Publication

• Title: Hydroxyethyl Starch 130/0.42 versus Ringer’s Acetate in Severe Sepsis.
• Acronym: 6S — Scandinavian Starch for Severe Sepsis/Septic Shock.
• Year: 2012; published online on 27 June and in the 12 July issue.
• Journal published in: New England Journal of Medicine.
• Citation: Perner A, Haase N, Guttormsen AB, Tenhunen J, Klemenzson G, Åneman A, et al.; 6S Trial Group; Scandinavian Critical Care Trials Group. Hydroxyethyl starch 130/0.42 versus Ringer’s acetate in severe sepsis. N Engl J Med 2012;367:124-134.

Context & Rationale

• Background

  • Hydroxyethyl starch (HES) was widely used for resuscitation, on the premise that more sustained intravascular expansion would achieve haemodynamic goals with less fluid than crystalloid. A physiological or volume-saving effect had not established improved survival.
  • VISEP had identified renal harm with an older, hyperoncotic formulation, 10% HES 200/0.5, in severe sepsis. Debate centred on whether these findings applied to newer 6% tetrastarches with lower molecular weight and molar substitution.¹
  • HES 130/0.4–0.42 had entered practice without an adequately powered assessment of mortality and serious renal outcomes in severe sepsis. The 6S protocol addressed the possibility of either benefit or harm.²
• Research Question/Hypothesis

  • In adults with severe sepsis requiring ICU volume resuscitation, does 6% HES 130/0.42, compared with Ringer’s acetate, change the risk of death or dialysis dependence at 90 days?
  • The trial sought a clinically important difference in this composite outcome; it was not an equivalence or non-inferiority trial.
• Why This Matters

  • A large, blinded comparison of a contemporary starch formulation against a balanced crystalloid could test whether claimed pharmaceutical improvements translated into patient benefit.
  • The chosen outcomes extended beyond immediate circulatory measurements to survival, renal support, bleeding and recovery. This mattered for a resuscitation fluid whose adverse effects might emerge after the initial haemodynamic response.

