Despite advances in the medical field, growing numbers of patients are becoming critically ill. Each year, 750,000 people in the United States of America are admitted to intensive care units (Angus 2001). Sepsis resulting from a generalized inflammatory and procoagulant response to an infection is associated with a death rate of 30% to 50% (Bernard 2001). This rate increases in the presence of circulatory shock despite aggressive antimicrobial therapy, adequate fluid resuscitation, and optimum care (Periti 2000); and may reach as high as 70% in patients with multiple organ dysfunction (Polderman 2004). Circulatory shock is defined as the failure of the circulatory system to maintain adequate perfusion. It may arise from: cardiogenic shock (heart failure); septic shock (severe infection); bleeding (haemorrhagic shock); brain and spinal cord injury (neurogenic shock); and allergic reactions (anaphylactic shock) (Müllner 2004). Severe sepsis is the second most frequent cause of death in intensive care patients, surpassed only by cardiovascular events (Polderman 2004).
Critical illness results in uncontrolled inflammation and vascular damage even when the cause of the illness is not infection; other causes are, for example: trauma; malignancy; complications of pregnancy; poisoning; allergic reactions; or liver failure (Periti 2000). With the above-mentioned disorders, a systemic activation of coagulation may occur which, at its worst, results in a fulminant disseminated intravascular coagulation (DIC). DIC is characterized by simultaneous widespread microvascular thrombosis and profuse bleeding from various sites (Levi 2004).
The inflammation associated with critical illness is characterized by an increase in the number and activity of numerous molecules, such as platelet activating factor, von Willebrand factor, and tumour necrosis factor. There is a simultaneous increase in the activity of pro-inflammatory and pro-coagulant processes, such as: thrombin formation; fibrin deposition at the vascular wall; and the formation of aggregates containing platelets and leukocytes. Leukocyte rolling, adhesion, and transmigration are also important parts of the inflammatory reaction. These processes lead to capillary leakage, severe disturbance of the microcirculation, tissue damage, and eventually multiorgan failure and death (Becker 2000).
Any proposed treatment of critical illness should aim to eliminate the underlying disorder or condition and to restore microvascular function, hence reducing organ dysfunction (Levi 2004).
Antithrombin III (AT III) is primarily a potent anticoagulant with independent anti-inflammatory properties. AT III irreversibly inhibits serine proteases (for example activated factor X and thrombin) in a one-to-one ratio, with the generation of protease-AT III complexes. Heparin prevents AT III from interacting with the endothelial cell surface by: binding to sites on the AT III molecule; competing for the AT III binding site; and reducing AT III ability to interact with its cellular receptor. AT III's anticoagulant effect is thus greatly accelerated (by a factor of 1000) by heparin; heparin reduces AT III's anti-inflammatory properties, weakens vascular protection, and increases bleeding events (Opal 2002; Rublee 2003). The theoretical beneficial effect of heparin among patients with DIC, a standard therapy in many intensive care units, has yet to be validated in a multicentre trial setting. There is also insufficient data to conclude that heparin is safe in DIC (Levi 2004; Wiedermann 2004).
The blood concentration of AT III falls by 20% to 40% in septic patients and these levels correlate with disease severity and clinical outcome (Opal 2002; Wiedermann 2002). This reduction in concentration is due to the combined effect of: decreased production of AT III in the liver; inactivation by the enzyme elastase, which is increased during inflammation; and loss of AT III from the circulation into tissues through inflamed and leaking capillary blood vessels. These processes reduce the half-life of AT III from a mean of 55 hours to 20 hours (Fourrier 2000). The main mechanism of AT III depletion in severe sepsis is linked to consumption of the molecule.
It is this depletion of AT III that has prompted research into the potential benefits of replenishing AT III levels. Investigators have often tried to increase the antithrombin concentration to supranormal values because the activity of proinflammatory and procoagulant molecules are increased in critically ill patients. Thus artificially high levels of AT III may be required to overcome the inhibitory effect of thrombin and other such serine proteases. This is because the normal serum concentration of AT III does not necessarily reflect the amount bound to endothelial receptors and appears insufficient (Fourrier 2000).
