Saline-based resuscitation strategies were first proposed as far back as 1831 during the Cholera Epidemic. In an article published in the Lancet in 1831, Dr. O’Shaughnessy suggests the use of injected salts into the venous system as a means of combating the dramatic dehydration seen in patients afflicted with this bacterial infection(1). Saline’s potential harms were first observed in post-surgical patients who after receiving large volumes of saline based resuscitation fluids during surgery were found to have a hyperchloremic acidosis (2). Though these changes appear transient and clinically trivial, it is theorized that when applied to the critically ill, the deleterious effects on renal blood flow may increase the rate of permanent renal impairment and even death. Unfortunately, no large prospective trials have demonstrated this hypothesis to be anything more than physiological reasoning. Small prospective trials have exhibited trivial trends in decreased renal blood flow, kidney function, and increased acidosis, though these perturbations were fleeting and of questionable clinical relevance (3, 4, 5, 6, 7). A larger retrospective study, bringing all the biases such trials are known to carry, demonstrated small improvements in mortality of ICU patients treated with a balanced fluid strategy, though it failed to demonstrate improvements in renal function (the theoretical model used to support balanced fluid administration) (8). In 2012 Yonus et al were the first to attempt to prospectively answer this question in an ICU population. Published in JAMA, on first glance the results seemed to vindicate those in support of the use of balanced fluids (9). Yet despite its superficial success, a closer look reveals this trial does little to demonstrate the deleterious effects of chloride-rich resuscitative strategies. In a recent publication in Intensive Care Medicine, Yonus et al re-examine this question in the hopes of once again demonstrating the benefits of balanced fluid strategies for the resuscitation of the critically ill (10).
In the original publication Yonus et al, using a prospective open-label before and after cohort design, hoped to demonstrate that use of balanced fluids in ICU patients would lead to improved renal function and decreased administration of renal replacement therapy (RRT). For the initial 6-month period fluid administration was left entirely to the whims of the treating intensivist. This was followed by a 6-month span during which ICU staff were trained and educated on the evils of chloride-rich solutions and the benefits of a more balanced approach to fluid selection. Following this smear campaign on normal saline and its high-chloride co-conspirators, authors spent the next 6-months recording fluid administration and subsequent patient outcomes. The authors’ co-primary outcomes were the increase in creatinine levels above baseline during ICU stay and the incidence of acute kidney injury (AKI) as defined by the RIFLE(Risk, Injury, Failure, Loss, End-stage) criteria. Secondary outcomes listed by the authors included the need for RRT, ICU length of stay, and mortality (9).
As far as convincing ICU staff that balanced solutions were beneficial, the authors’ experiment was an overwhelming success. 1,533 patients were examined, 760 patients during the 6-month control period and 773 patients during the subsequent 6-month intervention period. The total amount of normal saline used over the two periods was 2,411L and 52L respectively. Likewise the total chloride administration decreased by a total of 144,504 mmol, or by 198 mmol/patient (9).
On face value the study appears to have been a success, demonstrating statistically significant benefits for both primary outcomes. During the intervention period patients experienced a statistically lower rise in creatinine levels, 14.8 ?mol/L (95% CI, 9.8-19.9 ?mol/L) than during the control period 22.6 ?mol/L (95% CI, 17.5-27.7 ?mol/L). Authors also found a 5.6% absolute decrease in the rate of RIFLE defined kidney injury and kidney failure in patients during the intervention period when compared to those in the control period (9).
These seemingly positive results should be tempered by the fact that while statistically significant, the differences are, for the most part, clinically irrelevant. A 7.8 ?mol/L increase in creatinine translates to an approximately 0.09 mg/dl difference between the control and intervention periods, which is hardly clinically pertinent. The 5.6% difference in rate of AKI was primarily powered by the 3.3% difference in rate of the less severe RIFLE class, kidney injury. When kidney failure was examined alone, unaccompanied by this statistical augmentation, the difference was found to be statistically insignificant (9).
Even the 3.7% absolute decrease in RRT in the intervention period (10.0% vs 6.3%) is hard to conclusively attribute to the balanced fluid strategy, given the open nature of the trial design and the fact that these benefits did not translate into either a decrease in the rate of long term dialysis requirements or mortality. Furthermore the annual rates of RRT during the control and intervention periods are almost identical (7.4% vs 7.9%). In fact, the rates of RRT in the years bookmarking this study are highly variable, which speaks to the potential for unmeasured bias and the cyclic nature of random chance causing the observed differences in these groups, rather than the intervention in question. It is important to remember that though RRT appears to be a finite objective endpoint, it is largely dependent on the treating physician’s subjective judgement. In an open label design such as this, in which the authors are clearly in favor of one intervention over another, the potential for bias affecting this outcome is evident (9).
