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Trial Summaries & Critiques

LAIS

image: shutterstock / BelezaPoy

CT scan of a large left sided stroke

Publication

  • Title: Loberamisal for Acute Ischemic Stroke: The LAIS Randomized Clinical Trial.
  • Acronym: LAIS — Loberamisal for Acute Ischaemic Stroke.
  • Year: 2026; published online 10 September.
  • Journal published in: JAMA.
  • Citation: Li S, Feng B, He D, Wang X, Li H, Xu S, et al; LAIS Investigators. Loberamisal for Acute Ischemic Stroke: The LAIS Randomized Clinical Trial. JAMA. Published online September 10, 2026.

Context & Rationale

  • Background
    • Reperfusion does not address every component of ischaemic brain injury, and many patients present outside reperfusion treatment windows or remain disabled despite treatment.
    • Loberamisal, also designated Y-3 or ZL006-05, disrupts postsynaptic density protein 95–neuronal nitric oxide synthase coupling and potentiates α2-containing GABAA receptors.
    • Preclinical experiments suggested reduced excitotoxic injury, effects on inflammation and recovery, and antidepressant and anxiolytic activity. These mechanisms provide a rationale; their contribution to recovery in humans remains unproven.1
    • A preceding 240-patient phase II trial tested 20, 40 and 60 mg daily. The 40 mg group had the highest proportion with mRS 0–1 at 90 days, but the overall comparison across the four groups was inconclusive: P=0.164.2
  • Research Question/Hypothesis
    • Would a 10-day course of intravenous loberamisal, begun within 48 hours of acute ischaemic stroke, increase the proportion of patients with no significant disability at 90 days compared with placebo?
    • The hypothesis concerned an adjunct to standard care in patients not undergoing thrombectomy; it did not test replacement of reperfusion treatment.
  • Why This Matters
    • A treatment effective beyond the first few hours could address a substantial unmet need.
    • A convincing clinical benefit would challenge the repeated difficulty of translating experimental neuroprotection into improved patient outcomes.
    • The distinction between preventing dependency and improving recovery among already independent survivors is central to interpreting LAIS.

