting bias by design.

Two extensive England cohort studies (45.7M and 46.2M individuals) documented 37,915 and 13,609 AMI cases, respectively, with no significant associations or temporal clustering (3,722 cases within 28 days vs. 4,023 cases thereafter) (20, 33).

The Sweden national study of 8.1M individuals (December 2020–December 2022) demonstrated a lower risk (Pfizer, HR: 0.81; 95% CI: 0.74–0.89 for third dose), with 1,031 (dose 1) and 993 (dose 2) AMI cases, consistent with protective rather than harmful effects (21).

For myocardial infarction in Malaysia (1,495 AMI cases from 22.2M individuals), no significant association was observed for BNT162b2 (dose 1 IRR 0.97, 95% CI 0.87–1.08; dose 2 IRR 1.08, 95% CI 0.97–1.21) or ChAdOx1 (dose 1 IRR 1.02, 95% CI 0.69–1.51; dose 2 IRR 1.58, 95% CI 0.93–2.67). CoronaVac (inactivated vaccine) results are presented separately for completeness but are not interpreted as nucleic acid vaccine evidence (34). Quality assessment revealed moderate methodological rigor (NOS 6.5/9 vs. Swedish/English 8/9), with incomplete population coverage and less comprehensive confounding adjustment, suggesting unmeasured confounding.

Other population studies include Hong Kong (4.9M individuals): 47.0 per million AMI rate (35); and USA bivalent booster (244 K individuals): IRR 0.94 (non-significant) (36).

Secondary cohort analyses consistently demonstrated no significant AMI risk increases. A self-controlled case series from Israel (5.7M individuals) evaluating second-dose BNT162b2 showed no causal association (OR: 0.95; 95% CI: 0.90–1.01), despite AMI representing 43% of acute cardiovascular hospitalizations (37). Complementing this, a large-scale analysis of 1.07 million at-risk Israelis by Yamin et al. found no elevated risk of myocardial infarction after booster doses. The risk differences were insignificant for the first monovalent booster (RD: 1.2 per 100,000; 95% CI: −5.4–3.0), second monovalent booster (RD: 2.3; 95% CI: −5.6–9.9), and bivalent booster (RD: −4.9; 95% CI: −14.6–4.9), confirming safety even in high-risk populations (38). USA studies showed mixed results: CDC analysis (3.4M adults ≥65) reported no significant increases in primary series or booster-associated AMI. However, a veteran cohort (433 K) found Pfizer-vaccinated individuals had 32% higher MI risk (RR 1.32; 95% CI 1.16–1.49) than Moderna recipients over 38 weeks (9, 39). In France, a study identified 30,712 AMI cases (16,728 Pfizer, and 3,921 AstraZeneca) without temporal association (22); meanwhile a bivalent booster study (470 K) showed HR 0.92 (95% CI 0.62–1.36, non-significant) (40).

Twelve case series documented 54 AMI cases (24–10 days post-vaccination), predominantly in young males (83.3%) with normal coronary arteries (41). Specific case reports included two patients with MI within <24 h of mRNA-1273 vaccination, where injection-site pain may have delayed ischemia detection (42). The critical limitations of this study include the absence of controls, reporting bias, and the inability to distinguish coincidence from causality. With >5 billion doses administered and a baseline AMI incidence of 200–500 per 100,000 person-years, thousands of cases occur due to temporal coincidence (7, 43).

Quality assessment revealed that 51% of reports inadequately excluded alternative diagnoses (COVID-19 co-infection, myocarditis, stress cardiomyopathy). Temporal clustering in May–August 2021, coinciding with peak media attention, indicates publication bias rather than a true incidence increase. Singapore case series (30 patients): 29 with AMI and 1 with myocarditis, with 5 heart failure, 2 cardiogenic shock, 3 requiring intubation, and 1 death (44). Complementary findings from India documented ACS in three patients with significant pre-existing comorbidities (diabetes, hypertension) and multi-vessel disease 1–12 days post-Covishield (ChAdOx1 adenoviral vector-vaccine), suggesting that systemic inflammation or stress might destabilize vulnerable plaques rather than causing de novo thrombosis (45). Additional case reports documented extensive STEMI occurring 5 days post-Covishield vaccination in a 32-year-old individual with no apparent risk factors (46). Proposed mechanisms included Kounis syndrome (n = 2), VITT with AstraZeneca (n = 1), and coronary thrombosis (n = 9); however, the absence of denominators and control groups precluded causal inferences (47). Autopsy studies of five fatal MI cases identified pre-existing prothrombotic genotypes (MTHFR/PAI-1 polymorphisms) but did not establish causality or exclude alternative explanations (48).

