Publication

• Title: Hydroxyethyl Starch or Saline for Fluid Resuscitation in Intensive Care.
• Acronym: CHEST — Crystalloid versus Hydroxyethyl Starch Trial.
• Year: 2012; published online on 17 October and in the 15 November issue.
• Journal published in: New England Journal of Medicine.
• Citation: Myburgh JA, Finfer S, Bellomo R, Billot L, Cass A, Gattas D, et al.; CHEST Investigators; Australian and New Zealand Intensive Care Society Clinical Trials Group. Hydroxyethyl starch or saline for fluid resuscitation in intensive care. N Engl J Med 2012;367:1901-1911.

Context & Rationale

• Background

  • Hydroxyethyl starch (HES) was used to expand plasma volume, with the expectation that a smaller resuscitation volume than crystalloid would improve haemodynamics and reduce interstitial oedema. These physiological advantages had not established a patient-important benefit.
  • An international observational survey across 391 ICUs in 25 countries demonstrated marked geographical variation in fluid choice. Local practice was a major determinant of treatment, illustrating uncertainty rather than comparative effectiveness.¹
  • VISEP had associated 10% HES 200/0.5 with more acute renal failure and renal replacement therapy in severe sepsis. Whether those findings applied to newer, lower-molecular-weight, less substituted 6% HES 130/0.4 in a broader ICU population remained contested.²
• Research Question/Hypothesis

  • Among adults requiring ICU fluid resuscitation, does 6% HES 130/0.4 in saline, compared with saline alone, alter all-cause mortality at 90 days?
  • The primary hypothesis was no mortality difference. CHEST was designed to detect a difference; its final primary analysis was not a formal demonstration of equivalence or non-inferiority.
• Why This Matters

  • A widely administered synthetic colloid required direct evaluation of survival and renal safety at the licensed concentration and dose limit, rather than reliance on favourable surrogate outcomes or extrapolation from older formulations.
  • The trial extended the large, blinded fluid-comparison approach to a synthetic starch and prospectively included organ dysfunction, renal support and subsequent health-economic evaluation.³