Design & Methods

  • Research Question:
    • In adults with acute ischaemic stroke within 48 hours, NIHSS 7–20 and prestroke mRS 0–1, does loberamisal improve 90-day mRS 0–1 compared with placebo?
  • Study Type:
    • Multicentre, randomised, double-blind, parallel-group, placebo-controlled phase III superiority trial at 32 hospitals in China; an acute stroke hospital population rather than an ICU-specific cohort.
    • Recruitment: 24 July–7 December 2024; final follow-up: 8 April 2025.
    • Central web-based 1:1 allocation, stratified by centre and onset-to-randomisation time, ≤12 versus >12 hours.
    • Industry-sponsored, with support from NeuroDawn Pharmaceutical and the National Natural Science Foundation of China; registered as NCT06517173.
    • The rationale and design were published separately.3
  • Population:
    • Age 18–80 years; imaging-confirmed acute ischaemic stroke within 48 hours; NIHSS 7–20, including a combined arm and leg motor score of at least 2; prestroke mRS 0–1.
    • Intravenous thrombolysis was permitted; previous or planned thrombectomy or other interventional treatment for the presenting stroke was excluded.
    • Other important exclusions: NIHSS consciousness item 1a >1; persistent systolic pressure ≥220 or diastolic pressure ≥120 mm Hg despite treatment; significant intracranial haemorrhage; active major liver or kidney disease, ALT/AST >2 times the upper limit of normal or creatinine >1.5 times that limit; and expected survival below 90 days.
    • Patients with previous depression or anxiety, antidepressant or anxiolytic treatment, severe psychiatric illness or dementia were excluded.
    • Prior use of specified neuroprotective medicines after stroke onset also precluded enrolment; written consent came from the patient or a legally authorised representative.4
  • Intervention:
    • Loberamisal 40 mg intravenously once daily for 10 consecutive days, with standard stroke care.
    • The reconstituted preparation was diluted in 250 mL of 0.9% sodium chloride and infused over 60±10 minutes through a dedicated line.
    • The first dose was given as soon as feasible after randomisation; the second followed 12–25 hours after the first infusion started, and subsequent doses were scheduled every 24±1 hours, with a maximum of 10 doses.
    • All infusions occurred during hospitalisation; infusion slowing, interruption or discontinuation was permitted for intolerance.4
  • Comparison:
    • Matching intravenous placebo on the same 10-day schedule, with standard stroke care.
    • Background care permitted antiplatelet treatment, management of vascular risk factors and rehabilitation; eligible patients could receive intravenous thrombolysis.
    • Other specified neuroprotective drugs, including edaravone and edaravone dexborneol, were prohibited. The SAP specified no protocol rescue treatment.45
  • Blinding:
    • Participants, investigators, treating staff, outcome assessors and statisticians were masked; study preparations had matching appearance, packaging and labelling.
    • Certified local assessors used a simplified mRS questionnaire, in person or by telephone.
  • Statistics:
    • Power calculation: Assuming mRS 0–1 in 71.5% versus 60.7%, 798 evaluable patients were required for 90% power (β=0.10), with two-sided α=0.05; allowing 20% attrition increased the target to 998.
    • Analysis population: Modified intention-to-treat: all randomised participants receiving at least one dose; per-protocol analyses were supportive.
    • Primary outcome: mRS 0–1 at 90 days; mRS 0 denotes no symptoms, and mRS 1 permits symptoms without significant disability.
    • Estimand: Death, discontinuation for lack of efficacy and prohibited medicines affecting efficacy assessment counted as failure. Outcomes after discontinuation for adverse events or other reasons remained eligible for analysis.
    • Missing data: Remaining missing outcomes were imputed in 100 datasets separately by treatment group under a missing-at-random assumption.
    • Effect estimation: Generalised linear models estimated risk ratios and risk differences, adjusting for the onset-to-randomisation stratum; estimates were pooled using Rubin’s rules.
    • Multiplicity: One primary estimand; secondary and exploratory comparisons had no multiplicity adjustment.
    • Other analyses: Prespecified sensitivity analyses addressed missingness and covariate handling; an ordinal mRS analysis and subgroup interaction tests were planned. No interim analysis was planned.5
  • Follow-Up Period:
    • Assessments through 90 days, including NIHSS at days 10 and 30 and functional and mood outcomes at day 90.

Key Results

This trial was not stopped early. Recruitment reached 998 participants. One placebo-assigned patient developed acute myocardial infarction before treatment and received no study drug, leaving 997 in the primary and safety populations: 502 versus 495.

Efficacy counts and percentages below are the published estimates averaged across imputations, with counts rounded; they are not simply observed event counts. Safety counts are observed. RR denotes risk ratio; RD denotes absolute risk difference in percentage points. Exact efficacy P values were not reported in the main results table; the published 95% confidence intervals are shown. Secondary analyses are exploratory.56

