The impact of “early” versus “late” initiation of renal replacement therapy in critical care patients with acute kidney injury: a systematic review and evidence synthesis

Acute kidney injury (AKI) is a medical complication associated with significant morbidity and mortality in critically ill patients [1‐3]. AKI is common in critical illness, and severe AKI is associated with up to 60 % hospital mortality [4]. Renal replacement therapy (RRT) within the intensive care unit (ICU) is conducted as either intermittent hemodialysis or continuous renal replacement therapy (CRRT). Traditional indications for RRT require the development of overt clinical manifestations of renal insufficiency, such as acidosis, electrolyte disturbances (most notably hyperkalemia), uremic complications (encephalopathy or pericarditis), and volume overload unresponsive to aggressive medical management. In spite of research and increasing clinical experience with dialysis, the optimal time to initiate RRT in the course of critical illness complicated by AKI is unclear.

The notion of “early” RRT is to initiate dialysis therapy before nitrogenous and other metabolic products accumulate to the degree where they become relatively resistant to therapy [5, 6]. Despite the intuitive rationale for “early” RRT, there is limited evidence to guide clinicians on the optimal time to initiate RRT in critical illness. Neither standard clinical parameters nor research into novel clinical biomarkers has emerged to clearly define an ideal time or clinical picture where the initiation of RRT optimizes patient outcomes. Earlier initiation of RRT must be balanced with potential patient harm associated with RRTs. Protocolled use of hemofiltration for 96 h in patients with septic shock admitted to an ICU regardless of their renal function suggests that “early” RRT can be associated with negative patient outcomes [7]. As a result, research into “early” RRT includes multiple definitions of early that reflect a potpourri of time factors, biochemical markers, and clinical parameters in an attempt to balance the risks of initiating RRT with the benefits expected from supporting renal function during critical illness.

The authors of two earlier meta-analyses pooled available data on this topic to suggest that “early” RRT improves survival in critical illness. Seabra et al. [8] identified 23 studies (5 randomized controlled trials [RCTs]/quasi-RCTs, 1 prospective study, and 17 retrospective cohort studies) and concluded that “early” initiation of RRT was associated with 28 % mortality risk reduction (relative risk [RR] 0.72, 95 % CI 0.64–0.82, p < 0.001). Karvellas et al. [9] identified 15 studies (2 RCTs, 4 prospective studies, and 9 retrospective cohort studies) and reached similar conclusions, reporting a significant improvement in 28-day mortality with “early” RRT (OR 0.45, 95 % CI 0.28–0.72, p < 0.001). However, the overall findings were not congruent with the subgroup analysis of randomized trials (RR 0.64, 95 % CI 0.4–1.05, p = 0.08), where there was a signal that “early” RRT was not associated with a significant survival advantage. This has diminished clinical confidence in the conclusions reached by the earlier meta-analyses, and consequently “early” RRT in critical illness remains a controversial therapeutic intervention.

Since 2012, additional studies have been published that do not support the conclusions of the previous meta-analyses, and this has further diminished the confidence in the previous conclusions that suggested a survival benefit in critical illness associated with “early” RRT. We conducted a systematic review and evidence synthesis to investigate whether “early” versus “late” initiation of RRT in critically ill patients with AKI improves patient survival and selected secondary outcomes for potential signals to suggest that “early” RRT may reduce patient morbidity or enhance illness recovery. Our goal was to identify the highest-quality studies on this topic and use a pooled meta-analysis of these studies to inform our conclusions.

The systematic literature search yielded 2405 references that were subsequently refined to 36 studies eligible for inclusion in this meta-analysis (see Additional file 3: Figure S2 for article selection breakdown). These references included 7 RCTs [7, 12‐17], 10 prospective cohort studies [18‐27], and 19 retrospective cohort studies [28‐46]. Only nine studies met our criteria for high quality [7, 12, 14‐17, 21, 35, 40]. A summary of the fundamental characteristics of all evaluated studies is provided in Table 1.