Design & Methods

• Research Question:
  • Whether assigning HES rather than saline for ICU resuscitation changes 90-day mortality, acute kidney injury, renal replacement therapy, new organ failure or resource use.
• Study Type:
  • Investigator-initiated, international, multicentre, parallel-group, double-blind randomised trial in 32 medical and surgical ICUs in Australia and New Zealand.
  • Seven thousand adults were allocated 1:1. Recruitment ran from December 2009 to 23 January 2012, including a preliminary run-in phase.
  • A secure, encrypted web system used minimisation with stratification by institution and trauma at ICU admission.
  • Funding came from the Australian National Health and Medical Research Council, the New South Wales Ministry of Health and an unrestricted Fresenius Kabi grant. Fresenius Kabi supplied and distributed the masked fluids; the funders had no role in design, conduct, analysis or writing, and the investigators retained data access and publication responsibility.
• Population:
  • Adults aged ≥18 years whose clinician considered intravascular fluid resuscitation necessary, over and above maintenance, nutrition, replacement of ongoing losses and blood products, and regarded either study fluid as appropriate.⁴
  • At least one supporting criterion was required: heart rate >90/min; systolic pressure <100 mm Hg, mean arterial pressure <75 mm Hg or a fall of ≥40 mm Hg from baseline; central venous pressure <10 mm Hg; pulmonary artery wedge pressure <12 mm Hg; respiratory variation in systolic or mean pressure >5 mm Hg; capillary refill >1 second; or urine output <0.5 mL/kg/hour for one hour.⁴
  • Renal exclusions comprised current renal replacement therapy or its imminent requirement within six hours, or creatinine >350 µmol/L together with urine output ≤10 mL/hour averaged over 12 hours.⁴
  • Other exclusions included HES allergy, primary non-traumatic intracranial haemorrhage, severe traumatic intracranial haemorrhage with a mass lesion >25 mL, sodium >160 mmol/L, chloride >130 mmol/L, burns, admission after cardiac surgery or liver transplantation, and >1000 mL HES outside the ICU during the preceding 24 hours.⁴
  • Women aged 18–49 years required documented menopause, hysterectomy, sterilisation or a negative pregnancy test; breastfeeding was an exclusion. Patients with imminent inevitable death, life expectancy <90 days, or treatment limitations preventing protocol delivery were excluded.⁴
  • Previous CHEST enrolment and prior resuscitation prescribed in the study ICU during the current admission, or in a transferring ICU, generally precluded entry. Pre-ICU resuscitation was possible, including limited prior HES exposure.⁴
  • The six mortality subgroup pairs specified before unblinding concerned baseline urine-output-defined acute kidney injury, sepsis, trauma, traumatic brain injury, APACHE II score ≥25 versus <25, and previous HES exposure.
• Intervention:
  • 6% HES 130/0.4 in 0.9% sodium chloride, Voluven, supplied in 500-mL bags, for all ICU resuscitation until ICU discharge, death or 90 days after randomisation.
  • Clinicians determined the volume and infusion rate. There was no compulsory fixed bolus regimen, cumulative target or universal haemodynamic endpoint.
  • Masked study fluid was capped at 50 mL/kg/day. If this limit was reached, open-label saline was used for the rest of that 24-hour period.
  • Study fluid was stopped when renal replacement therapy commenced. Saline was then recommended, although another fluid could be used provided it was not HES.
• Comparison:
  • 0.9% sodium chloride in matching 500-mL bags for the same resuscitation indications and treatment period, with the same masked-fluid daily cap.
  • Maintenance fluids, nutrition, blood products, haemodynamic monitoring, vasopressors, ventilation and renal support were determined by the treating team.
  • Fluid administration outside the ICU was not controlled. Criteria for starting renal replacement therapy were not standardised.
• Blinding:
  • Patients, treating clinicians and study personnel were blinded to allocation through indistinguishable bags and masked administration. This was particularly valuable for a treatment delivered repeatedly according to bedside assessment.
  • The independent data and safety monitoring committee reviewed unblinded interim data; routine clinical teams remained blinded.
• Statistics:
  • Power calculation: 7000 patients were required to detect a 3.5-percentage-point absolute difference in 90-day mortality from an anticipated 26% baseline, with 90% power (β=0.10), two-sided α=0.05 and allowance for 5% loss to follow-up.
  • Efficacy analyses followed assigned treatment using available data. Patients who withdrew consent or lacked an outcome were absent from that analysis; missing outcomes were not imputed.
  • The primary unadjusted comparison used a χ² test and relative risk with a 95% confidence interval. Covariate-adjusted analyses included trauma, age, ICU admission source, APACHE II score and baseline creatinine; survival was also examined with Kaplan–Meier methods.
  • The published statistical analysis plan established an outcome hierarchy and six subgroup pairs before unblinding. Interim analyses after 2000 and 4000 patients had 90-day follow-up used an α-spending approach; the final nominal significance level remained 0.05. Multiple secondary outcomes and subgroups were not multiplicity-adjusted.⁵
  • A signed amendment dated 13 June 2012, before unblinding, replaced planned logistic models with models estimating adjusted relative risks directly, permitting robust Poisson regression if log-binomial models failed to converge. It also clarified subgroup interaction analyses.⁶
• Follow-Up Period:
  • The primary outcome was all-cause mortality at 90 days. Use of any modality of renal replacement therapy was recorded through day 90.
  • RIFLE renal categories were assessed from creatinine and urine-output data collected during days 0–7. New respiratory, cardiovascular, coagulation and hepatic failure used SOFA component scores ≥3 in patients without that failure at baseline, assessed during the first 28 days.⁴
  • Duration of ventilation and renal support, ICU and hospital stay, and mortality at other time points were additional outcomes. Longer-term quality of life and economic outcomes were planned separately.³

Key Results

This trial was not stopped early. It completed its planned 7000 allocations, with 3500 patients assigned to each group. Ninety-day mortality was available for 3315 HES patients and 3336 saline patients. The table reproduces published estimates; resource-duration values are means ±SE. The adverse-event rows use the corrected exposure-based populations and are not comparisons of the original randomised groups.⁷