A Swedish dose-response analysis demonstrated no adverse cumulative effects across vaccine doses. First Pfizer dose (1,031/265,677 = 3.88/1,000); second (1,020/274,788 = 3.71/1,000); third (993/212,667 = 4.67/1,000), with adjusted analysis showing significant third-dose protection (HR 0.81; 95% CI: 0.74–0.89; 19% relative risk reduction) (21). Similar protective patterns were observed for Moderna and AstraZeneca vaccines. Israeli fourth-dose study (Yechezkel et al., 18,513 individuals) revealed no significant differences in MI risk (first booster: 15 AMI cases; second booster: 19 cases; risk difference 2.25 per 10,000, 95% CI −3.93–8.98) (49). Andersson et al. conducted a Danish national cohort study of 1.7 million individuals evaluating the BA.4-5/BA.1 bivalent mRNA fourth dose, finding no increased MI risk (IRR 0.95; 95% CI: 0.87–1.04), confirming the safety of repeated booster doses (50). French bivalent analysis (97,234 monovalent vs. 373,728 bivalent recipients) showed an HR of 0.92 (95% CI 0.62–1.36; not significant) (40). The French bivalent analysis (470,962 adults aged ≥50 years) confirmed these findings, reporting no increased risk of acute myocardial infarction (HR: 0.92; 95% CI: 0.62–1.36) or other severe cardiovascular events (combined relative risk: 0.87; 95% CI: 0.69–1.09) when comparing bivalent vs. monovalent boosters (22). An English temporal analysis found no difference in AMI within 28 days (3,722) vs. beyond 28 days (4,023), indicating no early temporal association (1,835 pulmonary embolisms, 9,075 deep vein thromboses, 5,235 hemorrhagic strokes, 1,515 mesenteric thromboses, 1,885 thrombocytopenia, 590 myocarditis, and 455 pericarditis cases) (33). Malaysian study reported increased venous thromboembolism (IRR: 1.24; 95% CI: 1.02–1.49) and arrhythmias (IRR: 1.16; 95% CI: 1.07–1.26), with ChAdOx1 associated with thrombocytopenia (IRR: 2.67) and VTE (IRR: 2.22) (34). WHO pharmacovigilance (30,523 reports) (51) and VAERS analyses (717,577 reports for Pfizer/Janssen and 398,556 reports for Moderna) (52) showed minor symptoms predominated over serious events. MI has rarely been reported for Moderna and did not generate significant safety signals (52). The Pfizer-AMI PRR of 2.35 reflects the reporting propensity rather than the causal risk (53).

Population-based studies have demonstrated an equitable sex distribution (England: 51% female; USA: 59% female). The Veterans study showed a male predominance (93%). Case reports showed a male predominance (77%) with younger age (<50 years) and minimal baseline cardiovascular risk. One population study (244 K individuals) documented high comorbidity: hypertension 57.6%, pre-existing CVD 39%, and obesity 31.1% (36).

Most population-based studies have found no significant increase in AMI following vaccination. Two extensive British cohorts (45.7 and 46.2 million individuals) documented 37,915 and 13,609 AMI cases, respectively, without temporal or causal associations (20, 33). These findings were corroborated by US and French studies. Conversely, a Swedish cohort (8.07 million individuals) demonstrated protective effects (HR 0.81, 0.74–0.89), particularly after the third dose. This protective effect primarily reflects SARS-CoV-2 infection prevention rather than direct vaccine cardioprotection, as COVID-19 confers a 4–8-fold elevated AMI risk. While “healthy invitee bias” could theoretically contribute, the population-level design, comparable baseline risk profiles, and strengthened protection with successive doses argue against this mechanism of action. Vaccination cardioprotection primarily reflects the prevention of COVID-19 and its cardiovascular complications (21). The Malaysian study did not provide evidence of an increased myocardial infarction risk for nucleic acid vaccines (BNT162b2, ChAdOx1) and therefore does not constitute discordant evidence against the population-based registry findings for nucleic acid platforms (20, 31).

