Do GLP-1 Drugs Lower Tuberculosis Risk? What the New Observational Study Can—and Cannot—Show

A large observational study found lower recorded tuberculosis incidence among people with type 2 diabetes who started a GLP-1 receptor agonist than among matched users of four other glucose-lowering drug classes. That is a consistent association—not proof that GLP-1 drugs prevent tuberculosis.

Published in Nature Communications on August 22, 2026, the study used electronic health records from 143 healthcare organizations across multiple countries. Its size, active-comparator design, matching, sensitivity checks, and negative-control analysis make it more informative than a simple treated-versus-untreated database comparison. Its retrospective design and missing clinical details still leave several credible sources of bias.

The study connected medication records with later tuberculosis diagnosis codes. It did not test a tuberculosis-prevention treatment or establish a causal biological pathway.

Quick answer: do GLP-1 drugs lower tuberculosis risk?

Possibly, but this study cannot establish that they do. Across four separately matched comparisons, GLP-1 receptor agonist users had lower rates of newly recorded tuberculosis than users of sulfonylureas, metformin, DPP-4 inhibitors, or SGLT2 inhibitors.

The safest interpretation is narrow:

• The pattern is large enough and consistent enough to justify further research.
• The records show association, not randomized evidence of prevention.
• The study does not show that GLP-1 drugs treat active or latent tuberculosis.
• The findings do not establish infection protection as a reason to choose one diabetes drug over another.

What did the study find?

The relative association was strongest against DPP-4 inhibitors and weakest against SGLT2 inhibitors. Incidence rates are reported per 1,000 person-years, which accounts for both the number of people and how long they were followed.

| Matched comparison | GLP-1RA TB incidence | Comparator TB incidence | Hazard ratio (95% CI) | |---|---:|---:|---:| | Sulfonylureas | 0.68 | 1.67 | 0.53 (0.47–0.59) | | Metformin | 0.65 | 1.31 | 0.60 (0.51–0.70) | | DPP-4 inhibitors | 0.73 | 1.71 | 0.49 (0.43–0.56) | | SGLT2 inhibitors | 0.89 | 1.02 | 0.82 (0.72–0.92) |

A hazard ratio below 1 means the outcome was recorded less often over follow-up in the GLP-1RA cohort. It does not tell us why. Against SGLT2 inhibitors, the difference was much smaller: 0.13 fewer recorded cases per 1,000 person-years, compared with differences near or above 0.66 against the other classes.

That smaller comparison is not a nuisance to smooth away. It is evidence that the apparent association depends partly on which treatment group serves as the reference.

How was the study designed?

This was an active-comparator, new-user retrospective cohort study—not a clinical trial. The researchers searched TriNetX electronic health records from 2017 through 2025 for adults with type 2 diabetes starting one of the studied drug classes.

Four pairwise cohorts compared GLP-1 receptor agonists with:

1. sulfonylureas;
2. metformin;
3. DPP-4 inhibitors; or
4. SGLT2 inhibitors.

For each comparison, people with any earlier record of either the index or comparator class were excluded. This stricter exposure washout was separate from the 12-month window used to measure baseline covariates. Participants were assigned according to the first eligible drug class initiated, with follow-up beginning on that prescription date. The primary analysis used an intention-to-treat approach for up to five years, so later switching or discontinuation did not reassign exposure.

Tuberculosis was identified from recorded ICD-10-CM diagnosis codes: A15 for pulmonary TB, A17 for nervous-system TB, A18 for TB of other organs, and A19 for miliary TB. These are coded clinical outcomes, not centrally adjudicated cases with microbiology, imaging, or chart review.

What does propensity-score matching improve?

Matching made the compared groups more similar on recorded baseline factors, but it could not make treatment assignment random. Within each pair, the researchers estimated each person’s probability of receiving a GLP-1 receptor agonist based on measured characteristics, then created equal-sized matched cohorts.

The matching model included age, sex, race, BMI, HbA1c, diabetes complications, kidney and cardiovascular conditions, chronic respiratory disease, cancer, autoimmune and silica-related conditions, dialysis, malnutrition, and relevant medications. It also included available proxies for housing and economic problems, education, employment, occupational exposure, alcohol-related disorders, and nicotine dependence.

After matching, reported standardized mean differences were below 0.10. That supports balance on the variables the database captured. It cannot balance unrecorded TB exposure, country-level risk, healthcare access, treatment preferences, or socioeconomic conditions that never made it into a code.

Matching filters the recorded data into more comparable groups. The causal question remains on the other side of what the records cannot measure.

Why doesn’t a large matched study prove prevention?

Scale reduces random noise; it does not automatically remove systematic bias. Millions of records can produce precise confidence intervals around a biased estimate if key differences between treatment groups remain unmeasured.

Several limitations matter here.

TB exposure and disease detail were missing

The database did not provide TB contact history, latent-infection status, radiographic findings, bacterial burden, inflammatory markers, or reliable disease-severity measures. Those omissions prevent the study from separating lower exposure, lower progression from latent infection, diagnostic differences, or genuinely altered susceptibility.

Dose and adherence were unavailable

The researchers could not reliably analyze dose-response relationships or whether prescriptions were taken. A medication order is evidence of prescribing, not proof of sustained biological exposure.

Geography and socioeconomic conditions may still confound the result

TriNetX combined organizations across multiple countries, where background TB incidence and prescribing patterns differ. Available socioeconomic codes were used, but these codes are incomplete proxies. Country of origin, local TB prevalence, crowding, income, and access to care could remain uneven between groups.