Outcome	HES	Saline	Effect	p value / 95% CI	Notes
Death at 90 days	597/3315 (18.0%)	566/3336 (17.0%)	RR 1.06	95% CI 0.96 to 1.18; P=0.26	Primary outcome. Adjusted RR 1.05; 95% CI 0.95 to 1.16; P=0.33.
Renal replacement therapy by day 90	235/3352 (7.0%)	196/3375 (5.8%)	RR 1.21	95% CI 1.00 to 1.45; P=0.04	Prespecified secondary outcome. Adjusted RR 1.20; 95% CI 1.00 to 1.44; P=0.05.
RIFLE risk	1788/3309 (54.0%)	1912/3335 (57.3%)	RR 0.94	95% CI 0.90 to 0.98; P=0.007	Creatinine/urine-output composite; first seven days.
RIFLE injury	1130/3265 (34.6%)	1253/3300 (38.0%)	RR 0.91	95% CI 0.85 to 0.97; P=0.005	Composite components moved in different directions.
RIFLE failure	336/3243 (10.4%)	301/3263 (9.2%)	RR 1.12	95% CI 0.97 to 1.30; P=0.12	No demonstrated reduction in more severe renal dysfunction.
New cardiovascular failure	663/1815 (36.5%)	722/1808 (39.9%)	RR 0.91	95% CI 0.84 to 0.99; P=0.03	Among patients without this failure at baseline; unadjusted for multiplicity.
New hepatic failure	55/2830 (1.9%)	36/2887 (1.2%)	RR 1.56	95% CI 1.03 to 2.36; P=0.03	Small event count; unadjusted for multiplicity.
New respiratory failure	540/2062 (26.2%)	524/2094 (25.0%)	RR 1.05	95% CI 0.94 to 1.16; P=0.39	Among patients without this failure at baseline.
New coagulation failure	142/2987 (4.8%)	119/3010 (4.0%)	RR 1.20	95% CI 0.95 to 1.53; P=0.13	SOFA-defined failure; not a comprehensive bleeding endpoint.
Death within 28 days	458/3313 (13.8%)	437/3331 (13.1%)	RR 1.05	95% CI 0.93 to 1.19; P=0.40	Additional mortality time point.
ICU stay	7.3±0.2 days	6.9±0.2 days	Mean difference +0.4 days	95% CI 0.0 to 0.9; P=0.07	The displayed lower confidence limit is rounded.
Hospital stay	19.3±0.3 days	19.1±0.3 days	Mean difference +0.2 days	95% CI −0.8 to 1.1; P=0.72	No demonstrated reduction in stay.
Mechanical ventilation duration	6.0±0.2 days	5.7±0.2 days	Mean difference +0.4 days	95% CI −0.1 to 0.8; P=0.12	Among recipients of ventilation; clarified in the correction.
Renal replacement therapy duration	5.6±0.4 days	5.5±0.4 days	Mean difference +0.1 days	95% CI −0.1 to 1.2; P=0.86	Among recipients of renal replacement therapy; values as published.
Any treatment-related adverse event	180/3871 (4.6%)	95/2879 (3.3%)	Not reported	P=0.006; 95% CI Not reported	Corrected analysis: any HES exposure before or after randomisation versus saline-only exposure.
Pruritus	137/3871 (3.5%)	73/2879 (2.5%)	Not reported	P value and 95% CI Not reported	Corrected exposure-based safety analysis.
Skin rash	34/3871 (0.9%)	16/2879 (0.6%)	Not reported	P value and 95% CI Not reported	Corrected exposure-based safety analysis.
Serious non-fatal treatment-related adverse events	2/3871 (0.1%)	2/2879 (0.1%)	Not reported	P=0.77; 95% CI Not reported	HES: anaphylactic shock and extravasation causing airway obstruction; saline: toxic epidermal necrolysis and unexplained severe hypotension.

• HES did not demonstrate a survival benefit: mortality was 18.0% versus 17.0%, with a relative-risk confidence interval compatible with a small benefit or clinically important harm. This does not establish equivalence.
• Renal replacement therapy was more frequent with HES, 7.0% versus 5.8%. Its borderline statistical precision and the apparently favourable RIFLE risk/injury results require interpretation together, rather than selecting one renal endpoint in isolation.
• No prespecified mortality interaction was significant. In sepsis, deaths were 248/976 (25.4%) versus 224/945 (23.7%): RR 1.07; 95% CI 0.92 to 1.25; P=0.38; interaction P=0.78. The traumatic brain injury subgroup contained only 27 versus 30 patients, with 1 versus 3 deaths: RR 0.37; 95% CI 0.04 to 3.35; interaction P=0.31. It cannot establish safety or benefit in brain injury.⁴

