We systematically searched PubMed, Embase, Web of Science, the Cochrane Library, and the trial registry ClinicalTrials.gov from database inception to 14 October 2025 (20, 21). Search strategies combined controlled vocabulary (MeSH/Emtree) and free-text terms related to “daratumumab,” “multiple myeloma,” and “infection,” using Boolean and proximity operators; full strategies are provided in Supplementary Table S1. Eligibility was restricted to English-language full-text publications. We also screened reference lists of relevant trials and reviews (22). Records were deduplicated in reference-management software, and titles/abstracts and full texts were screened independently by two reviewers.

Studies were selected according to the PICOS framework (23). Population: adults (≥18 years) with NDMM or RRMM. Intervention: daratumumab-containing regimens added to a standard backbone. Comparison: the same backbone without daratumumab. Outcomes: infection-related events, including any-grade infection, grade ≥3 infection, pneumonia, and infection-related death; infections were captured as reported by the trials and, where available, aligned to CTCAE grade definitions (24). Study design: randomized phase II or III controlled trials.

Exclusion criteria comprised observational or single-arm studies, case series, reviews, conference abstracts without full data, duplicate/overlapping reports, and trials not reporting infection outcomes.

Two reviewers independently extracted data using a piloted form, including study characteristics (first author, year, phase, design, country/centers), patient population (NDMM/RRMM), treatment regimens, analysis population (safety vs. intention-to-treat), sample sizes, follow-up duration, and numbers of patients with each infection outcome. Discrepancies were resolved by discussion or by a third reviewer (20). For overlapping publications, the most comprehensive or most recent dataset was used. When necessary, we planned to contact study authors or consult trial registries to clarify unclear data (25).

Methodological quality was assessed with the Cochrane Risk of Bias tool (RoB 1.0) in Review Manager (RevMan, version 5.4) (26, 27). across seven domains: random sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, selective reporting, and other bias. Each domain was judged as low, unclear, or high risk according to the Cochrane Handbook (20). Because most trials were open-label, performance bias was commonly rated as high; outcome-assessment blinding and attrition were judged separately.

All quantitative analyses were performed using Review Manager (RevMan, version 5.4; Cochrane Collaboration) (26), and R software (version 4.5.1; metafor package) (28). For dichotomous outcomes, pooled risk ratios (RRs) with 95% confidence intervals (CIs) were estimated using the DerSimonian–Laird random‐effects model; a random‐effects approach was applied regardless of heterogeneity because clinical and methodological diversity was anticipated. Statistical heterogeneity was quantified with I², τ², and Cochran’s Q (29, 30); I² > 50% was interpreted as substantial (31). Predefined subgroup analyses assessed effect modification by disease status (NDMM vs RRMM) and transplant eligibility (TE vs TI), with between‐subgroup differences tested using a test for subgroup differences (interaction p) based on Cochran’s Q (32). Sensitivity analysis consisted of a leave‐one‐out influence analysis, sequentially omitting each trial to evaluate its impact on pooled estimates (33). Zero‐event handling: for trials with zero events in one arm, a continuity correction of 0.5 was applied; trials with zero events in both arms were excluded from that outcome’s meta‐analysis (34). Multi‐arm trials: when multiple daratumumab arms shared a single control, the shared control was evenly split (sample size and events) across comparisons to avoid double counting. Publication bias was assessed by visual inspection of funnel plots in RevMan and, when ≥10 studies were available for an outcome, by Egger’s regression in R (metafor) (20, 35). All tests were two‐sided with p< 0.05 considered statistically significant. For rare-event outcomes, when fewer than three trials reported an outcome and/or when definitions were materially heterogeneous for example, inclusion of COVID-19–related deaths, we prespecified that no meta-analysis would be conducted to avoid unstable or biased estimates; a descriptive synthesis was provided.

A total of 870 records were identified from databases and a trial registry, including 312 from PubMed, 278 from Embase, 185 from Web of Science, 45 from the Cochrane Library, and 50 from ClinicalTrials.gov (20, 21). After removing 210 duplicates, 660 unique records were screened by title and abstract; 600 were excluded for not meeting inclusion criteria. Full-text assessment was performed for 60 articles, of which 51 were excluded for the following reasons: non-randomized design (n = 18), absence of a daratumumab-containing arm (n = 12), no infection outcomes reported (n = 15), or duplicate/overlapping populations (n = 6). Ultimately, nine RCTs met all eligibility criteria and were included in both qualitative and quantitative syntheses. The screening and selection process is shown in Figure 1 (PRISMA 2020 flow diagram).