Design & Methods

• Research Question:
  • Whether assigning HES 130/0.42 rather than Ringer’s acetate for ICU resuscitation alters death or dialysis dependence at day 90, with separate evaluation of mortality and renal and bleeding outcomes.
• Study Type:
  • Investigator-initiated, international, multicentre, parallel-group, blinded randomised trial in 26 general ICUs: 13 university and 13 non-university units in Denmark, Norway, Finland and Iceland.
  • Recruitment ran from 23 December 2009 to 15 November 2011. Eight hundred and four patients underwent randomisation; 798 formed the final modified intention-to-treat population.
  • Computer-generated 1:1 allocation was implemented through the Copenhagen Trial Unit’s central telephone system, available around the clock. Stratification concerned shock, active haematological malignancy and university versus non-university hospital.
  • Funding came from the Danish research councils, Rigshospitalet’s research council and the Scandinavian Society of Anaesthesiology and Intensive Care Medicine’s ACTA foundation. B. Braun supplied fluids without involvement in design, conduct, analysis or reporting; independent Good Clinical Practice monitoring was used.
• Population:
  • Adults aged ≥18 years who needed volume resuscitation according to the ICU clinician and had fulfilled severe sepsis criteria within the preceding 24 hours. This did not require that sepsis itself had first begun within those 24 hours.³
  • Sepsis required an infectious focus and at least two systemic inflammatory response criteria. Severe sepsis additionally required at least one organ SOFA component >2, excluding organ failure already present at least 48 hours before sepsis onset.³
  • Shock was defined by mean arterial pressure <70 mm Hg, ongoing vasopressor or inotropic treatment, or lactate >4 mmol/L within the preceding hour. These alternatives differ from the later Sepsis-3 septic shock definition.
  • The prespecified baseline acute kidney injury subgroup used renal SOFA ≥2: plasma creatinine >170 µmol/L or urine output <500 mL/day. Patients with acute kidney injury could enter, but patients already receiving renal replacement therapy (RRT) could not.
  • Other exclusions comprised >1000 mL of any synthetic colloid in the preceding 24 hours; HES or malic acid allergy; previous 6S enrolment; burns involving >10% of body surface; potassium >6 mmol/L within six hours; and liver or kidney transplantation or intracranial bleeding during the current hospital admission.³
  • Patients were also excluded for withdrawal of active treatment or participation in another ICU drug trial potentially affecting circulation, kidney function or coagulation. Consent procedures, including surrogate consent, followed national requirements.³
• Intervention:
  • 6% potato-derived HES 130/0.42, Tetraspan, in a balanced acetate/malate-containing electrolyte solution, supplied in 500-mL bags for ICU volume resuscitation.
  • Study fluid could be used throughout ICU admission and on readmission to a trial ICU, for up to 90 days. Clinicians determined the volume and rate; equal fluid volumes were not mandated.
  • Both groups had a study-fluid ceiling of 33 mL/kg ideal body weight/day, rounded down to the nearest 500 mL. Ideal weight was height in centimetres minus 100 for men or 105 for women; synthetic colloid received during the preceding 24 hours was deducted from the first-day allowance.⁴
  • The protocol recommended fluid challenges guided by haemodynamic response, with reduction when filling pressures increased without improvement. It did not impose a mandatory cardiac-output algorithm or record which resuscitation targets clinicians actually used.⁴
  • Study fluid was permanently discontinued if RRT, severe bleeding or a severe allergic reaction occurred. Subsequent resuscitation used open-label saline or Ringer’s lactate.
• Comparison:
  • Ringer’s acetate, Sterofundin ISO, in matching 500-mL bags, for the same indications, duration and daily ceiling.
  • If either group reached the study-fluid ceiling, additional resuscitation used open-label Ringer’s acetate. Crystalloids and albumin were permitted for indications other than volume resuscitation; blood products were available for specific clinical indications.
  • Other care remained at clinician discretion. RRT initiation criteria and transfusion thresholds were not standardised as compulsory trial algorithms.
  • Fluid treatment outside the ICU was not controlled; transfer to a non-trial ICU ended study-fluid administration but did not end outcome follow-up.⁴
• Blinding:
  • Identical fluid containers were enclosed in sealed, opaque black bags by staff outside patient care and data collection. Patients, clinicians, investigators, statisticians and the writing committee were blinded.
  • The monitoring committee initially reviewed coded groups and could request disclosure when necessary. An abstract was drafted with the groups labelled 0 and 1 before treatment identity was revealed, providing a concrete safeguard against interpretation influenced by allocation.³⁴
• Statistics:
  • Power calculation: 800 patients were required to detect a 10-percentage-point absolute reduction in death or dialysis dependence, from 50% to 40%, with 80% power (β=0.20) and two-sided α=0.05.
  • The primary comparison used the modified intention-to-treat population, an unadjusted χ² test and relative risk with a 95% confidence interval. Logistic regression provided adjusted odds ratios, using stratification variables and prespecified prognostic factors.
  • Two per-protocol analyses and subgroup comparisons according to baseline shock and acute kidney injury were specified. Secondary outcomes and subgroup analyses were not adjusted for multiplicity.⁴
  • One interim analysis followed 90-day follow-up of 400 patients. The Haybittle–Peto boundary was P<0.001; the independent monitoring committee could also recommend stopping for safety or compelling external evidence.⁴
  • The original protocol was unchanged during recruitment. Changes to the statistical analysis plan were documented on 5 March 2012, before analysis and unblinding; the primary outcome remained unchanged.⁴
• Follow-Up Period:
  • The primary outcome was death or dialysis dependence at 90 days. Dialysis dependence meant any RRT during days 86–94, an operational definition that does not by itself establish irreversible end-stage kidney disease.⁴
  • Secondary outcomes included 28-day mortality, any RRT during 90 days, renal dysfunction, bleeding, severe allergic reactions, day-5 SOFA excluding the Glasgow Coma Scale, and proportions of days alive without organ support or outside hospital.
  • Severe bleeding was defined in the main publication as clinical bleeding requiring at least three units of packed red cells within 24 hours. The renal composite comprised RRT or renal SOFA ≥3 after a baseline score ≤2.
  • Six-month and one-year mortality were planned for subsequent assessment. Follow-up for the primary publication ended on 16 February 2012, with at least 90 days available for every analysed patient.

Key Results

This trial was not stopped early. Recruitment reached the planned sample after one interim analysis. The primary analysis included 398 patients assigned to HES and 400 assigned to Ringer’s acetate.