Internal Validity

• Randomisation and Allocation:
  • Central allocation, minimisation and concealment protected against foreknowledge of treatment assignment. Stratification by centre and trauma addressed two plausible sources of prognostic imbalance.
• Dropout and Post-randomisation Exclusions:
  • Consent was withdrawn for 137 HES and 113 saline patients. A further 5 versus 3 were lost during early follow-up and 43 versus 48 during later follow-up; the primary endpoint was available for 94.7% versus 95.3% of those randomised.
  • The intention-to-treat principle was applied to observed outcomes, but the primary comparison did not include all 7000 randomised patients. The varying denominators in renal and organ-failure analyses reflect additional outcome-specific availability.
• Performance and Detection Bias:
  • Effective masking substantially reduced the risk that knowledge of allocation changed fluid administration, adjunctive treatment or the threshold for renal support.
  • Mortality was objective. Renal replacement therapy was clinically important but clinician-dependent; blinding protects its comparative assessment without making its initiation criteria uniform.
• Baseline Characteristics and Heterogeneity:
  • Mean age was 63.1±17.0 versus 62.9±16.9 years. Median APACHE II score was 17 (IQR 12–22) versus 17 (12–23); surgical admissions comprised 42.5% versus 42.9%.
  • Mechanical ventilation was present in 64.1% versus 64.9%, vasopressors in 45.5% versus 46.1%, and sepsis in 29.2% versus 28.4%. These were substantially ill patients despite lower mortality than anticipated.
  • Baseline creatinine was 101.5±57.1 versus 100.1±58.0 µmol/L. Urine-output-defined acute kidney injury was present in 36.0% of each group among those with available measurements, which represented only 1449 versus 1421 patients.
  • The heterogeneous case mix supports an average ICU treatment-policy comparison. It does not provide equally precise estimates for every diagnostic subgroup.
• Timing and Dose:
  • Mean time from ICU admission to allocation was 10.9±156.5 versus 11.4±165.4 hours. These are means with very wide dispersion, not median times or evidence that every patient was randomised at approximately 11 hours.
  • Prior HES was recorded in 509/3347 (15.2%) versus 508/3372 (15.1%). Assignment therefore compared subsequent ICU fluid policies rather than first-ever HES exposure against complete avoidance.
  • During the first four days, mean daily study-fluid volume was 526±425 versus 616±488 mL (P<0.001). Exposure was modest relative to the permitted daily ceiling, with most study fluid administered during the first 24 hours.
• Separation of the Variable of Interest:
  • The randomised contrast added HES to the same saline carrier. The smaller study-fluid requirement with HES demonstrated a volume-sparing effect, but its clinical importance depends on patient outcomes rather than infused volume alone.
  • Mean daily positive fluid balance over the first four days was 921±1069 versus 982±1161 mL (P=0.03), while central venous pressure was 11.3±4.8 versus 10.4±4.4 mm Hg (P<0.001).
  • Mean arterial pressure, heart rate and lactate did not show significant between-group differences over this period. Higher filling pressure alone is not evidence of improved tissue perfusion.⁴
• Protocol Adherence and Crossover:
  • Fluid-administration errors affected 311 HES and 323 saline patients, with 473 versus 480 recorded episodes. Ineligible randomisation was recorded in 156 versus 161 patients; these categories should not be added as though they represented distinct patients.⁴
  • Open-label HES during the first four days was recorded in 0/3355 versus 2/3383 patients. The broader administration-error count is therefore not equivalent to the number crossing from saline to HES.⁴
  • Open-label saline was administered to 131/3355 (3.9%) versus 183/3383 (5.4%) during the first four days (P=0.003). Some saline use was permitted rescue treatment rather than a protocol violation.⁴
• Adjunctive Therapy and Delivery:
  • Mean daily non-study fluid over the first four days was 851±675 versus 1115±993 mL (P<0.001). Blood-product volume was 78±250 versus 60±190 mL/day (P<0.001). These are daily averages, not cumulative four-day volumes.
  • Four per cent albumin was used in 69/3355 (2.1%) versus 85/3383 (2.5%), and 20% albumin in 15/3355 (0.4%) versus 22/3383 (0.7%), during the first four days. Rescue albumin was uncommon.⁴
  • Discretionary co-interventions made the comparison clinically pragmatic. Differences emerging after allocation may be consequences of the assigned fluid policy and should not automatically be adjusted away as confounding.
• Outcome Assessment and Statistical Rigour:
  • The primary endpoint, allocation ratio, sample-size target and major renal outcomes were established prospectively. The final adjusted mortality estimate was consistent with the unadjusted estimate.
  • The analysis plan and pre-unblinding amendment documented the regression approach. The published protocol initially described four subgroup pairs, whereas the later analysis plan specified six; prespecification before unblinding should not be confused with inclusion in the initial protocol.³⁵⁶
  • The corrected adverse-event analysis grouped patients by actual HES exposure. Its different causal interpretation, incomplete follow-up and the multiplicity of secondary outcomes are addressed below.⁷

Conclusion on Internal Validity: Strong for the randomised comparison of ICU fluid policies, supported by concealed allocation, blinding and a large completed trial. Confidence is lower for small secondary effects and exposure-based adverse events because of incomplete outcome ascertainment, multiplicity and loss of randomisation in the safety comparison.