Outcome Loberamisal Placebo Effect p value / 95% CI Notes
mRS 0–1 at 90 days 350 (69.7%) 279 (56.3%) RR 1.24;
RD +13.28		 RR: 1.12 to 1.36;
RD: +7.24 to +19.32		 Primary outcome; favoured loberamisal.
Favourable sliding-dichotomy mRS at 90 days 246 (49.0%) 197 (39.8%) RR 1.23;
RD +9.30		 RR: 1.07 to 1.42;
RD: +3.08 to +15.52		 Success threshold varied with baseline NIHSS.
Ordinal mRS at 90 days Median 1; IQR 1–2 Median 1; IQR 1–2 Common OR not estimated Proportional-odds assumption test: P<0.001 This P value tests the model assumption, not treatment benefit.
mRS 0–2 at 90 days 387 (77.1%) 383 (77.3%) RR 1.00;
RD −0.21		 RR: 0.93 to 1.07;
RD: −5.54 to +5.12		 Post hoc functional-independence threshold; no demonstrated benefit.
NIHSS improvement ≥4 points at day 10 225 (44.7%) 243 (49.0%) RR 0.91 0.80 to 1.04 No demonstrated early neurological benefit.
NIHSS improvement ≥4 points at day 30 369 (73.5%) 360 (72.7%) RR 1.01 0.94 to 1.09 No demonstrated benefit.
Barthel Index ≥95 at 90 days 355 (70.7%) 348 (70.4%) RR 1.00 0.92 to 1.09 No demonstrated improvement in this activities-of-daily-living measure.
All-cause mortality 6/502 (1.2%) 10/495 (2.0%) Not reported Not reported Observed safety deaths; too few to establish a survival effect.
Any adverse event 441/502 (87.8%) 439/495 (88.7%) Not reported Not reported Numerically similar incidence.
Serious adverse event 43/502 (8.6%) 53/495 (10.7%) Not reported Not reported No clear excess signal; not evidence of equivalent safety.
Treatment stopped for adverse events 6/502 (1.2%) 6/495 (1.2%) Not reported Not reported No suspected unexpected serious adverse reactions were reported.
  • Primary result and robustness:
    • The published absolute improvement was 13.28 percentage points, with a 95% CI of 7.24 to 19.32 percentage points at the chosen threshold.
    • Counting all missing primary outcomes as failures gave 67.9% versus 54.7%; RR 1.24; 95% CI 1.12 to 1.37.
    • The per-protocol result was 71.6% versus 58.6%; RR 1.22; 95% CI 1.11 to 1.34.
    • The published tipping-point analysis retained an RR lower confidence limit above 1 across all combinations of success or failure among the 14 versus 20 missing outcomes.6
  • Pattern of benefit:
    • The ordinal table showed mRS 1 in 46.1% versus 35.1%, and mRS 2 in 7.8% versus 21.1%; mRS 0 occurred in 24.5% versus 22.7%.
    • This pattern concentrates the difference around the mRS 1–2 boundary; it does not demonstrate a uniform improvement across disability levels.
    • The sliding dichotomy used mRS 0 for baseline NIHSS 4–7, mRS 0–1 for NIHSS 8–14, and mRS 0–2 for NIHSS 15–25; it partly reuses the primary threshold rather than independently confirming benefit across a different domain.6
  • Subgroups:
    • Onset-to-treatment ≤12 hours: RR 1.16; 95% CI 0.94 to 1.43; >12–24 hours: RR 1.22; 95% CI 1.02 to 1.46; >24 hours: RR 1.25; 95% CI 1.09 to 1.43; interaction P=0.80.
    • With intravenous thrombolysis: RR 1.26; 95% CI 0.97 to 1.64; without: RR 1.22; 95% CI 1.10 to 1.36; interaction P=0.81.
    • These exploratory comparisons found no convincing interaction; they do not prove equal efficacy at every treatment time or establish benefit in the 171 patients receiving thrombolysis.6