Outcome	HES 130/0.42	Ringer’s acetate	Effect	p value / 95% CI	Notes
Death or dialysis dependence at 90 days	202/398 (51%)	173/400 (43%)	RR 1.17	95% CI 1.01 to 1.36; P=0.03	Primary outcome.
Death at 90 days	201/398 (51%)	172/400 (43%)	RR 1.17	95% CI 1.01 to 1.36; P=0.03	Almost entirely explains the composite result.
Dialysis dependence at 90 days	1/398 (0.25%)	1/400 (0.25%)	Not reported	P=1.00	Only two events; substantial competing mortality.
Death at 28 days	154/398 (39%)	144/400 (36%)	RR 1.08	95% CI 0.90 to 1.28; P=0.43	Earlier mortality assessment.
Any RRT within 90 days	87/398 (22%)	65/400 (16%)	RR 1.35	95% CI 1.01 to 1.80; P=0.04	Important secondary safety outcome.
Severe bleeding	38/398 (10%)	25/399 (6%)	RR 1.52	95% CI 0.94 to 2.48; P=0.09	One missing observation in the Ringer’s group.
RRT or new renal SOFA ≥3	129/398 (32%)	108/400 (27%)	RR 1.20	95% CI 0.97 to 1.48; P=0.10	Renal SOFA criterion required baseline score ≤2.
Doubling of plasma creatinine	148 (41%)	127 (35%)	RR 1.18	95% CI 0.98 to 1.43; P=0.08	38 versus 34 observations missing; reference was usual pre-admission creatinine.34
Packed red-cell transfusion	220/377	173/380	RR 1.28	95% CI 1.12 to 1.47; P<0.001	Blood-product exposure; available-data denominators.3
Cumulative study-fluid volume	3000 mL (1507–5100)	3000 mL (2000–5750)	Not reported	P=0.20	Median (IQR); no demonstrated volume-saving advantage.
Proportion of days alive without RRT	91%	93%	Not reported	P=0.048	Mean patient-level proportion; denominator was days alive.
Proportion of days alive without ventilation	62%	65%	Not reported	P=0.28	Mean proportion; not conventional ventilator-free days.
Proportion of days alive outside hospital	29%	34%	Not reported	P=0.048	Mean proportion; not a fixed 90-day denominator.

• HES increased the primary outcome and 90-day mortality. The publication gives an absolute mortality increase of 8 percentage points and a number needed to harm of 13; this estimate is specific to the trial’s population and treatment strategy.
• For the primary outcome, patients with baseline shock had 179/336 versus 148/337 events: RR 1.21; 95% CI 1.04 to 1.42. Without shock, events were 23/62 versus 25/63: RR 0.93; 95% CI 0.60 to 1.46. The interaction P=0.22 does not establish a different effect by shock status.
• With baseline acute kidney injury, primary events were 72/142 versus 63/140: RR 1.13; 95% CI 0.88 to 1.44. Without baseline injury, events were 130/256 versus 110/260: RR 1.20; 95% CI 1.00 to 1.45. Interaction P=0.60 provides no evidence that harm was confined to patients with pre-existing acute kidney injury.