Finally, by blocking the actions of thrombin AT III may have antiangiogenic and antitumour properties (Larsson 2001).
Although critically ill patients are a heterogeneous population they are characterized by having systemic inflammation, no matter what the cause of their illness is. This inflammation causes further damage to tissues and organs and can result in multiple organ failure and death. The process of inflammation can be modified by AT III, whether or not clotting is abnormal, and it is possible that AT III can reduce the high death rate or permanent damage experienced by critically ill patients. The benefit of AT III supplementation in critically ill patients is still controversial and its efficacy is debated. The aim of this review is to assess the evidence that AT III therapy is beneficial for critically ill patients.
We assessed the benefits and harms of AT III administration in critically ill patients.
Criteria for considering studies for this review
Types of studies
We included published and ongoing randomized controlled trials irrespective of blinding status or language. We excluded studies published as abstracts and studies that did not provide mortality data.
Types of participants
We included critically ill patients as variously defined by trial authors. However, we excluded trials of adjuvant AT III administration for the reduction of cardiovascular events in the invasive treatment of acute myocardial infarction.
The terminology for sepsis as originally proposed by the American College of Chest Physicians and the Society of Critical Care Medicine is in many ways outdated (Opal 2003). A loose definition of sepsis can easily result in enrolment of a heterogeneous population and hence in exaggerated findings, in either direction, that are difficult to reproduce. However, we accepted the various definitions of sepsis, septic shock, DIC, and other critical illnesses as proposed by the authors; we did not exclude any study based on their definitions. We chose to accept the term 'standard treatment of sepsis and DIC' as reported by many authors despite the lack of a generally accepted treatment regimen.
Types of interventions
We included AT III versus no intervention or placebo. We included any dose of AT III, any duration of administration, and co-interventions but excluded trials that compared different doses of AT III.
Types of outcome measures
The primary outcome measure was overall mortality. We used the longest follow-up data from each trial regardless of the period of follow up.
- Number of days in hospital
- Mean length of stay in an intensive care unit (ICU)
- Quality of life assessment, as defined by authors in included studies
- Severity of sepsis (according to different organ dysfunction scores; sepsis versus septic shock if adequately defined by authors)
- Incidence of respiratory failure (mechanically assisted ventilation)
- Duration of mechanical ventilation
- Bleeding events
- Incidence of surgical intervention
- Complications specific to the trial intervention, e.g. bleeding, limb venous thrombosis, line sepsis, local haematoma
- Complications during the in-patient stay not specific to the trial intervention, e.g. pneumonia, congestive cardiac failure, respiratory failure, myocardial infarction, renal failure, cerebrovascular accident
We defined bleeding events (7.) as intracranial bleeding or bleeding requiring transfusion of at least three units of blood. We counted repeated transfusions in the same participant as a singular event.
Search methods for identification of studies
We searched the Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library 2006, Issue 4); MEDLINE (1950 to November 2006); EMBASE (OVID platform) (1980 to November 2006); International Web of Science (1945 to November 2006); Latin American Caribbean Health Sciences Literature (LILACS) (up to November 2006); the Chinese Biomedical Literature Database (up to November 2006); and Cumulative Index to Nursing & Allied Health Literature (CINAHL) (up to November 2006). We performed a systematic and sensitive search strategy to identify relevant randomized clinical trials with no language or date restrictions.
For specific information regarding our search strategies and results please see Appendix 1.
We searched for ongoing clinical trials and unpublished studies on the following Internet sites (up to March 2005):
- Current Controlled Trials;
- Centre Watch Clinical Trials Listing Service.
Searching other resources
We handsearched the reference list of reviews, randomized and non-randomized studies, and editorials for additional studies. We contacted the main authors of studies and experts in this field to ask for any missed, unreported, or ongoing studies.