Despite several studies having been conducted on this topic over the last 30 years, a clear answer regarding the optimal timing of RRT in critical illness remains elusive. Our analysis does not confirm the conclusions of previous meta-analyses on this topic. Four studies [12, 14, 21, 35] in the high-quality group were previously included in the meta-analysis by Karvellas et al. [9], and only one study [12] was included in the meta-analysis by Seabra et al. [8]. The addition of four recently published studies [15‐17, 40] and one high-quality study that was not previously included in meta-analysis [7] accounts for our results that differ from those of earlier authors. Our conclusions build on the concerns raised by both earlier meta-analyses that the results of cohort trials in favor of “early” RRT were not reproduced in methodologically more rigorous study designs (i.e., RCTs). In our further analysis we did not identify critical illness patient subgroups for whom “early” RRT might be more beneficial. Similarly, how one defines early (according to time or on the basis of biochemical characteristics) does not identify a survival advantage associated with “early” RRT compared with usual care. The optimal timing for initiation of RRT is not clarified on the basis of research evaluated to date.

By limiting our analysis to studies meeting high-quality criteria, we dismissed a large volume of research on this topic. A critique of our work is that we discarded studies for methodological shortcomings that others may feel should have been included. Most studies (n = 21) in the low-quality group were excluded for incomplete cohort data or significant preintervention differences between cohort groups. The decision to exclude these trials is less controversial than our decision to exclude cohort trials for an NOQA Scale rating less than 7 (n = 6). This is potentially controversial because the NOQA Scale has received criticism regarding its validity and applicability in meta-analysis cohort trial quality assessment [50]. The NOQA Scale has received positive endorsement from some authors [11], but detailed psychometric properties have not been published in peer-reviewed journals to date. Furthermore, our selection of an NOQA Scale rating less than 7 to identify low quality is arbitrary. Our rationale for selecting this cutoff was that it necessitates that at least one of the three NOQA Scale domains be seriously compromised, and we felt that this represented a significant bias predisposing the study results to committing a type I error pattern. Seabra et al. [8] attempted to assign a quality score to trials (0 = lowest quality to 5 = best quality) to evaluate this domain, but their methodology for score assignment was obscure and was not able to be replicated or directly compared with our methods. In qualitative comparison, the study assigned their top score [12] was included in our quantitative analysis; however, their second highest quality study [13] was excluded due to lack of reported illness severity scores between groups. Including studies with methodological errors does not advance scientific understanding of this topic and has contributed to the discordant findings on it.

Early studies on this topic were small and may have overestimated an effect size associated with “early” RRT based on the small size of the study populations. An example of this problem is the Sugahara et al. study [14], where 14-day mortality within the “early” group was 14 % (2 of 14), compared with 86 % (12 of 14) in the “late” group (p < 0.01). While this study was included in our quantitative analysis, the magnitude of the mortality benefit reported in this trial associated with “early” RRT has not been reproduced by subsequent investigators, for reasons that are not clear. In our review of the ongoing trials on this topic registered with the NIH (www.​clinicalTrials.​gov), we identified three trials [51‐53] that may add to knowledge in this area. The methodology of all three active RCTs is roughly similar, with patients randomized from a point in time triggered by the development of biochemical renal injury reflected by a RIFLE grade of “failure” (at least one of rise in creatinine by minimum of 300 %, oliguria less than 0.3 ml/kg/h for 12 h, or anuria lasting more than 12 h). From this biochemical entry point, patients will be randomized to immediate initiation of RRT (goal time to RRT less than 12 h) or standard care (RRT initiated after failure of medical management to temporize metabolic derangements or volume overload). These study designs are similar to the design used by Wald et al. [17], included in our analysis, that was able to separate an “early” group to mean time to RRT of 9.2 h and a “late” RRT group with a mean time to RRT of 32 h after biochemical inclusion criteria were met. Wald et al. [17] did not identify a significant difference in mortality rates between their two groups (p = 0.74). These studies in process will add to the quantity of patients evaluated in this manner and will build on the availability of high-quality data on this topic. By clearly defining routine biochemical criteria associated with acute renal injury, they provide a practical method of renal injury assessment that can be determined by intensivists and nephrologists considering RRT.

The results of our meta-analysis contradict the findings reported by previous authors [8, 9], and we conclude that “early” initiation of RRT in critically ill patients with AKI does not improve survival. This conclusion is derived from the pooled high-quality trial data and excludes data from cohort trials where there were methodological shortcomings that predisposed them to find an effect misattributed to the intervention. Pooled analysis of secondary outcomes did not demonstrate a statistical reduction in ICU or hospital LOS. Additional well-designed RCTs will provide greater confidence in these conclusions as optimal patient care practices progress in critical care. Clinical triggers for the initiation of RRT to optimize patient outcomes have not been clearly identified by current research. Meanwhile, intensivists and nephrologists are encouraged to refrain from lowering their clinical thresholds for implementing RRT in critical care patients with acute renal injury.