Internal Validity

• Randomisation and Allocation:
  • Central allocation and masking made foreknowledge of treatment unlikely. Stratification addressed three important prognostic or organisational features; individual trial centre was not a randomisation stratum.
• Dropouts and Post-randomisation Exclusions:
  • Of 804 randomised patients, four were initially excluded: two lacked consent and two were ineligible and had received no study fluid. Four additional patients were randomised to replace these exclusions, producing 400 patients per group.
  • Two further HES-assigned patients withdrew permission for use of their data, leaving 398 versus 400. Primary follow-up was complete in these 798 patients; the analysis was therefore modified, rather than complete, intention-to-treat.
  • Stopping study fluid was more common than losing outcome data. Twenty-eight patients or surrogates declined further intervention but allowed continued data use; their outcomes remained available.³
• Performance and Detection Bias:
  • Blinding protected clinician decisions about fluid administration, transfusion and RRT from knowledge of assignment. All-cause mortality was an objective outcome, supported by clinical records or registries.
  • Independent monitoring and preparation of the abstract before unblinding strengthened data integrity and interpretation. Formal measurement of the success of blinding was not reported.³⁴
• Baseline Characteristics:
  • Median age was 66 versus 67 years, SAPS II 50 versus 51, and SOFA excluding the neurological component 7 versus 7. Mechanical ventilation was used in 240/398 (60%) versus 245/400 (61%).
  • Shock affected 336/398 (84%) versus 337/400 (84%); baseline acute kidney injury affected 142 (36%) versus 140 (35%). These were seriously ill, broadly comparable groups with a substantial opportunity for patient-important benefit or harm.
  • Pulmonary and abdominal infections predominated, and 29% in each group had undergone emergency surgery. Active haematological malignancy was present in 9% of each group.
• Timing and Previous Resuscitation:
  • Median ICU admission-to-randomisation time was 3.7 hours (IQR 1.3–12.9) versus 4.0 hours (1.4–12.6). Entry was relatively early in ICU care, although initial resuscitation had often already occurred.³
  • Synthetic colloid had been given during the preceding 24 hours to 169 patients (42%) versus 168 (42%). Median prior crystalloid volume was 2500 versus 2400 mL. The comparison therefore evaluated the assigned strategy after a variable amount of previous treatment.³
• Dose and Separation of the Variable of Interest:
  • Study fluid was received by 779/798 patients (98%). Cumulative exposure was a median 44 versus 47 mL/kg ideal body weight; these are cumulative volumes, not daily doses.
  • First-day median study-fluid volume was 1500 mL (1000–1500) versus 1500 mL (1000–2000). The first trial day lasted a median 14 hours, so it should not be interpreted as a uniform 24-hour exposure.
  • First-day fluid balance was 2206 versus 2200 mL, P=0.92. Neither the study-fluid volumes nor measured haemodynamic variables demonstrated the expected clinically useful advantage from assigning starch.
• Protocol Adherence and Crossover:
  • Sixty-nine patients exceeded the 33-mL/kg daily ceiling: 28 assigned HES and 41 assigned Ringer’s acetate. Median excess volume was 500 mL; only two HES-assigned patients exceeded 50 mL/kg, each on one day.³
  • Open-label synthetic colloid was administered to 77 patients, 39 versus 38. Across both groups, 67 received HES and 10 dextran; this weakened separation, although exposure was balanced by allocation.³
  • Protocol-triggered discontinuation for bleeding, allergy or RRT occurred in 104 versus 80 patients. This was an intended response to adverse events and should not be treated as ordinary non-adherence or a reason to remove patients from the primary analysis.
• Adjunctive Therapy and Delivery:
  • Any blood product was given to 243/376 versus 204/380 patients: RR 1.20; 95% CI 1.07 to 1.36; P=0.002. Among recipients, median cumulative volume was 1340 versus 1055 mL; the published volume comparison had P=0.003.
  • Albumin was administered to 80/379 versus 65/381 patients. Reported exposure to selected nephrotoxic drugs and radiographic contrast was broadly similar, although co-interventions were not comprehensively controlled.
  • The pragmatic approach tests the clinical consequences of choosing the fluid within routine ICU care. It does not isolate a particular titration algorithm or prevent all subsequent differences in management.
• Heterogeneity and Outcome Assessment:
  • Variation in infection, organ dysfunction, surgery and hospital type broadened the clinical population. The two prespecified subgroup interaction tests did not show convincing heterogeneity, but small subgroups were not capable of establishing uniform effects.
  • Death, RRT and major transfusion are clinically important. RRT remains a clinician-dependent endpoint, and dialysis dependence at a single late time point is distinct from any acute need for dialysis.
  • Creatinine doubling was unavailable in 38 versus 34 patients; missing usual pre-admission creatinine and early death contributed. Complete primary follow-up should not be mistaken for complete secondary-outcome data.³
• Statistical Rigour:
  • The prespecified primary comparison was retained, recruitment reached target, and there was no early stopping that could inflate the apparent treatment effect.
  • Adjusted analyses and per-protocol estimates remained directionally adverse for HES, but their effect measures and precision differed. The detailed implications of missing severity scores, secondary analysis-plan changes and survival testing are addressed below.³⁴

Conclusion on Internal Validity: Internal validity is strong for the effect of assignment on the primary 90-day outcome, supported by concealed randomisation, extensive blinding and nearly complete follow-up. Confidence is more moderate for secondary renal, recovery and mechanistic conclusions because of missing data, clinician-dependent decisions, multiplicity and changes to secondary estimands.

External Validity

• Population Representativeness:
  • The mixture of university and non-university general ICUs, medical and surgical patients, and common infection sources resembles routine adult sepsis practice. Inclusion of patients with acute kidney injury and shock strengthens relevance to the patients most exposed to resuscitation fluids.
  • Of 1211 patients assessed, 407 were not enrolled. Exclusions included patients already receiving RRT or recently exposed to >1000 mL synthetic colloid, limiting direct evidence for those groups.
  • The cohort was older and severely ill, with 43% control mortality at 90 days. The absolute effect should not be transferred unchanged to younger patients or contemporary populations with lower baseline mortality.
• Applicability:
  • The direct inference concerns repeated ICU resuscitation with 6% HES 130/0.42 versus this balanced crystalloid in adults meeting historical severe sepsis criteria.
  • Children, burns, intracranial bleeding, transplant recipients, elective surgery without sepsis and prehospital resuscitation were not adequately represented or were excluded. The trial did not separately test a single initial starch bolus before other resuscitation.
  • Four high-income health systems provided ready access to monitoring, transfusion and RRT. Consequences of renal injury may differ where dialysis access is limited, but that difference was not tested.
  • 6S does not determine optimal fluid volume, a universal stopping rule, or the comparative effects of albumin and different crystalloid formulations. Related evidence is needed for those questions.

