"The implementation of a chloride-restrictive strategy in a tertiary ICU was associated with a significant decrease in the incidence of AKI and use of RRT."
Pretty clear, eh? This article is one of several in a line of folks working to divorce us from normal saline. The argument is that this hypernatremic, hyperchloremic solution, when given for large-volume resuscitation in the critically ill, leads to metabolic acidosis and decreased urine output. This study, sponsored by Baxter, the makers of Plasma-Lyte, is an open-label, before-and-after design. One year, they gave whatever fluid they wanted – mostly saline. The next year, saline-containing fluids were restricted, and they used 20% albumin, lactated ringers (Hartmann's solution), or Plasma-Lyte.
Firstly, the primary outcome doesn't match their clinicaltrials.gov registration
. They've changed it from mean base excess during hospital stay to two primary outcomes that weren't even both previously defined as secondary outcomes – increase in creatinine from baseline and incidence of acute kidney injury according to the RIFLE classification.
Then, they offer two positive results from their study – a decrease in the incidence of AKI and the use of renal replacement therapy. The authors use RIFLE as their indicator of AKI – but they don't pre-define which categories of RIFLE they use, and lump "Injury" and "Failure" together to a composite endpoint to gain statistical significance. Otherwise, it's a 7.4% control and 5.4% intervention difference in "Failure" that doesn't reach statistical significance – and considering the mean baseline creatinine was lower in the intervention period, it ought to be expected to reach the failure definition less frequently.
The difference in rise of creatinine reaches statistical significance – but they've hidden the details in their online supplement The mean serum creatinine in the baseline period rises from 10.4 mmol/L to 11.0 mmol/L, and in the intervention period from 10.3 mmol/L to 10.7 mmol/L. This might be statistically significant, but hardly clinically significant. Luckily, the authors use a skewed y-axis to distort and magnify the difference in their graph of these results.
Lastly, the RRT difference reported in their six-month study period is befuddling. The overall rate of RRT in the entire year of their baseline period is 7.9%, while the rate of RRT in the entire year of their intervention period is 7.4%. Yet, in the six months reported for this study, they report RRT use of 10% in the baseline period and 6.3% for the intervention period. This implies the authors retrospectively selected their study period in order to magnify the effect of the RRT difference. This difference in RRT also doesn't match the 2% absolute difference in RIFLE classification for "failure" during the study period. This implies the open-label nature of the study influenced the frequency of RRT use, as the authors may have exerted control over an outcome measure.
As far as patient-oriented outcomes go, after all this splitting of hairs, ICU length of stay was no different, the incidence of long-term dialysis was no different, and mortality was no different. This is also a "bundle-of-care" study, with multiple different chloride-poor and chloride-rich fluids in use, which confounds the generalizability of the results.
Maybe chloride-sparing therapy is important. But these authors are guilty of distorting and misleading with their presentation of results – and the JAMA editors, again, have failed us.
"Association Between a Chloride-Liberal vs Chloride-Restrictive Intravenous Fluid Administration Strategy and Kidney Injury in Critically Ill Adults"www.ncbi.nlm.nih.gov/pubmed/23073953Credit for much of the insight into this article goes to Greg Press, who prepared this article for last month's Journal Club at UT-Houston – but he is in no way responsible for this unhinged rant.