Different Short-Term Kidney Injury Risks Linked to GLP-1 and SGLT2 Diabetes Drugs: A Comparative Analysis

The literature search and screening process are outlined in Figure 1. After excluding 152 articles for not meeting inclusion criteria (see Table S3) [9,10,11,12,24,25,26,27,28,29,30,31,32,33,34,35,36,37,38,39,40,41,42,43,44,45,46,47,48,49,50,51,52,53,54,55,56,57,58,59,60,61,62,63,64,65,66,67,68,69,70,71,72,73,74,75,76,77,78,79,80,81,82,83,84,85,86,87,88,89,90,91,92,93,94,95,96,97,98,99,100,101,102,103,104,105,106,107,108,109,110,111,112,113,114,115,116,117,118,119,120,121,122,123,124,125,126,127,128,129,130,131,132,133,134,135,136,137,138,139,140,141,142,143,144,145,146,147,148,149,150,151,152,153,154,155,156,157,158,159,160,161,162,163,164,165,166,167,168,169,170,171], a total of 64 studies comprising 67 RCTs were included in the analysis (see Table S4) [28,97,107,144,172,173,174,175,176,177,178,179,180,181,182,183,184,185,186,187,188,189,190,191,192,193,194,195,196,197,198,199,200,201,202,203,204,205,206,207,208,209,210,211,212,213,214,215,216,217,218,219,220,221,222,223,224,225,226,227,228,229,230,231,232,233]. These trials enrolled 199,877 participants, with a mean age of 63.2 years (range: 45.1–74.2 years), and a mean female representation of 38.1% (range: 20.8–81.6%). The average follow-up duration across studies was 126.8 weeks (range: 4–281 weeks). Investigated GLP-1RAs included albiglutide, dulaglutide, efpeglenatide, exenatide, liraglutide, lixisenatide, semaglutide, and tirzepatide. SGLT2is evaluated included bexagliflozin, canagliflozin, dapagliflozin, empagliflozin, ertugliflozin, and sotagliflozin.

The distribution of key clinical and design-related effect modifiers across treatment nodes is summarized in. The network was largely placebo-centered, with the placebo/control node contributing the largest number of trials and participants, whereas several active treatment nodes were informed by relatively few studies. Age and sex distributions were broadly comparable across many nodes; however, visible between-node imbalances were observed in study duration, the proportion of trials including patients with renal impairment, and the proportion of diabetes-enriched populations. These differences should be considered when interpreting indirect comparisons and do not eliminate concern regarding transitivity. In particular, several SGLT2 inhibitor nodes included a higher proportion of trials enrolling patients with renal impairment and had longer follow-up durations, whereas tirzepatide nodes tended to have shorter follow-up and did not include renal impairment-enriched trials. No included trial was restricted to a single sex or to a specific age-defined population. However, because age and sex may still act as study-level effect modifiers across treatment nodes, mean age and female proportion were extracted and summarized into improve transparency regarding potential between-node differences. Table S9 Table S9

Our analysis identified that among all evaluated agents and dosages, only high-dose tirzepatide (10–15 mg/week) was associated with a statistically significant elevation in the risk of AKI when compared with control treatments. The estimated absolute risk difference was 0.28%, corresponding to a number needed to harm (NNH) of 357.34 patients. Although high-dose tirzepatide was the only regimen associated with a statistically significant increase in AKI risk, the estimate was based on sparse-event data with wide credible intervals and should therefore be interpreted cautiously. Conversely, lixisenatide, high-dose canagliflozin (300 mg/day), empagliflozin, and dapagliflozin were associated with a lower incidence of AKI compared to controls. Among all regimens assessed, high-dose tirzepatide had the highest SUCRA-based risk ranking for AKI (Figure 2, Figure 3 and Figure S3 and Table 1). Although high-dose tirzepatide was the only regimen associated with a statistically significant increase in AKI risk, the estimate was based on sparse-event data with wide credible intervals, indicating limited information size and substantial imprecision.