Internal Validity

  • Randomisation and allocation:
    • Central allocation after eligibility confirmation supported concealment; centre and time stratification reduced imbalance in important design factors.
    • The primary model adjusted for the time stratum, but not centre; this matched the academic SAP.5
  • Post-randomisation exclusions and missing outcomes:
    • One of 998 randomised participants was excluded before receiving placebo; the principal analysis was therefore modified, rather than full, intention-to-treat.
    • Missing 90-day outcomes affected 14/502 (2.8%) versus 20/495 (4.0%); the primary conclusion was insensitive to the published alternative assumptions.
    • The per-protocol population included 475 versus 461 participants; concordance is supportive but does not remove selection inherent in excluding post-randomisation deviations.6
  • Performance and detection bias:
    • Matching placebo and masking of patients, staff and assessors reduced differential care and ascertainment.
    • The primary outcome remained an assessor-rated functional judgement, collected locally rather than centrally.
    • Formal assessment of masking success and the proportions assessed by telephone versus in person were not reported.
  • Protocol adherence and treatment separation:
    • Mean doses delivered: 9.9±1.0 versus 9.7±1.4.
    • Adherence of 80–120% of planned treatment: 492/502 (98.0%) versus 477/495 (96.4%).
    • Any protocol deviation: 185/502 (36.9%) versus 186/496 (37.5%); major deviations: 18 (3.6%) versus 19 (3.8%). The larger totals mostly reflected procedural or laboratory deviations.
    • Prohibited medicines were used by 12 (2.4%) versus 13 (2.6%); thus contamination was limited and balanced.
    • Four deviations categorised under randomisation/blinding concerned incorrect stratification entries, rather than documented disclosure of allocation.6
  • Baseline characteristics and heterogeneity:
    • Median age was 64 years in both groups; median NIHSS was 8, with IQR 7–8 versus 7–9.
    • Women comprised 36.1% versus 31.3%; prestroke mRS 0 occurred in 91.4% versus 91.7%.
    • Most measured prognostic characteristics were similar. The narrow observed severity distribution reduced clinical heterogeneity within the trial.
    • Only five participants per group had NIHSS ≥15; neither group had a primary-outcome responder in this subgroup.6
  • Timing, dose and co-interventions:
    • Median onset-to-first-dose time was 25.2 hours (IQR 17.0–33.3) versus 25.5 hours (IQR 17.0–32.7); 53.4% versus 55.2% began treatment after 24 hours.
    • Intravenous thrombolysis was used in 82/502 (16.3%) versus 89/495 (18.0%).
    • The 40 mg dose was supported by exploratory phase II findings; phase III tested neither alternative doses nor shorter treatment courses.2
    • Comparative rehabilitation intensity and detailed use of permitted background medicines were not reported, limiting assessment of their balance.
  • Statistical rigour and oversight:
    • The planned recruitment target was achieved, missingness was below the allowance, and the primary confidence interval excluded no effect.
    • The academic SAP was dated 21 January 2025, after recruitment but before database lock and unblinding on 18 April 2025.
    • Academic and regulatory statistical teams analysed the locked data independently and compared results; the academic team was described as operationally independent of the sponsor and principal investigator.56
    • The publication declared no author conflicts and stated that funders had no role in design, conduct, analysis or publication decisions.

Conclusion on Internal Validity: Internal validity is strong for the primary randomised comparison, supported by concealment, extensive masking, high treatment adherence and robust sensitivity analyses. Confidence is lower in the breadth of clinical benefit and in uncommon harms; local outcome assessment and changes between analysis documents merit scrutiny.

External Validity

  • Population representativeness:
    • Direct applicability is greatest to previously independent adults aged ≤80 years with predominantly moderate deficits, treated in Chinese stroke hospitals without thrombectomy.
    • The eligibility range NIHSS 7–20 overstates the representation of severe stroke: only 10 patients had NIHSS ≥15.
    • Older patients, those with prior dependency, impaired consciousness, major organ dysfunction or established mood disorders were excluded or poorly represented.
    • The findings provide little direct evidence for patients requiring neurocritical care, including those with large infarctions and severe neurological impairment.
  • Reperfusion and healthcare setting:
    • No thrombectomy population was studied; the thrombolysis subgroup was too small to establish treatment interaction reliably.
    • The small prevalence of atrial fibrillation, 3.0% versus 2.6%, and lack of reported vascular and infarct phenotyping limit comparisons with other stroke populations.
    • Ten inpatient intravenous infusions create staffing, bed-use and delivery implications where stroke admissions are shorter.
    • A shortened course, outpatient administration or an oral alternative cannot be assumed to reproduce this regimen’s effect.7

Conclusion on External Validity: Generalisability is moderate for patients resembling those enrolled and limited for broader international practice. The results should not be extrapolated to thrombectomy recipients, very severe stroke, prestroke dependency or abbreviated treatment regimens without further evidence.

Strengths & Limitations

  • Strengths:
    • Large multicentre placebo-controlled trial with concealed allocation and masking extending to assessors and statisticians.
    • Clinically relevant 90-day primary outcome and completion of planned recruitment.
    • High adherence and modest, reasonably balanced missingness.
    • Consistent primary effects across multiple sensitivity analyses, including the regulatory method.
    • Accessible protocol versions, academic SAP and detailed supplementary results.
  • Limitations:
    • Functional benefit was concentrated at one mRS threshold, without corroboration from NIHSS, Barthel function or the post hoc independence threshold.
    • Local functional ratings and different intercurrent-event strategies across analyses complicate interpretation.
    • One-country recruitment, exclusion of thrombectomy and minimal representation of severe stroke.
    • No direct evidence establishing the mechanism, optimal treatment window or minimum effective course.
    • Limited power for mortality, uncommon harms and interactions with reperfusion treatment; follow-up restricted to 90 days in this report.

