https://papers.ssrn.com/sol3/papers.cfm?abstract_id=7172531
there is also a commentary about this: ( Oseltamivir Flops in the Critically Ill)
https://voices.nejm.org/doi/full/10.1056/VOICESpost2600044
chatGPT(5.6paid)
Overall assessment
This is an important and potentially practice-changing REMAP-CAP randomised trial. It provides the first randomised comparison of continued oseltamivir versus no antiviral treatment in patients already critically ill with laboratory-confirmed influenza.
Its most defensible conclusion is:
Starting or continuing oseltamivir after a patient has reached organ-support-level critical illness did not improve outcomes.
The data also raise a credible signal of increased mortality, but the paper overstates the certainty and magnitude of that harm. The trial is substantially stronger for concluding “no evidence of benefit and benefit is unlikely” than for concluding that oseltamivir itself doubles mortality.
Study summary
Design
This was an international, open-label, Bayesian adaptive platform trial within REMAP-CAP.
Participants were:
- Aged at least 12 years.
- Hospitalised with laboratory-confirmed influenza.
- Critically ill and receiving respiratory or cardiovascular organ support.
- Randomised within 48 hours of starting sustained organ support.
- Enrolled at 139 sites in 18 countries between March 2020 and March 2026.
The three reported groups were:
| Treatment | Participants |
|---|---|
| Oseltamivir for 5 days | 162 |
| Oseltamivir for 10 days | 156 |
| No antiviral | 124 |
The recommended oseltamivir dose was 75 mg twice daily, adjusted for renal function where necessary.
The primary outcome was all-cause mortality at 90 days. The adaptive trial stopped recruitment to both oseltamivir groups when each crossed the prespecified inferiority boundary: less than a 0.2% probability of being the best treatment in the antiviral domain.
Population and timing
Patients were already severely ill:
- 47% were invasively ventilated.
- Approximately 42% were receiving vasopressors.
- Median symptom duration before randomisation was five days.
- Randomisation occurred approximately 10–12 hours after ICU admission.
- Only three participants were under 18.
Importantly, 41.8% had already received one dose of oseltamivir before randomisation.
Main results
Mortality
| Group | Deaths by 90 days | Crude mortality |
|---|---|---|
| No antiviral | 17/124 | 13.7% |
| Five-day oseltamivir | 32/162 | 19.8% |
| Ten-day oseltamivir | 30/155 | 19.4% |
The crude absolute excess mortality was therefore approximately six percentage points in each oseltamivir group.
The Bayesian covariate-adjusted estimates were much larger:
- Five days: adjusted OR 2.13, 95% credible interval 1.03–4.52.
- Ten days: adjusted OR 2.17, 95% credible interval 1.05–4.64.
- Pooled oseltamivir: adjusted OR 1.92, 95% CrI 1.00–3.81.
- Posterior probability of harm: approximately 98% for each duration.
- Probability of achieving at least a 20% mortality-odds reduction was only about 0.5%.
There was no evidence that ten days was better than five days.
Secondary outcomes
None of the secondary outcomes indicated benefit from oseltamivir. These included:
- Organ-support-free days.
- ICU-free days.
- Hospital-free days.
- Survival time.
- Progression to invasive ventilation, ECMO or death.
Among patients not invasively ventilated at baseline, progression occurred in:
- 27.1% with five-day oseltamivir.
- 17.8% with ten-day oseltamivir.
- 19.7% with no antiviral.
These estimates were imprecise, but they gave no convincing efficacy signal.
Subgroups
No prespecified subgroup showed evidence of benefit. The probability of harm appeared greater in:
- Patients with shock.
- Patients with proven bacterial coinfection.
- Immunocompromised patients.
- Patients randomised at least five days after symptom onset.
For patients with symptoms for less than five days, however, the probability of harm from pooled oseltamivir was only 55.6%—essentially inconclusive. This timing interaction was not established as statistically convincing, but it is clinically important.
Adverse events and fungal infection
Formally attributed serious adverse events were rare.
Pulmonary Aspergillus was isolated or treated in:
- 1/124, or 0.8%, of the no-antiviral group.
- 12/318, or 3.7%, of the pooled oseltamivir groups.
This is an interesting safety signal, but these were not necessarily centrally adjudicated, systematic diagnoses and the absolute numbers are small.
What is genuinely novel?
1. The first randomised no-antiviral comparison in critical influenza
This is the principal novelty. Oseltamivir became standard treatment in critical influenza largely through:
- Extrapolation from outpatient trials.
- Pharmacological plausibility.
- Observational hospital and pandemic-influenza studies.
The present trial directly tests the treatment in the critically ill population for whom it is routinely recommended.