Data collection and analysis
We used the above strategy to search for relevant trials. We then screened the titles and abstracts in order to identify studies for eligibility. We independently extracted and collected the data on a standardized paper form. We were not blinded to the author, source institution, or the publication source of trials. We resolved disagreements by discussion and approached all first authors of the included trials for additional information on risks of bias. For more detailed information please see the section 'Contributions'.
Evaluation of risk of bias in trials
We evaluated the validity and design characteristics of each trial. Trials were evaluated for major potential sources of bias (random sequence generation, allocation concealment, blinding, intention-to-treat analysis, and completeness of follow up) (Higgins 2005). We assessed each study quality factor separately and defined the trials as having low risk of bias only if they adequately fulfilled all of the criteria.
Random sequence generation
Adequate: the method used generated random sequences, e.g. random number generation, toss of coin.
Unclear: no information on random sequence generation available.
Inadequate: alternate medical record numbers or other non-random sequence generation.
Adequate: allocation method prevented investigators or participants from knowing the next allocation, e.g. central allocation; sealed opaque envelopes; serially-numbered, sequentially-numbered but otherwise identical vehicles, including their contents; or other descriptions of convincing concealment of allocation.
Unclear: no information on allocation method available or the description did not allow a clear distinction.
Inadequate: allocation method allowed the investigators or participants to know the next allocation, e.g. alternate medical record numbers; reference to case record numbers or date of birth; an open allocation sequence, unsealed envelopes.
Adequate: double blinded and the method of blinding involved identical placebo. Studies were categorised as double blinded if the participant and at least one other of the personnel (relative, investigator, one of the many intensive care doctors, one of the many intensive care nurses, one of the many other people looking after the participant who could affect their outcome) were unaware of whether AT III or placebo was being given.
Unclear: blinding not described.
Inadequate: not double blinded; categorized as an open-label study; or without use of placebo.
Intention-to-treat (ITT) analysis
Adequate: we could extract data according to ITT principles.
Unclear: we could not extract data according to ITT principles.
Inadequate: use of per protocol analyses, i.e. participants who were randomized were not included in the analysis because they did not receive trial intervention; withdrew from the trial; or were not included because of protocol violation.
We defined a trial as at low risk of bias if all the above components were adequately conducted. The remaining trials were defined as at high risk of bias.
We used Review Manager software (RevMan 5.0). We calculated the relative risks (RR) with 95% confidence intervals (CI) for dichotomous variables and mean difference (MD) with CI for continuous outcomes. We used the chi-squared test to provide an indication of heterogeneity between studies, with P < 0.1 considered significant. The degree of heterogeneity observed in the results was quantified using the I-squared (I²) statistic, which can be interpreted as the proportion of the total variation observed between the studies that is attributable to differences between studies rather than sampling error (chance) (Higgins 2002). I² > 75% is considered as very heterogeneous. We used both a random-effects model and a fixed-effect model. If I² = 0 we only reported the results from the fixed-effect model; and in the case of I² > 0 we reported only the results from the random-effects model.
We planned the following subgroup analyses:
- the effect of AT III in participants given heparin (all types and doses) versus participants not given heparin;
- comparing estimates of the pooled intervention effect in trials with low risk of bias to estimates from trials with high risk of bias (i.e. trials having at least one inadequate risk of bias component);
- duration of drug administration (up to one week, more than one week);
- completeness of follow up (the actual number of randomized participants with outcome data at the defined end of follow up for the trial, where we compared the groups of trials based on the degree of follow-up completeness);
- comparing the pooled intervention effect in trials with a follow up that was longer than the median follow up with trials having a follow up equal to or shorter than the median follow up of trial participants. This was in order to detect a possible dependency of the estimate of intervention effect with length of follow up. There was no biological rationale for choosing the median follow up as a fixed time point but rather this was a pragmatic approach in order to perform a subgroup analysis;
- the effect of AT III in the trauma population;
- the effect of AT III in obstetrics (eclampsia, pre-eclampsia, or DIC);
- the effect of AT III in paediatrics (we defined an age below 18 years for our inclusion criteria);
- the effect of AT III in sepsis.