In the sensitivity analysis focusing on RCTs that did not enroll participants with baseline kidney disease, findings were consistent with the primary results. Specifically, high-dose tirzepatide (10–15 mg/week) remained significantly associated with increased AKI risk (ARD = 0.28%, NNH = 357.34). In contrast, high-dose canagliflozin (300 mg/day), dapagliflozin, and low-dose empagliflozin (1–10 mg/day) continued to demonstrate protective associations against AKI. Again, high-dose tirzepatide ranked highest for AKI risk (Figure 4, Figure 5 and Figure S3B, and Table 2).

Among the included agents, tirzepatide and canagliflozin were associated with lower all-cause dropout rates relative to controls. This finding was interpreted descriptively as a general tolerability measure and not as validation of renal safety (). Figures S1, S2 and S3C, and Table S5

Comprehensive SUCRA-based treatment hierarchies are detailed in. Results remained robust in sensitivity analyses based on deviation-model frameworks, with no significant instability observed (). Table S6A–C and Figure S4A–F Figure S5A–I

Risk-of-bias evaluation showed that 78.3% (367 of 469 items) of included studies were deemed low risk, 15.6% (73 items) unclear, and 6.1% (29 items) high risk (). Risk-of-bias assessment suggested that most included studies were judged to be at low risk, with a smaller proportion rated as unclear or high risk (). In node-splitting analyses, no statistically significant local inconsistency was detected among the estimable comparisons for the overall primary outcome, the subgroup excluding trials enrolling patients with underlying renal dysfunction, or the all-cause dropout network (). However, many active-comparator contrasts had no direct head-to-head evidence and therefore could not be formally assessed for local inconsistency. Certainty of evidence varied across comparisons: several placebo-linked contrasts, including tirzepatide high-dose versus placebo/control, were rated as high certainty, whereas many indirect active-versus-active comparisons remained low certainty because of limited direct evidence and reliance on indirect estimates (). Figure S6A,B Figure S6A,B Table S7A–C Table S8A–C

Our analysis possesses several methodological strengths. First, the NMA framework enabled head-to-head comparisons across multiple agents and dosages, thereby improving the precision and granularity of risk estimates. By limiting inclusion to RCTs and applying rigorous quality assessments, we minimized the risk of selection and measurement biases. The use of subgroup analysis—specifically excluding studies that enrolled patients with baseline renal impairment—allowed us to test whether our findings were robust across different clinical populations. Additionally, the separation of treatments by both compound and dose offers clinicians actionable data for patient-specific risk stratification.