Conclusion on External Validity: External validity is strong for adult ICU patients with severe sepsis requiring further resuscitation in comparable health systems, and limited for populations and treatment windows outside that setting. Its exact absolute harm estimate is less transferable than the finding that this starch strategy offered no net clinical advantage.

Strengths & Limitations

• Strengths:
  • A clinically important question tested in a sizeable, international, investigator-led randomised trial.
  • Concealed allocation, credible masking of fluids, independent monitoring and interpretation before unblinding.
  • A balanced crystalloid comparator, a conservative starch dose ceiling and direct measurement of delivered fluid volumes.
  • A prespecified patient-important primary outcome, complete ascertainment in the analysed cohort, and publication of the protocol, supplement and analysis-plan revisions.
• Limitations:
  • A modified intention-to-treat analysis with six post-randomisation exclusions and some previous or subsequent non-assigned colloid exposure.
  • Clinician-directed resuscitation, RRT and transfusion, with incomplete information on the physiological targets used.
  • A composite almost entirely determined by death, very few late dialysis-dependence events, and limited precision for several individual harms.
  • Missing severity and creatinine data, multiple secondary comparisons and secondary rate definitions amended before unblinding but after recruitment.
  • Direct applicability to one formulation and a particular ICU resuscitation strategy, with the mechanism and minimum harmful exposure unresolved.

Interpretation & Why It Matters

• Patient-important harm

  • Assigning HES increased 90-day mortality and the need for RRT without demonstrating a compensating reduction in resuscitation volume. The clinical argument against this strategy therefore rests on both harm and absence of a demonstrated advantage.
  • The primary result concerns a treatment policy: initial assignment, repeated dosing when clinicians judged fluid necessary, and cessation when predefined complications occurred. It does not estimate the biological effect of every additional litre.
• The renal findings

  • Only one surviving patient in each group was dialysis-dependent at 90 days. This does not neutralise the excess acute RRT requirement or establish renal safety, particularly when more HES-assigned patients died before the late assessment.
  • The renal and bleeding findings make plausible explanations for harm, but the trial did not randomise these intermediate events and cannot definitively apportion the mortality effect between mechanisms.
• What changed

  • 6S undermined the assumption that reducing starch molecular weight and substitution was sufficient to ensure safety in severe sepsis. It made patient outcomes, rather than pharmaceutical design or short-term circulatory response, central to the choice of resuscitation fluid.
  • Its practice-changing importance is the demonstration of net harm under a credible clinical strategy, even though a more favourable strategy in a different population remained a separate question.