External Validity

• Population Representativeness:
  • The broad medical and surgical case mix, bedside eligibility criteria and discretionary co-interventions resemble routine adult ICU resuscitation in well-resourced health systems.
  • Of 19,475 screened patients, 10,612 were ineligible and 1863 otherwise eligible patients were not enrolled, including 735 overlooked and 547 excluded by clinician decision. The enrolled population therefore represents clinical equipoise and operational recruitment, rather than every patient receiving ICU fluids.
  • Advanced renal dysfunction, current or imminent dialysis, major intracranial haemorrhage, cardiac surgery, burns and liver transplantation were excluded. These restrictions limit direct extrapolation and do not establish safety in the excluded groups.
• Applicability:
  • CHEST directly informs a policy of using saline-based HES 130/0.4 for adult ICU resuscitation. It does not directly answer isolated perioperative blood-loss replacement, paediatric resuscitation, pregnancy, prehospital care or treatment in settings without comparable renal support.
  • The comparison holds the saline carrier constant. It does not establish saline as the optimal crystalloid or show that balanced-carrier HES has the same effect.
  • The pragmatic design allows adaptation to different bedside resuscitation practices, but absolute risks and renal replacement therapy use will vary with case mix and local treatment thresholds.

Conclusion on External Validity: Moderate overall, with strong applicability to similar adult medical and surgical ICU populations requiring resuscitation. Applicability is substantially more limited for excluded high-risk groups, isolated perioperative treatment and different fluid formulations or healthcare resources.

Strengths & Limitations

• Strengths:
  • Large, completed, international randomised comparison of a precisely specified starch formulation against its crystalloid carrier.
  • Concealed allocation and sustained double blinding, with clinician-directed delivery reflecting routine ICU practice.
  • A patient-important 90-day primary endpoint, prespecified renal outcomes, public methodological documents and subsequent reproducibility assessment.
  • Detailed reporting of fluid exposure, co-interventions, organ dysfunction and the denominators underlying individual outcomes.
• Limitations:
  • Incomplete primary-outcome follow-up and greater missingness for some renal measures, without imputation in the principal analyses.
  • Previous fluid exposure and variable time to randomisation limited inference about immediate initial resuscitation.
  • A clinician-dependent dialysis endpoint, short biochemical renal surveillance and unadjusted multiple secondary comparisons.
  • Limited precision for small mortality effects and small subgroups, together with exclusion of several clinically important populations.
  • Corrected adverse-event analyses based on exposure and organ-support durations restricted to recipients require different interpretation from the randomised whole-population comparisons.

Interpretation & Why It Matters

• Patient-important benefit

  • HES reduced the amount of study fluid administered but did not improve survival, shorten admission or demonstrate a clinically persuasive organ-support advantage.
  • The mortality estimate should be read through its confidence interval. CHEST excludes a large survival benefit in the enrolled population but remains compatible with clinically relevant mortality harm.
• Renal safety

  • More patients assigned HES received renal replacement therapy. This patient-important adverse outcome carries weight even though the unadjusted P value was close to 0.05.
  • A decision to avoid a discretionary resuscitation fluid can rest on lack of demonstrated benefit plus credible renal harm; it does not require a separately conclusive increase in mortality.
• Contribution to practice

  • CHEST directly challenged the assumption that the newer tetrastarch formulation was sufficiently different from older starches to justify routine ICU use.
  • Its contribution is formulation-specific randomised evidence that must be interpreted alongside other trials. Neither oncotic efficiency nor a favourable component of an organ-failure score substitutes for overall clinical benefit.