However, this study is not without limitations. The focus on RCTs, while enhancing internal validity, may exclude real-world signals observed in observational cohorts or long-term registry studies. We standardized the terminology throughout the manuscript as AKI and rechecked the included RCTs to confirm that AKI events were directly reported in all included studies. Remaining limitations therefore relate primarily to sparse-event imprecision, indirect evidence, and between-node differences in study populations rather than to mixed inclusion of inferred renal injury outcomes. Another limitation is that this was a predominantly placebo-centered network, such that many clinically relevant active-comparator contrasts were informed mainly by indirect evidence. Although we summarized key clinical and design-related effect modifiers across treatment nodes (Table S9) and additionally examined baseline renal dysfunction in sensitivity analysis, Table S9 also revealed visible between-node imbalances rather than eliminating concern about transitivity. In particular, several SGLT2 inhibitor nodes were enriched for renal-impairment trials and had longer follow-up durations, whereas tirzepatide nodes tended to have shorter follow-up and no renal-impairment-enriched trials. These differences may have influenced indirect comparisons and therefore argue against overinterpretation of active-versus-active contrasts. Accordingly, comparisons between active agents should not be interpreted as equivalent to direct head-to-head randomized evidence. Although no significant local inconsistency was detected among the estimable comparisons, many clinically relevant active-comparator contrasts lacked direct head-to-head evidence and were therefore informed predominantly by indirect estimates. This explains why certainty remained high for some placebo-linked contrasts but lower for many indirect active-versus-active comparisons. Moreover, the modest absolute risk difference further suggests that statistical detectability should not be overinterpreted as implying a large clinical effect. Although no sex-specific or age-specific trials were included, differences in age and sex distribution across treatment nodes may still have influenced indirect comparisons. We therefore summarized these characteristics at the study level (Table S9); however, the present network meta-analysis could not determine whether age or sex modified AKI risk at the individual-patient level. Accordingly, demographic effect modification by age or sex cannot be excluded and should be explored in future individual-participant-data analyses. Although meta-analyses are sometimes criticized for inconsistencies in endpoint adjudication, they remain an indispensable tool for aggregating safety signals across disparate trials [7,8,243,244]. Our decision to include trials regardless of whether AKI was a primary or secondary endpoint may increase heterogeneity, but also reflects the reality that adverse renal outcomes are often underreported. Importantly, while many of the included RCTs did not explicitly aim to assess AKI risk, renal function changes were frequently monitored as part of safety evaluations. Subgroup analyses were used to minimize the confounding effect of underlying renal disease. We emphasize that all-cause dropout should not be interpreted as corroborative evidence for the AKI findings. This endpoint is influenced by multiple nonrenal factors, including efficacy, gastrointestinal adverse effects, adherence, follow-up duration, and trial design, and therefore serves only as a broad tolerability measure. Accordingly, the dropout analysis was retained only for descriptive tolerability context and not for validation of renal safety signals. Because the primary signal was based on sparse-event data with wide credible intervals, and because many clinically relevant active-comparator contrasts were informed predominantly by indirect evidence, the present findings should be viewed primarily as hypothesis-generating rather than as definitive comparative evidence of drug-specific renal harm. Consistent with this, GRADE certainty varied across comparisons rather than remaining uniformly high across the network. While several placebo-linked contrasts were supported by higher-certainty evidence, many indirect active-versus-active contrasts remained of low certainty because of limited direct evidence and reliance on indirect estimates.

These limitations underscore the need for future large-scale trials specifically designed to assess renal outcomes with emerging glucose-lowering therapies. Prospective trials that incorporate real-time biomarker assessments of tubular stress and injury may further clarify the mechanisms underlying these observations.

We conducted comprehensive searches across multiple databases, including PubMed, Embase, Cochrane CENTRAL, ClinicalTrials.gov, ScienceDirect, ProQuest, Web of Science, and ClinicalKey, covering studies published up to 5 February 2025 (see Table S2). Two independent reviewers (PT Tseng and BY Zeng) screened titles, abstracts, and full texts. Any disagreements were resolved through discussion. Additional studies were identified by manually screening the reference lists of existing systematic reviews [33,45,101,125,129,171], meta-analyses [9,10,26,32,36,38,39,41,43,54,55,63,67,70,72,78,79,83,92,95,99,100,103,108,113,114,115,121,124,126,135,139,143,146,147,150,151,152,164,165,166,169,170], and prior NMAs [42,91,98,137,140,160,161,162]. No restrictions were applied based on language or geographic region.

We applied the PICOS framework (Population, Intervention, Comparison, Outcome, Study Design) to determine study eligibility: Population: Human participants with or without pre-existing renal dysfunction; Intervention: Any GLP-1RA or SGLT2i, regardless of dose; Comparator: Placebo, standard of care, or an active control; Outcomes: Directly reported incidence of AKI; Study design: Randomized controlled trials (RCTs).

Eligible studies were required to directly report AKI outcomes associated with GLP-1RA or SGLT2i interventions. After rechecking all included trials, we confirmed that AKI events were directly reported in the final included dataset.