The included trials comprised POLLUX (36), CASTOR (15), ALCYONE (37), MAIA (16), CASSIOPEIA (38), GRIFFIN (39), APOLLO (40), CANDOR (41), and PERSEUS (42), covering both newly diagnosed and relapsed/refractory MM populations. Treatment backbones included immunomodulatory drugs (IMiDs), proteasome inhibitors (PIs), and pomalidomide–dexamethasone (Pd).

Nine RCTs comprising 5,281 patients were included (2,720 receiving daratumumab-containing regimens and 2,561 receiving control therapy). Because reporting of infection endpoints was not uniform across trials, denominators differed by outcome: any infection was available in six RCTs, grade ≥3 infections in all nine RCTs, and pneumonia in nine RCTs (the contributing trials for each endpoint are indicated in the corresponding figures/tables). Key characteristics are summarized in Table 1. Expanded baseline demographics and prior lines of therapy are provided in Supplementary Table S2. Five trials enrolled NDMM (ALCYONE, MAIA, CASSIOPEIA, GRIFFIN, PERSEUS) (16, 37–39, 42), and four enrolled RRMM (POLLUX, CASTOR, APOLLO, CANDOR) (15, 36, 40, 41). Most studies were phase III; GRIFFIN was a randomized phase II trial (39). Daratumumab was combined with standard backbones including Rd, Vd, VMP, VTd, VRd, or Pd; accordingly, infection outcomes were assessed across IMiD-based, PI-based, and IMiD+PI regimens. Median follow-up ranged from 16 months (APOLLO) to 56 months (MAIA) (16, 40).

Risk of bias was evaluated using the Cochrane RoB 1.0 tool in RevMan (version 5.4) (26, 27), Overall, the trials demonstrated low risk of bias across most domains (random sequence generation, allocation concealment, incomplete outcome data, and selective reporting). Because most trials were open-label, blinding of participants and personnel was judged at high risk for performance bias; however, blinding of outcome assessment was considered low risk, as infection outcomes were objectively defined and systematically collected per protocol (33). Several studies had minor concerns under “other bias,” mainly related to smaller sample sizes or exploratory design for example, the phase II GRIFFIN trial (39). No major methodological concerns were identified that would materially affect pooled estimates. The overall profile is summarized in Supplementary Figure S1 (summary plot) and Supplementary Figure S2 (domain-level distribution).

Six RCTs reported any-grade infections (16, 37–40, 42). In the random-effects meta-analysis (Figure 2), daratumumab-containing regimens were associated with increased risk of infection (pooled RR, 1.23; 95% CI, 1.14–1.33). Between-study heterogeneity was moderate (I²=66%; τ²=0.01; Q = 14.82, df = 5, p=0.01). The 95% prediction interval was 1.00–1.52, indicating that the true effect in a comparable future setting is expected to fall within this range. Despite heterogeneity, the direction and magnitude of the effect were consistent, and leave-one-out analyses did not materially alter the pooled estimate (33).

All nine RCTs reported grade ≥3 infections (Figure 3) (15, 16, 36–42). Daratumumab-containing regimens were associated with a higher incidence of severe infections (pooled RR, 1.29; 95% CI, 1.17–1.42). Between-study heterogeneity was negligible (I²=0%; τ²=0.00; Q = 4.90, df=8, p=0.77). The 95% prediction interval was 1.17–1.42. In subgroup analyses, increased risk was observed in both NDMM (RR, 1.36; 95% CI, 1.18–1.56) and RRMM (RR, 1.23; 95% CI, 1.08–1.40) populations (Supplementary Figure S3), with no significant interaction (interaction p=0.30). Similarly, elevated risk was seen in both transplant-eligible and transplant-ineligible groups (TE: RR, 1.20; 95% CI, 1.03–1.40; TI: RR, 1.45; 95% CI, 1.20–1.75; Figure 4), again with no significant interaction (interaction p=0.13).