In a secondary analysis of their data set, Yunos et al hoped to address some of these uncertainties. In this manuscript, published in Intensive Care Medicine in 2014, the authors added an additional 6 months of patient data to both the control and intervention periods, with the intention to demonstrate that the positive findings of their initial publication were due to the favorable influences of balanced fluids. The control period was expanded to include patient data (n=716) from the 6-month period prior to the study’s original start date. The authors then incorporated an additional 6 months of data to the intervention group (n=745) after its original stop date. Overall the two augmented periods ran from February 2007 to February 2008 and August 2008 to August 2009. The authors again found success. And though their primary endpoints remained of questionable clinical significance, the magnitude of their triumph was certainly more impressive (10).
With the addition of this 12-month period of data, the authors boast a 4.8% absolute decrease in the rate of moderate or severe kidney injury as compared to the control. Though the absolute difference in the rate of RRT decreased from 3.6% to 3.0%, when the additional patients were added to the analysis, the difference still remained statistically significant (10). Interestingly, despite both the added control and intervention groups regressing to the mean, the overall magnitude of benefit reported by the authors seemed to increase. This slight of hand was achieved not by some complex form of statistical wizardry, but rather simply lowering the bar for what the authors defined as success.
In their original manuscript, Yunos et al used the RIFLE criteria to define the varying degrees of AKI. Conversely in the more recent publication, AKI was evaluated using the Kidney Disease: Improving Global Outcomes (KDIGO) scale. Despite its grandiose title, in reality this scale is essentially the amalgamation of the previous two scales traditionally used to define AKI (the RIFLE and AKIN criteria). Creators of the KDIGO criteria hoped to identify a greater proportion of patients who would benefit from RRT, and thus created a novel tool by incorporating both definitions of AKI (11). Of course, as is typical with any diagnostic tool, augmenting its sensitivity is achieved by sacrificing its specificity.
Such is the case for the KDIGO score. Not surprisingly, when examined, the KDIGO score identified significantly more patients in renal failure than either the RIFLE or AKIN criteria. In a trial published by Critical Care in 2014, Luo et al compared RIFLE, AKIN and KDIGO’s abilities to identify clinically important AKI (12). They found that the use of the KDIGO criteria identified more overall patients as having AKI (51% compared to 46.9% and 38.4% respectively) as well as classified an larger subset of patients as being in failure (16% compared to 13.8% and 12.8% respectively). Despite the increased yield, no difference was seen in each respective criterion’s abilities to predict death (AOC were 0.738, 0.746, 0.757 respectively). It is still unclear whether the additional patients identified using the KDIGO criteria benefit from early aggressive management of their subtle renal impairment or are harmed from the invasive interventions performed in hopes of treating pathology that would likely resolve without interference. What is clear is that changing from the more conservative RIFLE criteria to the more liberal KDIGO, makes interpreting the clinical relevance of Yunos et al's results difficult.
In the 2014 publication by Yunos et al, the absolute difference in AKI is similar to that described in the 2012 publication (4.8% vs 5.6%), but unlike their original population there is a shift to a more severe spectrum of renal impairment. Using the KDIGO criteria authors found significantly more stage 3 AKI than in their original publication. In the original manuscript the difference in RIFLE failure (class 3) AKI failed to reach clinical significance. In their updated cohort the authors now cite a statistically significant decrease in the rate of KDIGO class 3 AKI (the equivalent of RIFLE failure). The original trial states an absolute difference in the rate of RIFLE class 3 AKI of 2.1%. In their more recent document Yunos et al now cite a 4% (14% vs 10%) absolute decrease in KDIGO stage 3 AKI. Likewise the original manuscript states an absolute difference of 3.3% in the rate of RIFLE class 2 AKI. In the more recent document this same difference is now stated to be only 2%. Clearly the use of the KDIGO criteria has shifted the severity of the cohort in an alarming fashion. This increase in class 3 AKI may be a more accurate interpretation of reality, but given that these differences did not translate into a decrease in either long-term dialysis or mortality, its clinical relevance is unlikely.
