I hope I don't sound like a broken record; I commented briefly on the limitations of studies using historical controls last March, in a study of neonatal abstinence syndrome. However, the stakes are much higher in this study of hemolytic uremic syndrome (HUS). Should we overlook the limitations of historical control studies and change our practice to conform with this study's findings? Read on.
Source: Ardissino G, Tel F, Possenti I, et al. Early volume expansion and outcomes of hemolytic uremic syndrome. Pediatrics.2016;137(1):1-9; doi:10.1542/peds.2015-2153. See AAP Grand Rounds commentary by Dr. Pamela Singer (subscription required).
PICO Question: Among children diagnosed with Shiga toxin-producing Escherichia coli-hemolytic uremic syndrome, is early volume expansion, compared to fluid restriction, associated with improved clinical outcomes?
Question type: Intervention
Study design: Retrospective cohort
These Italian investigators compared outcomes of 38 children with HUS managed from 2006 to 2009 with fluid restriction to those of 38 children managed from 2012 to 2014, after a change in fluid management policy. The authors noted that 56 pediatric units in Italy banded together in 2010 to centralize diagnosis and study HUS.
Fortunately, mortality was low overall in the 2 time intervals, so it wasn't possible to make conclusions about that particular outcome. However, another important outcome, the use of renal replacement therapy (RRT), is both important and easy to measure retrospectively. If we just look at that outcome, the early (initial fluid restriction group) saw 22 of 38 children (58%) needing RRT, compared to 10 of 38 (26%) in the later volume expansion group, with a p value of 0.01. On closer examination, the latter group seemed to have less severe illness overall at the time of diagnosis, possibly related to the HUS network set up in 2010 that could have led to increased awareness of HUS, and earlier diagnosis. So, the authors performed a subgroup analysis, probably post hoc, to examine just the children with more severe disease at diagnosis, defined as initial serum creatinine >2 mg/mL. In that severe illness subgroup, the volume expansion children still required less RRT, only 5 of 12 compared to 14 of 20 in the earlier fluid restriction group. However, this result was not statistically significant, p = 0.11. Perhaps the real contributor to improved outcomes in the later group was due to earlier diagnosis.
Clearly, advances in intensive care and RRT occurred over the time period spanned by these 2 treatment groups, and it is difficult to determine how much that might contribute to better outcomes in the volume expansion group. Still, preventing the need for dialysis or other significant RRT is a big deal, so how much should we quibble about issues of study design?
Not being a nephrologist, I don't think I could answer that question, but I know how I'd go about it if I were charged with making such decisions. First, if I worked at an institution using fluid restriction as the primary initial fluid management of HUS patients, I'd look at how my center's RRT rate compared to the numbers in the Italian study. If it was closer to that 58% number, I'd think seriously about changing fluid management studies. If, on the other hand, it was closer to the 26% number seen with the Italian volume expansion cohort, I'd consider organizing a randomized controlled trial of the 2 methods of fluid management to look more closely at potential benefits of differing fluid management strategies.
In terms of evaluating use of historical controls, I like an FDA official's conclusion on factors strengthening the findings of such studies: 1) short difference in time between collection of the historical data and performing the clinical trial; 2) large, broad historical dataset; and 3) large treatment effect. Although I'm guessing this online presentation intended to guide prospective trial design, applying this reasoning to our 2 HUS groups, I think this Italian study succeeds only in item 3.