Controversies & Other Evidence

• Were Patients Already Resuscitated?:
  • The criticism that 6S missed the relevant treatment window drew on previous fluid exposure and apparently satisfactory median baseline physiology: central venous pressure 10 mm Hg, central venous oxygen saturation 75% and lactate 2.0 mmol/L in the HES group. Those values do not demonstrate that all participants were stable or unresponsive to fluid.⁵
  • Central venous pressure was available in only 110 versus 101 patients and central venous oxygen saturation in 175 versus 152. These selected measurements cannot characterise the entire cohort; 84% met the trial’s shock definition and clinicians judged further resuscitation necessary.³⁵
  • The limitation remains real: 6S did not exclusively enrol untreated patients at first presentation. However, later exploratory analyses found no convincing treatment interaction for randomisation before versus after four hours in ICU, P=0.85; previous colloid exposure, P=0.57; or lactate above versus below 4 mmol/L, P=0.54.⁶
  • These subgroup comparisons retained the original randomised treatment assignment but were selected post hoc and had limited power. They weaken the claim that the observed harm arose solely from late enrolment; they do not prove identical effects in every resuscitation phase.⁶
• Fluid Titration, Dose and Physiological Efficacy:
  • A central physiological criticism was that a more potent volume expander could cause overfilling if cardiac output and fluid responsiveness were not monitored. The trial did not mandate equal volumes, however: similar administered volumes were an observed result of blinded clinician-directed treatment.⁵
  • Absence of a compulsory haemodynamic algorithm limits extrapolation to a specified goal-directed regimen, but does not invalidate the randomised comparison of the strategies actually delivered. It remains unproven that another algorithm would preserve benefit while preventing starch toxicity.⁵⁷
  • The 33-mL/kg daily ceiling was below the then licensed 50-mL/kg limit, and only two HES-assigned patients exceeded that larger limit. Cumulative median exposure of 44 mL/kg should not be misrepresented as a daily overdose.³
  • Measured cumulative fluid balance was 5452 versus 4616 mL, P=0.17, but available in only 288 versus 291 patients. Neither this comparison nor similar central venous pressures establishes that overfilling never occurred; equally, neither demonstrates that overfilling explains the mortality difference.³
  • The published journal critique highlighted discretionary fluid assessment, non-standardised RRT criteria and uncontrolled co-interventions. These primarily constrain mechanistic explanation and replication of a particular bedside regimen; mortality ascertainment and allocation concealment remain strong.⁷
• Observational Evidence on Delivered Fluid Volumes:
  • A later analysis of 654 6S participants still in ICU for three days found differences between hospitals in resuscitation volume and total fluid input after adjustment for baseline characteristics, both P<0.001. This supports substantial variation in how the pragmatic strategy was implemented.⁸
  • Hospital practice and delivered volume were not randomised exposures. Selection of patients who survived and remained in ICU, residual confounding by indication, and the inclusion of pre-randomisation fluids in the main volume analysis prevent these associations from identifying an optimal dose or overturning the original treatment comparison.⁸
• Product Identity and the Balanced Comparator:
  • The published correction changed references to the tested product from HES 130/0.4 to HES 130/0.42 and identified Tetraspan explicitly. It corrected product nomenclature, without changing the outcome data.⁹
  • Potato-derived 130/0.42 and maize-derived 130/0.4 are not chemically identical. The correspondence raised this as a restriction on extrapolation; product differences warrant attention, but require clinical evidence before being treated as protection against harm.⁵
  • Both 6S solutions were balanced, but their electrolyte compositions were not identical. Sodium/chloride concentrations were 140/118 mmol/L in Tetraspan and 145/127 mmol/L in the Ringer’s comparator; potassium, calcium, magnesium, acetate and malate concentrations matched.³
  • Thus, the experiment compared complete fluid formulations rather than adding starch to a perfectly identical carrier. It substantially reduced the saline-versus-balanced-fluid ambiguity, but cannot attribute every effect exclusively to the polymer.³
• Baseline Imbalance, Transfusion and Mediation:
  • An assertion that the HES group contained more patients with shock or acute kidney injury misread the subgroup figure: 179 versus 148 and 72 versus 63 were primary-outcome events within subgroups. The corresponding baseline populations were 336 versus 337 and 142 versus 140.⁵
  • The excess red-cell transfusion occurred after randomisation. It could lie on the causal pathway from HES through coagulopathy or bleeding to death; treating it as an ordinary baseline confounder and adjusting it away could remove part of the treatment effect or introduce selection bias.⁵
  • A post hoc analysis found any bleeding in 93 patients (23%) versus 60 (15%): RR 1.55; 95% CI 1.16 to 2.08; P=0.003. Severe bleeding was associated with death after adjustment, HR 1.74; 95% CI 1.20 to 2.53; P=0.004. The randomised assignment comparison supports a bleeding effect, but the bleeding–mortality association does not prove mediation.¹⁰
  • A subsequent KDIGO-based renal analysis found greater early AKI severity with HES and earlier RRT initiation, HR 1.40; 95% CI 1.01 to 1.93; P=0.04. Adjustment for time-varying AKI attenuated the mortality association, consistent with possible renal mediation; post-treatment adjustment cannot establish that mechanism causally.¹¹
• Composite Outcomes, Competing Death and Statistical Precision:
  • The primary composite was effectively a mortality endpoint because only one additional survivor in each arm was dialysis-dependent. Calling the result an increase in “death or end-stage renal failure” without separating components would overstate evidence about permanent kidney failure.
  • More deaths in the HES group reduced opportunities to survive long enough to be classified as dialysis-dependent. Death also complicates comparisons of RRT duration and renal recovery; a rare late renal endpoint is not reassuring in isolation.
  • The fixed 90-day mortality comparison had P=0.03, whereas the 90-day Kaplan–Meier log-rank comparison had P=0.07 and 28-day mortality P=0.43. These tests address different features of survival, with curves separating mainly after approximately day 20; the log-rank result does not replace the prespecified fixed-time primary test.
  • Nevertheless, the primary confidence interval begins close to no effect, and the RRT finding was one of several unadjusted secondary comparisons. The exact magnitude of harm is less secure than a binary “statistically significant” description implies; coherence with independent trials is important.
• Analysis-plan Changes and Sensitivity Analyses:
  • The 5 March 2012 revisions followed completion of 90-day follow-up but preceded analysis and unblinding. They changed organ-support rate denominators from 90 days to days alive, replaced survivor hospital length of stay with a rate of days alive outside hospital, and formalised additional safety and missing-data analyses.⁴
  • The final 91% versus 93% RRT-free figures are mean proportions of each patient’s surviving days, not 90-day RRT-free days. An early death can coexist with a high support-free proportion. The analogous ventilation and hospital measures should therefore be read alongside mortality, not as standalone measures of recovery.⁴
  • These documented, blinded changes carry less concern than changes selected after seeing treatment identity. They still mean that the secondary estimands were not all fixed before recruitment; the unchanged primary endpoint deserves greater inferential weight.⁴
  • SAPS II remained incomplete in 213 patients after logical imputation. Some substitutions used day-1 or day-2 physiology to fill baseline values, potentially incorporating post-treatment information. This issue affects covariate adjustment rather than the unadjusted primary comparison.³
  • The adjusted primary odds ratio was 1.53; 95% CI 1.13 to 2.07; P=0.005 in the best-case scenario and 1.35; 95% CI 1.00 to 1.81; P=0.05 in the worst-case scenario. These odds ratios should not be compared numerically with the unadjusted RR 1.17 as though they were the same effect measure.³
  • The two per-protocol estimates were RR 1.14; 95% CI 0.97 to 1.34; P=0.12 and RR 1.16; 95% CI 0.97 to 1.37; P=0.07. They were directionally consistent with harm, but neither independently met the conventional significance threshold; exclusions also weakened randomisation, particularly where non-assigned colloid was handled differently by treatment arm.³
• Long-term Survival and Patient-reported Outcomes:
  • Follow-up obtained vital status for all 798 analysed participants at a median 22 months. Six-month mortality was 53.3% versus 47.5%: RR 1.12; 95% CI 0.98 to 1.29; P=0.10. At one year it was 56.0% versus 51.5%: RR 1.09; 95% CI 0.96 to 1.24; P=0.20.¹²
  • At longest follow-up, mortality was 59.8% versus 56.3%: RR 1.06; 95% CI 0.94 to 1.20; P=0.31. Later estimates moved towards no effect, with confidence intervals still including clinically important harm. They did not demonstrate an enduring statistically significant mortality excess, establish equivalence or negate the earlier deaths.¹²
  • Among Danish survivors, 182 of 295 completed quality-of-life questionnaires at a median 14 months. Median SF-36 mental component scores were 45 versus 53, P=0.01. Pruritus occurred in 49% versus 43%: RR 1.13; 95% CI 0.83 to 1.55; P=0.43.¹³
  • The quality-of-life study was post hoc, restricted to survivors and subject to substantial non-response. Differential survival and response can disrupt comparability despite the original randomisation; these findings are exploratory rather than definitive estimates of the effect on long-term quality of life.¹³
• Related Randomised Trials:
  • CRYSTMAS randomised 196 patients with severe sepsis to HES 130/0.4 or saline. Among patients achieving haemodynamic stabilisation, initial study-fluid volume was 1379±886 versus 1709±1164 mL; published mean difference −331 mL, 95% CI −640 to −21; P=0.0185. Four-day study-fluid totals were comparable, and the trial was too small to establish mortality or renal safety.¹⁴
  • CHEST subsequently randomised 7000 general ICU patients to maize-derived HES 130/0.4 in saline or saline. Ninety-day mortality was 18.0% versus 17.0%: RR 1.06; 95% CI 0.96 to 1.18; P=0.26. RRT occurred in 7.0% versus 5.8%: RR 1.21; 95% CI 1.00 to 1.45; P=0.04.¹⁵
  • CHEST independently reinforced renal safety concerns with another tetrastarch, in a less severely ill and more heterogeneous population. Its mortality interval is compatible with the 6S estimate; different P values do not establish contradictory treatment effects.¹⁵
  • CRISTAL compared heterogeneous colloids against heterogeneous crystalloids in 2857 patients with hypovolaemic shock. The primary 28-day mortality outcome did not differ, RR 0.96; 95% CI 0.88 to 1.04; P=0.26, while secondary 90-day mortality favoured colloids, RR 0.92; 95% CI 0.86 to 0.99; P=0.03. Its open-label class comparison and exploratory later outcome cannot establish that the specific 6S starch regimen was beneficial.¹⁶
• Systematic Reviews and Meta-analyses:
  • A sepsis-specific review of HES 130/0.38–0.45 found overall mortality RR 1.04; 95% CI 0.89 to 1.22, but RR 1.11; 95% CI 1.00 to 1.23 in trials at low risk of bias. The trial-sequentially adjusted mortality interval was 0.95 to 1.29, tempering claims of conclusive mortality harm from that synthesis alone.¹⁷
  • The same review found increased RRT, RR 1.36; 95% CI 1.08 to 1.72, with a trial-sequentially adjusted interval of 1.03 to 1.80. Renal harm was more consistently established than the precise pooled mortality effect.¹⁷
  • The broader 2018 Cochrane review found little or no mortality difference between starches and crystalloids, RR 0.97; 95% CI 0.86 to 1.09, while RRT increased, RR 1.30; 95% CI 1.14 to 1.48. Differences in populations, formulations and follow-up explain why a broad pooled mortality estimate need not reproduce the 6S sepsis-specific estimate.¹⁸
  • These syntheses include 6S and CHEST; they organise and increase the precision of the evidence, but should not be counted as additional independent replications of those trials.
• Recent Perioperative Evidence and Its Boundaries:
  • PHOENICS, published in 2026, studied elective abdominal surgery and explicitly excluded sepsis, critical illness and renal impairment. Of 2289 randomised patients, 1958 received trial fluid; HES 130/0.4 was capped at 30 mL/kg and given during surgery and for up to 24 hours afterwards.¹⁹
  • The change to the lowest cystatin C-based eGFR in the first three postoperative days was −3.4±17.7 versus −1.0±17.1 mL/min/1.73 m². HES met the prespecified non-inferiority margin of 8.1 mL/min/1.73 m²; P<0.001 for non-inferiority. The 90-day mortality/major-complication composite was 35% in each group.¹⁹
  • A 2026 perioperative meta-analysis included 114 trials and 13,951 patients, with starch exposure almost always restricted to less than 24 hours. AKI was not significantly increased: RR 1.02; 95% CI 0.91 to 1.16.²⁰
  • These results concern surgical populations, shorter exposure and different estimands. They support reassessing that separate clinical indication, but cannot reverse the randomised finding in severe sepsis. The meta-analysis disclosed manufacturer funding of the commissioned research organisation; its methods and applicability remain more informative than sponsorship alone.²⁰
• Current Guidelines:
  • The 2026 Surviving Sepsis Campaign strongly recommends against starches for resuscitation in sepsis or septic shock, with high-certainty evidence. It recommends crystalloids first line and conditionally favours balanced crystalloids over saline for initial resuscitation.²¹
  • This recommendation reflects the accumulated clinical evidence: plausible haemodynamic efficacy and findings from carefully selected surgical patients do not justify HES use in the septic ICU population tested by 6S.²¹