Nine RCTs reported pneumonia, the most common site-specific infection associated with daratumumab (Figure 5) (15, 16, 36–42). Daratumumab-containing regimens were associated with a higher risk of pneumonia (pooled RR, 1.60; 95% CI, 1.24–2.07). Between-study heterogeneity was moderate (I²=60%; τ²=0.09; Q = 19.94, df=8, p=0.01); the 95% prediction interval was 0.84–3.04. In subgroup analyses by treatment backbone, age, and COVID-era timing, point estimates were consistently >1 with no significant between-subgroup interactions (between-subgroup tests: backbone χ²=0.39 [df=2], p=0.82; age χ²=2.25 [df=1], p=0.13; COVID-era χ²=0.00 [df=1], p=0.96; Supplementary Table S3). Leave-one-out analysis showed no single trial materially altered the pooled estimate (Supplementary Table S4).

Two trials (CANDOR and PERSEUS) reported infection-related fatalities (40, 41). Given event sparsity, the presence of double-zero trials, and materially heterogeneous definitions (including COVID-19–related deaths), and per our prespecified analysis plan, we did not pool this outcome. Absolute rates were ≤2% in both arms, and no consistent excess mortality with daratumumab was observed across trials.

A leave-one-out analysis for grade ≥3 infection (Supplementary Figure S4) yielded pooled RRs ranging from 1.27 to 1.32, with all 95% CIs > 1.0. The direction and significance of the overall effect were unchanged, and heterogeneity remained low across iterations, supporting the stability of the primary findings (28).

Formal assessment of publication bias was not undertaken because <10 studies contributed to each quantitative outcome (43), limiting the reliability of funnel-plot asymmetry tests (35). Visual inspection of the available effect sizes did not suggest substantial small-study effects or selective reporting.

Previous quantitative syntheses have largely focused on overall safety endpoints or hematologic toxicity rather than infection-specific outcomes (46, 47). By restricting inclusion to phase II/III randomized trials with standardized safety reporting, the present study offers higher-level evidence that more directly quantifies infection risk attributable to daratumumab. Separate analyses of any infection, grade ≥3 infection, and pneumonia further delineate the spectrum and clinical severity of infectious complications.

This review has several analytic and reporting limitations. First, our primary random-effects model used the DerSimonian–Laird estimator; alternative approaches such as REML with the Hartung–Knapp–Sidik–Jonkman adjustment (REML-HKSJ) generally yield wider confidence intervals and more conservative inference. In exploratory checks, effect directions were unchanged but precision varied. Second, for rare-event outcomes (notably infection-related deaths), summary estimates may differ by method, for example Peto odds ratio, arcsine risk difference, or continuity-correction models. Given event sparsity, the presence of double-zero trials, and heterogeneous definitions (including COVID-19–related deaths), we prespecified not to pool mortality and instead provided a descriptive synthesis. Third, small-sample issues—specifically zero-event handling (0.5 continuity correction for single-zero trials and exclusion of double-zero trials in some models) and splitting shared controls in multi-arm trials—may introduce modest bias; more complex models (beta-binomial or GLMM) were not applied. Fourth, infection definitions and reporting formats (including different CTCAE versions) varied across trials; we harmonized outcomes at the grade ≥3 threshold and used random-effects models throughout, yet residual heterogeneity likely remains. Fifth, trial-level information on vaccination, routine antimicrobial prophylaxis, and IVIG policies was variably reported and not comparable across studies; these measures were therefore summarized qualitatively and not meta-analyzed. Sixth, study-level aggregation precluded adjustment for individual-level risk factors and prophylactic practices. Seventh, fewer than ten studies contributed to each endpoint, limiting the power and interpretability of funnel plots and Egger’s tests for small-study bias. Eighth, we restricted eligibility to English-language full-text publications and mainly relied on ClinicalTrials.gov for trial registries; consequently, regional or non-English evidence (and non-ClinicalTrials.gov registrations) may have been missed. Finally, most trials predated widespread COVID-19 vaccination and contemporary supportive-care practices, which may affect current absolute risks and the generalizability of pooled estimates.