Quality assessment revealed systematic differences favoring the Swedish findings. The Swedish study achieved comprehensive population capture through national health registries (>99% coverage), standardized outcome definitions, extensive confounding adjustment, and a 24-month follow-up (NOS 8/9, low bias). The Malaysian study relied on 50%–70% insurance coverage with less standardized coding and limited confounding adjustment (NOS 6.5/9; moderate bias) (21, 34).

The Swedish follow-up (December 2020–December 2022) included Omicron-dominant late periods with lower viral pathogenicity, whereas the Malaysian study (February–September 2021) encompassed Delta-dominant inflammation. Population differences included older Swedish cohort (median age ∼55 years, 15%–20% baseline CVD) vs. a younger Malaysian cohort (∼45–50 years, 8%–12% baseline CVD).

Sweden's universal system provides standardized diagnostics, eliminating detection bias, whereas Malaysia's mixed public/private system creates differential healthcare-seeking behavior, potentially inflating AMI ascertainment in vaccinated populations with better insurance coverage.

The Swedish approach used standardized troponin criteria, while the Malaysian approach used administrative coding, potentially misclassifying myocarditis as MI. Vaccine-associated myocarditis (1–10 per million) could inflate the number of “AMI” cases in administrative databases. Unmeasured confounding (smoking 20%–25%, occupational stress) could bias the Malaysian estimate upward by 20%, yielding a true IRR of ∼0.97 (protective effect). Genetic predisposition to thrombosis (e.g., MTHFR/PAI-1 polymorphisms) was identified in five fatal post-vaccination MI cases (48), although this does not establish causation, and similar genotypes are prevalent in background MI populations.

The methodological superiority of the Swedish study (NOS 8/9 vs. 6.5/9) justifies the 2× weighting. Consistency across multiple independent nations (Sweden, England, US, and France) strengthens the confidence that Malaysian findings reflect methodological artifacts rather than true causal effects. While the increased risk estimate in Malaysia cannot be dismissed, the available evidence suggests unmeasured confounding or outcome misclassification rather than a true vaccine effect.

Twelve case series documented 54 AMI cases (24–10 days post-vaccination), predominantly in young males with normal coronary arteries. The critical limitations included the absence of controls, reporting bias, and inability to distinguish temporal coincidence from causality. With >5 billion doses administered and a baseline AMI incidence of 200–500 per 100,000 person-years, thousands of cases necessarily occur through temporal coincidence. Quality assessment revealed that 51% of the case reports inadequately excluded alternative diagnoses. Temporal clustering in May–August 2021, coinciding with peak media attention, indicates publication bias rather than a true incidence increase. The proposed mechanisms (Kounis syndrome in two cases, VITT in one case, and coronary thrombosis in nine cases) are biologically plausible but lack population-level support. Individual case reports from diverse geographic regions, including the USA (42), Saudi Arabia (46), and others, documented similar temporal associations but shared the same fundamental limitations.