Controversies & Other Evidence

• Mortality precision and the anticipated event rate:
  • Control mortality was 17.0%, below the anticipated 26%. The subsequent debate questioned power, but a lower event rate does not automatically invalidate an absolute-risk-difference calculation. The investigators stated that power remained 90% for a 3-percentage-point absolute difference at the observed event rate.⁸
  • The more useful interpretation is the observed RR 1.06 with 95% CI 0.96 to 1.18: a substantial survival advantage is unlikely, while a modest adverse mortality effect remains plausible. Failure to reject the null is neither proof of equality nor proof that HES increased mortality.
  • The six subgroup interaction tests did not identify a population with differential mortality benefit. Their limited precision, especially for trauma and brain injury, prevents interpreting absent interaction as demonstrated biological uniformity.
• How persuasive is the dialysis result?
  • Correspondence challenged the combination of P=0.04 and a lower confidence limit printed as 1.00. The apparent discrepancy arises from rounding; it is not evidence that the primary computation was necessarily wrong. Adjustment produced RR 1.20; 95% CI 1.00 to 1.44; P=0.05.⁸
  • The estimate changes little after adjustment. Treating P=0.04 as definitive harm and P=0.05 as no effect would impose an artificial distinction on essentially the same estimate.
  • Renal replacement therapy was prespecified and clinically consequential, but it was one of several secondary outcomes without multiplicity correction. CHEST alone therefore provides a concerning, imprecise harm estimate whose credibility increases when considered with independent renal evidence.
  • The absence of standardised initiation criteria was a substantive criticism. Blinding limits differential clinician behaviour, while variation between centres adds clinical heterogeneity. A higher creatinine prompting dialysis can be part of the treatment’s renal effect, rather than automatically constituting ascertainment bias.⁹
• The RIFLE paradox: composite definitions and surveillance:
  • Lower RIFLE risk and injury rates with HES coexist with more dialysis and higher creatinine. These findings cannot be reduced to a claim that HES protected renal function.
  • In the post hoc component analysis, doubling of creatinine occurred in 245/3149 (7.8%) versus 191/3171 (6.0%): RR 1.29; 95% CI 1.08 to 1.55; P=0.006. Conversely, the RIFLE-injury urine-output threshold occurred in 1077/2977 (36.2%) versus 1200/3024 (39.7%): RR 0.91; 95% CI 0.85 to 0.97; P=0.005.⁴
  • Categorical oliguria and creatinine thresholds therefore moved in opposite directions. Across the overall early longitudinal measurements, HES was associated with higher creatinine (P=0.004) and lower daily urine output (P=0.003); it is inaccurate to describe HES as simply producing more urine in the whole cohort.
  • Threshold-based classifications, daily averages, differing available-data populations and timing answer different questions. The component analysis is explanatory and post hoc; it does not identify a proven mechanism for the discordance.
  • Creatinine and urine-output surveillance covered seven days, whereas renal replacement therapy was recorded for 90 days. Delayed dysfunction could therefore be captured by the latter without being represented in the early biochemical classification.⁴
  • The appendix classified a patient as positive when an observed day met a criterion; a patient with some observed negative measurements and no observed positive measurement could be classified as negative despite missing days. This can miss episodes occurring during unobserved periods.⁴
• Were patients enrolled too late or without sufficient hypovolaemia?
  • The approximately 11-hour mean interval after ICU admission, previous fluid administration and relatively normal average haemodynamic measurements prompted criticism that CHEST studied patients after substantial initial resuscitation. It did not test a uniform first bolus at the onset of shock.⁹
  • Eligibility relied on clinician judgement plus permissive physiological criteria, rather than a validated demonstration of fluid responsiveness. A qualifying pressure, heart rate or urine output does not itself establish that another bolus will help.
  • Conversely, average measurements cannot establish that all participants had completed resuscitation: approximately 46% required vasopressors and 64% were ventilated. The relevant randomised question was the subsequent ICU resuscitation policy in patients for whom clinicians still judged fluid necessary.
  • A benefit confined to earlier, objectively fluid-responsive patients remains a hypothesis, not a CHEST finding. The trial also did not randomise dose, so its modest average exposure cannot define an optimal or safe HES dose.
• Adherence, missing outcomes and selective analyses:
  • The correspondence proposed a per-protocol analysis because of administration errors. The investigators defended intention-to-treat analysis and the similar error frequency between groups.⁸