Interpretation & Why It Matters

  • A credible primary finding
    • The trial supports a substantial increase in reaching mRS 0–1 under the specified treatment and analysis strategy.
    • Low attrition and sensitivity analyses make missing outcomes an unlikely explanation for the entire primary effect.
  • A specific clinical benefit
    • mRS 1 generally permits usual activities despite symptoms; mRS 2 denotes independence in personal affairs but inability to perform all previous activities.
    • Improvement around this boundary can matter substantially to patients, but differs from preventing dependency or death.
    • The absence of clear benefits on other measures does not invalidate the primary outcome; it limits claims about the range of benefit and warrants replication.
  • Implications for practice
    • LAIS provides a strong reason for independent confirmatory trials of loberamisal.
    • It does not establish efficacy alongside thrombectomy, an optimal 48-hour biological window, or permission to delay established reperfusion treatment.
    • Routine international adoption requires confirmation of benefit, safety and feasibility in the populations and care pathways where the drug would be used.

Controversies & Other Evidence

  • Clinical meaning of the primary estimand:
    • Classifying prohibited medication or discontinuation for inefficacy as failure means the primary outcome combines functional status with aspects of the treatment course.
    • The ordinal analysis instead retained measured outcomes after these events under a treatment-policy strategy. Its category totals therefore need not reproduce the primary binary result.
    • These are different clinical questions, not merely alternative statistical presentations of identical data; a clearly reported binary treatment-policy analysis would aid interpretation.5
  • Analysis changes and transparency:
    • The December 2023 protocol already specified 90-day mRS 0–1. The September 2024 amendment, during recruitment, revised the estimand and added analyses following regulatory feedback.
    • The amended protocol specified a Mantel–Haenszel approach with last observation carried forward; the academic SAP specified generalised linear models with multiple imputation.
    • The reported regulatory-method sensitivity analysis gave RR 1.24; 95% CI 1.12 to 1.37, and RD 13.10 percentage points; 95% CI 7.12 to 19.09. Thus the conclusion did not depend on choosing the academic method.
    • The academic SAP preceded unblinding, but was not finalised before recruitment; the design article appeared online in December 2025, after follow-up. These distinctions should accompany any claim of complete prospective prespecification.3456
  • Disability distribution and outcome ascertainment:
    • The failure of the proportional-odds assumption is consistent with an effect that varies across disability thresholds. It prevents a straightforward common-odds-ratio summary; it does not itself test whether treatment works.
    • The primary difference could represent a meaningful improvement in resuming usual activities, but local ratings at the mRS 1–2 boundary make standardised, centrally adjudicated replication particularly valuable.
    • There is no documented evidence that masking failed. Nevertheless, the absence of central assessment or a formal masking assessment leaves detection bias incompletely characterised.7
    • Figure 2 labels the placebo group as n=494, whereas the primary population is n=495; this denominator discrepancy is unexplained. Imputed mRS death-category estimates also should not be substituted for the observed safety deaths.
  • Biological plausibility and treatment timing:
    • Saver highlights the unusually large functional effect, limited independent translational validation and need to distinguish acute tissue protection from later neural repair.7
    • The published preclinical study used both rats and mice; the stronger concern is independent reproducibility and translation, rather than the editorial’s literal claim of evidence from only one species.17
    • A median treatment delay near 25 hours and 10 days of exposure permit several possible mechanisms. LAIS did not establish which mechanism caused the clinical difference.
    • No thrombectomy and infrequent thrombolysis do not establish permanent vascular occlusion: recanalisation status was not measured in the reported analyses.
    • The timing interaction P=0.80 does not prove that delaying treatment is harmless or that efficacy is constant throughout 48 hours.
  • Dose selection, mood effects and safety:
    • The phase II 40 mg group achieved mRS 0–1 in 76.7% versus 60.7% with placebo, but the small dose groups and inconclusive overall comparison did not establish an optimal dose or a reproducible dose–response relationship.2
    • LAIS did not clearly demonstrate the proposed mood benefits: MADRS ≥22 occurred in 4.9% versus 7.8%, RR 0.63; 95% CI 0.38 to 1.04; HAMA ≥21 occurred in 4.7% versus 7.2%, RR 0.66; 95% CI 0.39 to 1.11.6
    • Similar overall adverse-event rates are reassuring for this selected population, but cannot establish rare-event safety or safety with thrombectomy and intensive reperfusion strategies.
  • Related PSD-95 evidence:
    • ESCAPE-NEXT randomised 850 thrombectomy patients not receiving thrombolysis. Nerinetide did not improve 90-day mRS 0–2: 45% versus 46%; OR 0.97; 95% CI 0.72 to 1.30; P=0.82.8
    • A post hoc individual-participant meta-analysis selected 690 patients from ESCAPE-NA1, ESCAPE-NEXT and FRONTIER who were enrolled within 3 hours and selected for reperfusion. Trial-defined response occurred in 56% versus 48%; adjusted OR 1.48; 95% CI 1.07 to 2.06; P=0.017.9
    • That selected early-treatment signal is hypothesis-generating. Different drugs, populations, windows and outcome definitions prevent it from validating loberamisal or a general PSD-95 treatment effect.
  • Other recent trials:
    • TASTE-SL randomised 914 patients in China: sublingual edaravone dexborneol increased mRS 0–1 at 90 days, 64.4% versus 54.7%; OR 1.50; 95% CI 1.15 to 1.95; P=0.003. Several other functional outcomes did not improve.10
    • EMPHASIS randomised 1724 patients in China to oral minocycline or placebo within 72 hours: mRS 0–1 occurred in 52.6% versus 47.4%; adjusted RR 1.11; 95% CI 1.03 to 1.20; P=0.0061. Its ordinal analysis also favoured minocycline.11
    • These trials support renewed investigation of pharmacological recovery strategies, but are studies of different agents and are not independent replications of LAIS.
  • Guidelines and the evidential position:
    • The 2026 AHA/ASA guideline advises against neuroprotective treatments to improve functional outcome on the evidence then available: class III, no benefit; level A.
    • That guideline was published online in January 2026 and its evidence review preceded the LAIS publication; it should not be portrayed as having evaluated or rejected these results.12
    • The immediate priority is independent multinational confirmation with rigorous outcome adjudication, explicit estimands, appropriate reperfusion cohorts and longer follow-up. Independent statistical programming on the same dataset strengthens reproducibility of analysis but cannot replace independent clinical replication.7