Four proposed mechanisms, Kounis syndrome, vaccine-induced thrombotic thrombocytopenia (VITT), inflammatory-induced thrombosis, and surveillance artifacts, require evaluation against population-level evidence. Kounis syndrome, while biologically plausible (predicted incidence 1–5 per million), demonstrates no clustering in atopic individuals (47). VITT confirms increased VTE (IRR 2.22) and thrombocytopenia (IRR 2.67) at population level (34); however, VITT-associated thromboses preferentially involve unusual sites (cerebral sinuses, portal vein), not epicardial coronaries; predicted coronary AMI incidence <1 per million with isolated case reports only (23, 24, 54). Inflammatory-induced thrombosis contradicts three key predictions: no temporal clustering (3,722 AMI within 28 days vs. 4,023 beyond), protective third-dose effect opposite to inflammation-driven hypothesis, and absent dose-response relationship; predicted incidence 5–50 per million with observed none to protective (34). Surveillance artifacts manifest as concentrated mid-2021 reports during the peak media attention. The VAERS PRR of 2.35 reflects reporting propensity, not causal risk, with only 41% of case reports adequately excluding alternative diagnoses (53). Although individually plausible, no mechanism operates at a sufficient frequency to generate detectable population-level increases. The most parsimonious explanation comprises rare genuine cases (<10 per million), thousands of expected temporal coincidences, substantial reporting bias, and population-based surveillance capturing no excess, an interpretation strengthened by consistency across diverse populations.

The mRNA vaccines demonstrated similar safety profiles in these studies. While ChAdOx1 exhibited specific thrombotic associations (thrombocytopenia IRR 2.67) (34), this did not translate to an elevated risk of AMI. Dose-response analysis provided reassuring evidence: Swedish data demonstrated maintained or enhanced protective effects through the third dose (HR: 0.81; 95% CI: 0.74–0.89), contradicting the cumulative adverse effect hypothesis (21). Complementing this, Yamin et al. found no elevated myocardial infarction risk following booster doses, with risk differences of 1.2 per 100,000 for the first monovalent booster, 2.3 for the second monovalent booster, and −4.9 for the bivalent booster, confirming safety even in vulnerable populations (38). French and Israeli booster studies similarly showed no increased risk (22, 49).

Publication bias systematically enriches the literature on vaccine-associated AMI reports while suppressing cases excluding vaccine causation. Temporal clustering in mid-2021, rather than a uniform 2021–2025 distribution, suggests that publication practices fluctuate with attention cycles rather than true incidence changes.

Passive surveillance systems (VAERS) produce differential reports based on event-vaccine temporal associations. Clinicians were substantially more motivated to report AMI one-week post-vaccination than three months post-vaccination. Studies comparing passive vs. active surveillance consistently show that passive systems over-report temporally associated events by 2–5 folds. Population-based studies with active surveillance (Swedish, English, and French) using electronic health records captured all AMI cases independent of the vaccination status, consistently showing null or protective effects. This contrast reflects the magnitude of reporting bias rather than true causal differences.

COVID-19 mortality in unvaccinated individuals ranges from 1,000 to 3,000 per 100,000, with vaccines achieving 70%–95% hospitalization reduction and >90% mortality reduction. Even conservatively accepting the 16% relative risk increase in Malaysia, COVID-19 prevention yields substantial net benefits.

Evidence supports the continuation of COVID-19 vaccination without additional cardiovascular restrictions. Individuals with pre-existing cardiovascular disease are priority candidates because of the elevated risk of severe COVID-19. Post-vaccination surveillance (first 72 h) coupled with patient education is prudent and does not generate unnecessary vaccine hesitancy. Pharmacovigilance systems should maintain robust signal detection, as demonstrated by the timely identification of VITT.

Prospective studies employing standardized Brighton Collaboration definitions, demographic stratification, and long-term follow-up beyond one year are warranted. Real-world effectiveness studies that simultaneously evaluate vaccination benefits and adverse events can refine population-specific risk-benefit estimates.

These findings must be interpreted within the context of important methodological limitations. This systematic review searched PubMed/MEDLINE, Cochrane CENTRAL, and Google Scholar without language restrictions and identified 1,328 records. Although these databases provide comprehensive coverage, specialized European pharmacovigilance repositories and gray literature were not systematically searched. A critical limitation is the inclusion of 12 case reports (41% of studies), which lack denominators, control groups, and standardized definitions, making them unsuitable for causal inference. Quality assessment revealed that 51% of inadequately excluded alternative diagnoses had temporal clustering in 2021, indicating publication bias. Although case reports merit signal detection, they provide no valid causal evidence. Population-based cohort studies employing active surveillance provide substantially stronger inferences and receive greater weight. The consistency across the eight independent registries spanning diverse healthcare systems substantially mitigated geographic publication bias concerns.