Treatment stage differed between comparators

Metformin is commonly used earlier in type 2 diabetes care than GLP-1 receptor agonists. The authors treated it as a benchmark rather than a perfectly interchangeable treatment choice. DPP-4 and SGLT2 inhibitors are more clinically comparable later-line alternatives, yet even those groups may differ for reasons that influence infection detection or risk.

The curves separated early

Relatively early separation of the time-to-event curves raises the possibility of time-related confounding or pre-existing differences. Schoenfeld-residual tests did not find a statistically significant proportional-hazards violation (reported p-values above 0.05), but that test does not prove the early split was biological. The authors acknowledged that unmeasured time-related factors could not be excluded.

Treatment changes were not modeled over time

The primary intention-to-treat analysis kept people in their starting group regardless of later switching or discontinuation. TriNetX did not support the preferred time-varying exposure model with censoring at those changes. This can blur what sustained treatment exposure actually means.

What was wrong with one sensitivity analysis?

An exposure-restricted sensitivity analysis introduced immortal time bias and should be interpreted cautiously. It required a later prescription during years one through five and excluded people with comparator exposure during follow-up.

That uses future information to decide who qualifies. A participant must remain alive, observable, and eligible long enough to satisfy the rule, creating an “immortal” interval during which the outcome cannot be counted in the same way. A peer reviewer identified this problem, and the authors explicitly accepted it.

The primary new-user analysis did not use that future-exposure eligibility rule. Still, the flawed sensitivity analysis cannot be used as clean confirmation of the main finding. The correct future test would model treatment and switching over time, which the platform could not do.

What did the negative-control analysis add?

The skin-cancer negative control was reassuring, but it did not eliminate residual confounding. The investigators selected an outcome not expected to be caused by GLP-1 receptor agonists. Hazard ratios stayed near 1 across all comparisons: 0.99 against sulfonylureas, 0.97 against metformin, 1.02 against DPP-4 inhibitors, and 1.03 against SGLT2 inhibitors, with every confidence interval including 1.

If the same large bias had appeared for an unrelated outcome, confidence in the TB association would fall. Its absence is useful. But a negative control only detects confounding patterns that affect that control outcome similarly; TB-specific geographic, socioeconomic, exposure, or diagnostic factors can remain.

Why do the SGLT2 and extrapulmonary results matter?

They caution against describing GLP-1 receptor agonists as universally protective. The SGLT2 comparison produced the smallest main association, and in the U.S.-restricted analysis it attenuated to HR 0.94 (95% CI 0.83–1.06), compatible with no difference.

For extrapulmonary TB, the comparisons were not uniformly significant. The confidence intervals crossed 1 for metformin (HR 0.90, 0.65–1.23) and SGLT2 inhibitors (HR 0.81, 0.63–1.04), although associations remained below 1 against sulfonylureas and DPP-4 inhibitors.

These results do not disprove a possible effect. They show why “GLP-1 drugs protect against TB” is too broad. The estimate changes by comparator, geography, and TB subtype.

What can researchers reasonably conclude?

The study supports a research hypothesis, not a prevention claim. A plausible anti-inflammatory or immune-modulatory mechanism may motivate laboratory work and better-designed clinical studies. Mechanistic plausibility cannot repair missing exposure data or turn nonrandom prescribing into randomization.

Stronger evidence would require designs with verified TB outcomes, latent-infection and contact data, geographic context, dose and adherence measurement, and time-varying treatment models. Randomized evidence would be needed before claiming that GLP-1 receptor agonists prevent TB.

For broader context, GLP-1 Peptides vs Research Peptides explains how regulated GLP-1 medicines differ from loosely marketed research compounds. How to Evaluate Peptide Claims Online and Peptide Research Status Explained provide a wider evidence-literacy framework.

Frequently asked questions

Did the study prove GLP-1 drugs prevent tuberculosis?

No. It found lower recorded TB incidence in matched observational cohorts. Randomized prevention evidence was not generated.

Did researchers test GLP-1 drugs as TB treatment?

No. The study examined incident diagnosis codes among people with type 2 diabetes. It did not test treatment of active or latent infection.

Why use four comparator drug classes?

Each comparator represents a different prescribing context. Seeing a similar direction across several groups improves robustness, while the smaller SGLT2 estimate reveals important comparator dependence.

Were all TB cases clinically confirmed?

The analysis used ICD-10-CM diagnosis codes in routine electronic health records. It lacked centralized microbiological, radiographic, and severity confirmation.

Was the study independently funded?

The paper states that all authors declared no relevant funding. The authors also declared no competing interests. Their listed affiliations were hospitals and academic institutions in Taiwan.

Sources

1. Liao KM, Wu JY, Lai CC. “Glucagon-like Peptide-1 Receptor Agonists and Risk of Tuberculosis in Type 2 Diabetes.” Nature Communications. Published August 22, 2026. doi:10.1038/s41467-026-77068-0.
2. Supplementary information, including eligibility, covariate, outcome-code, sensitivity, and negative-control tables.
3. Transparent peer-review file, including author responses about cohort construction, early curve separation, and immortal time bias.
4. Source-data workbook.

This article is for general education. It does not provide TB screening or treatment guidance, medication-selection advice, or instructions to start, stop, dose, or change any drug.