2. It challenges a deeply embedded treatment assumption
The study shows that observational associations between oseltamivir and lower mortality may not survive randomisation. Possible explanations include confounding by treatment access, early presentation, healthcare quality and clinicians’ selection of patients for treatment.
It is a valuable example of how a plausible and widely accepted intervention can remain inadequately tested in the population receiving it.
3. The 90-day rather than in-hospital mortality endpoint
Much of the observational literature uses in-hospital mortality. The trial instead captures deaths occurring after discharge or transfer, which is a more comprehensive critical-care outcome.
4. Direct comparison of five and ten days
The study finds no evidence supporting an extended ten-day course. This directly challenges recommendations to prolong oseltamivir in severe disease.
5. A possible disease-stage-dependent effect
The results suggest that inhibiting viral replication after critical illness is established may be too late—and possibly harmful. That helps distinguish:
- Early antiviral treatment during active viral replication.
- Late treatment during organ failure, epithelial injury, dysregulated inflammation and secondary infection.
The study therefore tests a treatment-stage strategy, not merely a drug.
6. A hypothesis-generating host-neuraminidase mechanism
The authors propose that oseltamivir might affect host neuraminidase-dependent pathways involving:
- Platelet desialylation.
- Neutrophil function.
- Immune responses to Aspergillus.
- Responses during shock and secondary infection.
This is mechanistically interesting, particularly given the Aspergillus imbalance, but remains speculative.
Strengths
- Randomised design addressing a major evidence gap.
- International recruitment across 18 countries and several influenza seasons.
- Laboratory-confirmed influenza in the main analysis.
- Clinically meaningful 90-day mortality endpoint.
- Prespecified adaptive stopping thresholds.
- Broad consistency across sensitivity analyses.
- Separate analysis restricted to sites genuinely offering no-antiviral randomisation.
- Little evidence of benefit across any secondary outcome.
- Similar findings for five- and ten-day treatment, providing an internal consistency check.
- Randomisation and stopping decisions were concealed from treating teams and the steering committee until the trigger was reached.
Critique
1. The trial supports futility more strongly than definite harm
The crude mortality risk ratio is approximately:
$$
\frac{19.6%}{13.7%}\approx1.43
$$
Yet the reported adjusted odds ratios are around 2.1. Moreover, the paper converts these adjusted odds ratios into estimated absolute mortality increases of approximately 11.6–11.9 percentage points—almost twice the observed crude difference.
That amplification is generated by the modelling and covariate adjustments, not directly observed in the raw data. The authors should explain much more clearly:
- Which covariates drive the change.
- How much is driven by site and eligibility adjustment.
- How much comes from hierarchical borrowing.
- Whether positivity or sparse-site problems affect the estimate.
- Why the model-derived absolute effect should be preferred to the observed six-point difference.
The finding that clinically important benefit is very unlikely is robust. The claim that oseltamivir approximately doubles mortality is less secure.
2. The clean concurrent comparison is considerably smaller
Only 79 of 139 sites offered the no-antiviral group. In the co-eligible population—the patients recruited at sites where no antiviral was actually an option—the comparison was:
- No antiviral: 124 patients.
- Five-day oseltamivir: 69 patients.
- Ten-day oseltamivir: 55 patients.
The corresponding credible intervals crossed one:
- Five days: OR 2.27, 95% CrI 0.88–6.00.
- Ten days: OR 2.19, 95% CrI 0.82–5.69.
The direction is consistent with harm, but uncertainty is substantial. The primary model uses oseltamivir patients from sites that never offered no antiviral and attempts to handle this statistically. That is legitimate within a platform design, but it makes the result more model-dependent than a simple three-arm trial with uniform allocation.
3. Baseline severity was unfavourable in the oseltamivir groups
The groups were not perfectly balanced:
| Characteristic | Five days | Ten days | No antiviral |
|---|---|---|---|
| Invasive ventilation | 47.5% | 53.2% | 38.7% |
| Vasopressors | 43.2% | 55.1% | 37.9% |
| Median APACHE II | 15 | 18 | 16 |
The ten-day group was particularly sick. Randomisation means imbalance can occur by chance, and adjustment is appropriate, but the comparatively small control group makes residual imbalance relevant.
The striking point is that adjustment apparently increases rather than reduces the harm estimate. That deserves a transparent decomposition.
4. Pretreatment complicates the causal question
Before randomisation, one oseltamivir dose had already been received by:
- 50.0% of the five-day group.
- 41.0% of the ten-day group.
- 32.2% of the no-antiviral group.
In addition, 8.9% of the no-antiviral group received oseltamivir after randomisation.
This contamination probably biases a comparison of “any exposure” toward the null. More importantly, it means the trial does not strictly compare oseltamivir-naïve treatment with no oseltamivir. It more closely estimates the effect of assigning continued treatment after critical illness has developed.