  • Balanced error counts do not prove absence of dilution, but excluding patients according to post-randomisation treatment can break comparability. An unadjusted per-protocol comparison would not reliably identify the causal effect of perfect adherence.
  • Consent withdrawal and missing vital status were modest but relevant to an estimated mortality difference this small. Similar follow-up percentages are reassuring about gross imbalance, but cannot establish that missing outcomes were unrelated to allocation or prognosis.
  • The exposure-based adverse-event comparison has a different limitation: previous HES recipients in the saline arm were grouped with HES recipients. Correct denominators make that descriptive comparison coherent, but do not restore the balance created by randomisation.⁷
• The 2016 correction and the meaning of organ-support duration:
  • The correction replaced the adverse-event denominators and percentages with 180/3871 (4.6%) versus 95/2879 (3.3%), P=0.006, and corrected the individual event categories. It did not change the randomised mortality or renal replacement therapy results.⁷
  • It also clarified that mean ventilation and renal replacement therapy durations in the main table concerned patients who received those treatments. The supplementary whole-group averages and recipient-only averages consequently estimate different quantities.⁷⁴
  • Recipient-only renal support duration conditions on an event that treatment can itself affect. Similar duration among recipients cannot counterbalance a greater probability of receiving renal support, nor quantify the overall causal effect on days of organ support.
  • The SOFA-defined cardiovascular and hepatic findings, each with P=0.03, also require caution because of multiple comparisons. Neither should be presented as a separately established protective or toxic organ-specific mechanism.
• Data access and reproducibility:
  • A 2016 BMJ investigation criticised the refusal to release CHEST data through a proposed Yale Open Data Access process supported by Fresenius Kabi. The investigators cited concerns about commercial influence and subsequent analyses; the dispute also exposed weaknesses in the original adverse-event presentation.¹⁰
  • In 2017, Duke Clinical Research Institute investigators reconstructed analyses using supplied case-report data, the database, protocol and analysis plan. They reproduced the primary mortality estimate and confidence interval, obtained almost identical renal replacement therapy findings, and found no secondary discrepancy that changed the conclusions.¹¹
  • The reanalysis was commissioned and funded by the George Institute and its publication included original CHEST investigators. It provides meaningful computational verification by an external analytical group, but is not an independent randomised replication and cannot remove missing-data or endpoint-design limitations.¹¹
  • The methodological judgement should distinguish the legitimate case for transparent data access from the evidential claim that the principal results were overturned. The published reanalysis did not overturn them.
• Other randomised ICU evidence: 6S and CRISTAL:
  • The 6S trial, published after CHEST recruitment ended, compared balanced 6% HES 130/0.42 with Ringer’s acetate in severe sepsis. Ninety-day mortality was 201/398 (51%) versus 172/400 (43%): RR 1.17; 95% CI 1.01 to 1.36; P=0.03. Renal replacement therapy occurred in 87 (22%) versus 65 (16%): RR 1.35; 95% CI 1.01 to 1.80; P=0.04.¹²
  • Differences in formulation, carrier and severity limit direct numerical pooling without attention to clinical heterogeneity. Nevertheless, the adverse renal direction in both trials undermines the argument that CHEST’s finding merely reflected saline as the comparator or carrier. Different mortality P values do not establish contradictory treatment effects.¹²
  • CRISTAL randomised 2857 patients with hypovolaemic shock to classes of colloids or crystalloids. Twenty-eight-day mortality was 25.4% versus 27.0%: RR 0.96; 95% CI 0.88 to 1.04; P=0.26. Lower 90-day mortality with colloids, 30.7% versus 34.2%, was a secondary finding: RR 0.92; 95% CI 0.86 to 0.99; P=0.03.¹³
  • CRISTAL was open-label and combined different colloids and crystalloids. Its exploratory longer-term result does not isolate a benefit of HES 130/0.4 or reverse CHEST’s formulation-specific comparison.¹³
• Systematic reviews: consistent renal concern, differing mortality estimates:
  • The 2013 Zarychanski meta-analysis excluded seven studies associated with an investigator whose other work had been retracted for research misconduct. In that analysis, HES increased mortality (RR 1.09; 95% CI 1.02 to 1.17), renal failure (RR 1.27; 95% CI 1.09 to 1.47) and renal replacement therapy (RR 1.32; 95% CI 1.15 to 1.50).¹⁴
  • The broader 2018 Cochrane review found little or no difference in mortality at the end of follow-up for starches versus crystalloids: RR 0.97; 95% CI 0.86 to 1.09, across 24 studies and 11,177 participants. Renal replacement therapy was increased: RR 1.30; 95% CI 1.14 to 1.48, across nine studies and 8527 participants.¹⁵