Summary

  • LAIS randomised 998 adults at 32 Chinese hospitals to loberamisal 40 mg intravenously daily for 10 days or placebo, beginning within 48 hours of ischaemic stroke.
  • The primary outcome, mRS 0–1 at 90 days, improved from 56.3% to 69.7%; RR 1.24; 95% CI 1.12 to 1.36; absolute difference 13.28 percentage points.
  • The primary effect persisted across sensitivity analyses, but overall independence, NIHSS recovery and Barthel function did not show clear improvement.
  • No clear overall safety excess emerged; mortality and uncommon harms remained imprecisely characterised.
  • Predominantly moderate stroke, exclusion of thrombectomy, local outcome ratings and a demanding inpatient regimen limit immediate extrapolation; independent confirmation is needed.

Overall Takeaway

LAIS is an important phase III trial showing a substantial, statistically robust improvement in reaching no significant disability at 90 days in a selected stroke population. Its narrower functional pattern and limited applicability require independent confirmation before it can be considered a practice-defining landmark or a basis for routine international use.

Overall Summary

  • Primary finding: More patients reached mRS 0–1 at 90 days with loberamisal; the published absolute improvement was 13.28 percentage points.
  • Key qualification: Benefit was concentrated around the mRS 1–2 boundary, without demonstrated improvement in overall independence or neurological recovery measures.
  • Clinical implication: A promising treatment requiring independent confirmation, especially in international and reperfusion-treated populations.

Bibliography

Added September 11th, 2026