Exclusion criteria included (1) non-RCTs; (2) RCTs without direct comparison of relevant agents; (3) studies lacking directly reported AKI outcomes; and (4) preclinical or animal trials.

Two reviewers independently assessed study quality using the Cochrane Risk of Bias Tool 1.0 [247]. Disagreements were adjudicated by a third reviewer.

AKI was used as the standardized term throughout this manuscript. Trial-level renal outcome definitions were reviewed individually, and studies were categorized according to whether AKI was explicitly reported or whether acute renal injury-related events were identified through broader renal adverse-event reporting. The diagnosis of AKI was according to KDIGO clinical practice guidelines for AKI [248]. As a secondary outcome, we analyzed all-cause dropout as a broad measure of trial retention and general tolerability, recognizing that it is not a renal-specific safety endpoint.

Dosage categories were defined according to the classification used in the original RCTs [28,97,107,144,172,173,174,175,176,177,178,179,180,181,182,183,184,185,186,187,188,189,190,191,192,193,194,195,196,197,198,199,200,201,202,203,204,205,206,207,208,209,210,211,212,213,214,215,216,217,218,219,220,221,222,223,224,225,226,227,228,229,230,231,232,233]:

Given that baseline renal insufficiency is a well-established risk factor for AKI [4], we performed a subgroup analysis excluding RCTs that specifically recruited patients with advanced renal impairment. This subgroup analysis aimed to isolate drug effects on AKI risk in populations with preserved renal function.

Two investigators (PT Tseng and BY Zeng) independently extracted key trial data, including study design, population characteristics, interventions, outcomes, and adverse event data. Any missing or unclear information was requested from corresponding authors. Extraction procedures adhered to the Cochrane Handbook for Systematic Reviews of Interventions and current best practices in evidence synthesis [249].

We implemented a Bayesian random-effects network meta-analysis in MetaInsight (v4.0.2), using its Bayesian analysis modules implemented through the R packages gemtc, BUGSNET, and bnma [250,251]. Binary outcomes were analyzed using arm-level event-count data (events and sample sizes). For dichotomous outcomes, the Bayesian network meta-analysis was implemented in MetaInsight using a binomial-likelihood framework with an appropriate link function for relative treatment effects. Because the primary endpoint was a rare adverse event, the resulting estimates were interpreted with caution in light of sparse-event data and wide credible intervals.

Effect sizes were reported as odds ratios (ORs) with 95% credible intervals (CrIs) and visualized using forest plots [252]. Four Markov chain Monte Carlo (MCMC) chains were run for 25,000 iterations, discarding the initial 5000 as burn-in. Posterior distributions were sampled with a thinning interval of 1, yielding 80,000 samples for inference. Model priors were set as non-informative, with mean = 0 and consistent precision across arms. Model fit was assessed using residual deviance and leverage plots. Convergence was evaluated by visual inspection of Gelman–Rubin diagnostic plots.

Node-splitting analysis was employed to assess inconsistency between direct and indirect comparisons [251,253]. Treatment rankings were calculated using the surface under the cumulative ranking (SUCRA) curve method and presented using Rank-O-Gram and SUCRA radial plots [254].

To assess the plausibility of transitivity in this predominantly placebo-centered network, we summarized major clinical and design-related effect modifiers across treatment nodes, including age, sex distribution, study duration, the proportion of trials including patients with renal impairment, and the proportion of trials including patients with diabetes mellitus (). These characteristics were examined descriptively to improve transparency regarding the comparability of study populations contributing to indirect comparisons. Table S9

We conducted deviation-based sensitivity analyses to evaluate model stability [255]. The Grading of Recommendations Assessment, Development and Evaluation (GRADE) framework was used to rate the certainty of evidence for all comparisons [256].

This study complied with the principles outlined in the Declaration of Helsinki and was approved by the relevant institutional review board.

Dataset available on request from the authors (The raw data supporting the conclusions of this article will be made available by the authors on request).