Even these clinically questionable differences cannot be directly attributed to the more balanced fluid strategy utilized during the intervention period. It is equally likely the multiple biases introduced by a before and after study design were responsible. Using a multivariant regression model, Yunos et al hoped to account for many of these biases. On initial presentation authors seem to be vindicated in their assertions that these differences in renal function were due to the change in fluid administration. When the addition of the extended control and intervention periods were included in the multivariable analysis, the rate of KDIGO stage 2 and 3 AKI and RRT remained statistically significant. This benefit was powered completely by the initial cohort, the addition of the extended cohorts served only to regress these benefits towards the mean. The odds ratio in the original cohort for preventing AKI was 1.68 (1.28-2.21). When the extended groups were incorporated the odds ratio falls to 1.32 (1.11-1.58). In fact a thorough examination comparing the four time periods uncovers the initial results are hardly as robust as they originally appear. When the extended time period is examined alone (control vs intervention), there was no difference between in the incidence of AKI or RRT. Additionally when the extended control is compared to the original intervention period, the decrease in difference in AKI remains significant but the rate of RRT is no longer statistically significant. There is even a statistically significant increase in the rate of AKI when the original intervention period is compared to the extended intervention period. In fact this is the very same difference in both AKI and RRT that is observed when comparing the original control group to the extended intervention group (10) . Essentially, though it was the authors intent to validate the findings of their initial study, the inconsistent benefits demonstrated in the extended cohort do just the opposite. These differences seem to be due more to random chance than any beneficial effects of a balanced fluid strategy.
The interpretation of medical literature very rarely is as straightforward as we would like to imagine. Much like searching for truth in a magic mirror, so often it serves only to confirm our own beliefs and supports our incredulities. And yet if we are to claim to be authentic curators of truth in medicine, it is important we apply just as much academic rigor when examining topics which we support as we do with those we distrust. A balanced approach to fluid administration has a strong physiological base to support its use. But physiologic reasoning has led us down many blind paths and dark alleys. It is only when we shine the light of critical research we reveal which are dead ends and which lead us and our patients to a better place. Currently we are uncertain as to whether the success of a balanced fluid strategy is due to its chloride-sparring effects or due to the uncontrollable bias introduced by a non-randomized, unblinded trial design, with serious potential for the Hawthorne effect. It may very well be that any fluid in excess is harmfull and “balanced” fluids high in acetate and lactate have their very own unintended consequences when administered in high volumes. The SPLIT trial (scheduled to be published in 2015) may validate our beliefs in the superiority of a balanced fluid strategy, but until then it is important we resist the urge to become quite so dogmatic with our cries of indignation towards chloride-rich solutions.
A brief disclosure: I am, in fact, overwhelmingly and irredeemably in favor of the Stewart approach to acid-base disorders. although there is no convincing evidence directly demonstrating its superiority over the more traditional Henderson-Hasselbalch model, its elegance and intuitive nature make it perfect for the swirling chaos and uncertainty of the Emergency Department. As such it is not hard to imagine that the more judicious administration of fluid, specifically those high in chloride content, would benefit our patients by reducing hyperchloremic acidosis and the concomitant renal failure. I am however, less enthused by the evidence supporting this premise.
-A special thanks to Anand Swaminathan (@EMSwami) for his thoughts and guidance during the writing of this post.
-As always a special thanks to my ever patient wife, Rebecca Talmud(@DinosaurPT), for her editorial wizardry without which this blog would be the unstructured ramblings of a madman.
- O'Shaugnessy, WB (1831). “Proposal for a new method of treating the blue epidemic cholera by the injection of highly-oxygenated salts into the venous system”. Lancet 17 (432): 366–71
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- Yunos NM, Bellomo R, Hegarty C, Story D, Ho L, Bailey M (2012) Association between a chloride-liberal vs chloride-restrictive intravenous fluid administration strategy and kidney injury in critically ill adults. JAMA 308:1566–1572
- Yunos NM, Bellomo R, Glassford N, Sutcliffe H, Lam Q, Bailey M. Chloride-liberal vs. chloride-restrictive intravenous fluid administration and acute kidney injury: an extended analysis. Intensive Care Med. 2014.
- Luo X, Jiang L, Du B, et al. A comparison of different diagnostic criteria of acute kidney injury in critically ill patients. Crit Care. 2014;18:(4)R144.
University of Georgetown
Resuscitation and Critical Care Fellowship Graduate