  • The syntheses differ in eligible populations, comparisons and studies. It would be inaccurate to claim that every meta-analysis demonstrates excess mortality; the more consistent finding is lack of established survival benefit with increased renal support. Both syntheses include CHEST and therefore do not constitute wholly independent confirmation.¹⁴¹⁵
• Longer-term CHEST follow-up and economics:
  • The prespecified New South Wales follow-up cohort comprised 3537 participants, with 3450 included in the economic analysis. At 24 months, mortality was 586/1687 (35%) versus 594/1708 (35%): RR 1.00; 95% CI 0.91 to 1.10; P=0.89.¹⁶
  • Six-month EQ-5D utility was 0.67±0.34 versus 0.69±0.35 (P=0.33). Mean 24-month costs were AUD 62,196 versus AUD 62,617 (P=0.83); the estimated probability of HES being cost-effective at AUD 100,000 per life-year gained was 29%.¹⁶
  • This geographically restricted, linked follow-up of randomised patients found no later survival, quality-of-life or economic advantage. It does not negate early renal harm or establish equivalence across the entire original trial population.¹⁶
• Perioperative trials address a different population:
  • FLASH tested early, algorithm-guided HES versus saline in 775 high-risk major abdominal surgery patients. Death or major postoperative complications occurred in 139/389 (36%) versus 125/386 (32%): RR 1.10; 95% CI 0.91 to 1.34; P=0.33. Goal-directed perioperative delivery therefore did not establish the benefit missing from CHEST.¹⁷
  • PHOENICS (2026) randomised 2289 elective abdominal surgery patients; 1958 received study fluid and entered the treated analysis. It compared balanced HES, capped at 30 mL/kg, with its balanced crystalloid carrier, excluding critical illness, sepsis and renal impairment.¹⁸
  • PHOENICS met its non-inferiority criterion for the three-day change in cystatin-C-based eGFR: mean±SD −3.4±17.7 versus −1.0±17.1 mL/min/1.73 m², against an 8.1 mL/min/1.73 m² margin (P<0.001 for non-inferiority). Renal replacement therapy occurred in 9 (0.9%) versus 10 (1.0%).¹⁸
  • These findings concern selected surgical patients, short exposure and a specified non-inferiority margin. They do not demonstrate benefit or establish safety in CHEST’s ICU population, which the surgical eligibility criteria deliberately excluded.¹⁸
  • A September 2026 perioperative meta-analysis of 114 trials and 13,951 patients found no detected increase in acute kidney injury: RR 1.02; 95% CI 0.91 to 1.16. Exposure was almost always limited to less than 24 hours.¹⁹
  • That contemporary synthesis informs perioperative use. Its population, treatment duration and inclusion of the newer surgical trials prevent treating it as evidence that ICU HES safety concerns have been resolved.¹⁹
• Current guidance and the remaining fluid-choice question:
  • The 2026 Surviving Sepsis Campaign retains a strong recommendation against starches for resuscitation in sepsis or septic shock, based on high-certainty evidence. It recommends crystalloids first line.²⁰
  • The 2024 ESICM fluid-choice guideline conditionally favours balanced crystalloids over saline in general critical illness and sepsis, while favouring saline in traumatic brain injury. CHEST therefore supports avoiding routine HES without resolving every subsequent choice among crystalloid solutions.²¹
  • The contemporary clinical implication is to choose fluid composition according to the patient and indication, while recognising that CHEST provides no patient-important justification for routine saline-based tetrastarch resuscitation in a similar ICU population.

Summary

• CHEST completed a blinded, concealed, 7000-patient comparison of 6% HES 130/0.4 in saline versus saline for adult ICU resuscitation.
• Ninety-day mortality was 18.0% versus 17.0%: RR 1.06; 95% CI 0.96 to 1.18; P=0.26. A survival benefit was not demonstrated, and equivalence was not established.
• Renal replacement therapy was more frequent with HES, 7.0% versus 5.8%: RR 1.21; 95% CI 1.00 to 1.45; P=0.04. Lower composite RIFLE risk/injury rates do not establish renal protection.
• The 2016 correction clarified exposure-based adverse-event denominators and recipient-only organ-support durations. Subsequent reanalysis reproduced the principal mortality and renal replacement therapy findings.
• Together with other ICU trials and evidence synthesis, CHEST supports avoiding routine HES resuscitation. Recent selected perioperative studies do not establish safety in critically ill patients.

Overall Takeaway

CHEST is a landmark trial because it showed that the modest volume-sparing effect of a widely used modern starch did not translate into better survival or resource use, while renal replacement therapy was more frequent. Its durable contribution is a robust challenge to routine ICU HES use, interpreted through the mortality confidence interval, the limitations of individual renal endpoints and the subsequent body of evidence.

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