Summary

• 6S was a completed, blinded, multicentre randomised trial comparing 6% HES 130/0.42 with Ringer’s acetate in adults with severe sepsis requiring ICU resuscitation; 798 patients were analysed.
• Death or dialysis dependence at 90 days occurred in 51% versus 43%: RR 1.17; 95% CI 1.01 to 1.36; P=0.03. The difference was almost entirely mortality.
• Any RRT increased from 16% to 22%, with more red-cell transfusion and no demonstrated reduction in cumulative study-fluid volume.
• Allocation concealment, blinding and primary follow-up were strong. Important qualifications concern prior resuscitation, clinician-directed treatment, secondary analysis-plan changes, missing data and imprecision; they do not establish a beneficial sepsis subgroup.
• Long-term mortality estimates attenuated without establishing equivalence. Independent renal findings and current guidelines support avoiding starches in sepsis; recent perioperative evidence addresses a different population.

Overall Takeaway

6S is a landmark fluid-resuscitation trial because it demonstrated that a contemporary, balanced tetrastarch strategy could increase mortality in severe sepsis despite a conservative daily dose ceiling. Its enduring lesson is that resuscitation fluids require evidence of patient benefit and acceptable harm, beyond a plausible physiological advantage. Together with subsequent evidence, it supports choosing crystalloid over HES for septic ICU patients.

Bibliography

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