Consequently, it cannot determine whether oseltamivir given promptly at symptom onset prevents later progression to critical illness.
5. The conclusion is framed too broadly
The abstract says oseltamivir “is ineffective and highly likely to increase 90-day mortality in critically ill patients.” A more precise conclusion would be:
In patients enrolled after they had developed organ-support-requiring critical illness, assignment to five or ten days of oseltamivir produced no evidence of benefit and was associated with higher 90-day mortality.
That wording preserves the randomised finding without implying that:
- Early outpatient treatment is harmful.
- Treatment before critical deterioration is ineffective.
- The result necessarily applies to pandemic strains.
- The trial has established a drug-specific toxic mechanism.
6. Timing may be central
Median symptom duration was five days, around the point at which viral replication may be waning and inflammatory or secondary-infectious pathology may predominate.
The subgroup findings are compatible with this:
- Symptoms under five days: 55.6% probability of harm.
- Symptoms five days or longer: 97.0% probability of harm.
These exploratory results suggest the aggregate finding might be driven by late treatment. The study lacks the power to establish that interaction, but the manuscript should place more emphasis on it.
7. The mechanism of harm is unproven
The host-neuraminidase hypothesis is biologically plausible but not demonstrated by this trial. The reported Aspergillus difference could reflect:
- A genuine immunological effect.
- Differences in baseline severity.
- More intensive investigation in sicker patients.
- Differences in corticosteroid or antibiotic exposure.
- Chance.
The study did not collect post-randomisation concomitant medications, including corticosteroids and antibiotics. That is a serious limitation for interpreting fungal infection and immune effects.
8. Viral and strain information appears insufficient
Approximately 89% had influenza A, but detailed strain or subtype effects are not presented in the principal report. The trial spans several seasons and both hemispheres, including years with minimal influenza circulation.
It therefore remains uncertain whether the result is homogeneous across:
- A(H1N1)pdm09.
- A(H3N2).
- Influenza B.
- Antiviral susceptibility patterns.
- Pandemic versus seasonal influenza.
This matters because much of the favourable observational evidence came from the 2009 H1N1 pandemic.
9. The adaptive Bayesian estimate is complex and potentially opaque
The model includes:
- Hierarchical borrowing between durations and severity states.
- Adjustment using participants from the broader REMAP-CAP platform.
- Site nested within country.
- Time epochs.
- Eligibility for the no-antiviral group.
- Other platform interventions.
The paper reports sensitivity analyses, but readers need accessible unadjusted and conventionally adjusted estimates alongside the main Bayesian model. A frequentist risk ratio or risk difference with confidence intervals would help show how much of the conclusion is data-driven versus model-driven.
10. Open-label treatment could affect secondary outcomes
Mortality is relatively resistant to ascertainment bias, but open-label allocation could influence:
- Decisions about discharge.
- Duration of ICU treatment.
- Thresholds for intubation.
- Investigation for secondary infection.
- Clinicians’ use of other therapies.
This is especially relevant because concomitant medications were not collected.
11. Some reporting inconsistencies need correction
There are small but notable discrepancies:
- The abstract and Results give harm probabilities of approximately 98.0% and 98.2%, while Table 2 reports 98.3% and 98.9%.
- Table 2 labels “probability of efficacy” as OR >1 in some rows, when efficacy was defined elsewhere as OR <1.
- The abstract’s phrase “met a predefined inferiority threshold” may be misread as proving clinical inferiority; technically, the threshold was a very low probability of being the optimal domain treatment.
These do not overturn the study but should be corrected during peer review.
Interpretation for clinical practice
This trial should prompt reassessment of routine oseltamivir continuation in patients who are already critically ill with seasonal influenza, particularly when:
- Treatment begins late.
- Shock or bacterial/fungal coinfection is present.
- There has been no evidence of ongoing viral replication.
- The rationale is simply that oseltamivir is customary or guideline recommended.
It does not show that early treatment of uncomplicated influenza is ineffective, nor does it establish that treatment initiated before critical deterioration cannot prevent progression.
Bottom line
The paper’s major contribution is not that it has conclusively proved oseltamivir doubles mortality. It is that the first randomised evidence in established critical influenza finds:
- No efficacy signal.
- An extremely low probability of clinically meaningful benefit.
- Consistently worse mortality numerically.
- A credible but still mechanistically unexplained harm signal.
- No justification for extending treatment from five to ten days.
The finding of no benefit is strong and likely practice-changing. The estimated magnitude and causal mechanism of harm require replication, more transparent modelling, strain-specific analysis, and better data on treatment timing, viral load, secondary infection and concomitant drugs.