If analyses of various subgroups were significant, we performed a test of interaction (Altman 2003). We considered P values < 0.05 as indicating significant interaction between the AT III effect and subgroup category.
|Figure 1. Funnel plot, overall mortality regardless of follow up (quality)|
Description of studies
Through electronic searches and from reading the references of potentially relevant articles, we identified 8775 publications on AT III. We excluded 8716 publications as they were either duplicates or were clearly irrelevant. A total of 61 relevant publications were retrieved for further assessment. From these, we included 20 trials that were described in 21 publications (see Additional Figure 2) and which randomized a total of 3458 participants. The sample size varied from 25 to 2314 participants. We excluded 40 publications for the reasons detailed in the Characteristics of excluded studies. We found one ongoing trial (D'angelo 2005) but no data were provided for this trial.
|Figure 2. How searching results found|
Types of participants
We classified two trials as obstetric studies (Kobayashi 2003; Maki 2000); three trials as paediatric trials (Fulia 2003; Mitchell 2003; Schmidt 1998); and a further two trials as trauma studies (Grenander 2001; Waydhas 1998). The remaining trials consisted of mixed populations of critically ill participants, mainly with sepsis.
Types of interventions
The duration of intervention varied from less than 24 hours to four weeks. Three trials had a median duration of AT III intervention that was longer than one week (Inthorn 1997; Mitchell 2003; Smith-Erichsen 1996). Follow up ranged from seven days to 90 days.
The comparison group received placebo in 10 trials (Baudo 1998; Diaz-Cremades 1994; Eisele 1998; Fourrier 1993; Fulia 2003; Haire 1998; Maki 2000; Schmidt 1998; Warren 2001; Waydhas 1998). The agent used as placebo was albumin, in different concentrations. One trial did not provide information on the placebo agent used (Eisele 1998).
Risk of bias in included studies
Generation of the allocation sequence
Allocation concealment was adequately reported in 12 trials (60%) (Albert 1992; Baudo 1998; Fourrier 1993; Fulia 2003; Grenander 2001; Haire 1998; Kobayashi 2003; Maki 2000; Mitchell 2003; Schmidt 1998; Warren 2001; Waydhas 1998) (see Analysis 1.3).
Ten trials provided sufficient data to be categorized as double blinded (50%) (Baudo 1998; Eisele 1998; Fourrier 1993; Fulia 2003; Haire 1998; Kobayashi 2003; Maki 2000; Schmidt 1998; Warren 2001; Waydhas 1998). The remaining trials were either open label or did not provide sufficient data on how the double blinding was achieved (see Analysis 1.4).
Two trials did not provide data on follow up (Baudo 1992; Diaz-Cremades 1994). Twelve trials (60%) had complete follow up (Eisele 1998; Fourrier 1993; Fulia 2003; Grenander 2001; Haire 1998; Inthorn 1997; Kobayashi 2003; Langely 1993; Schmidt 1998; Schorr 2000; Smith-Erichsen 1996; Waydhas 1998) (see Analysis 1.5).
Intention-to-treat analysis (ITT)
Thirteen trials (65%) performed analysis according to the ITT method or provided sufficient data to perform ITT analyses (Baudo 1992; Eisele 1998; Fourrier 1993; Fulia 2003; Haire 1998; Harper 1991; Inthorn 1997; Langely 1993; Maki 2000; Schmidt 1998; Schorr 2000; Smith-Erichsen 1996; Waydhas 1998) (see Analysis 1.6).
Sample size calculation
Effects of interventions
Combining all trials showed no statistically significant effect of AT III on mortality: 667/1708 deaths (39.1%) in the experimental group compared with 699/1750 deaths (39.9%) in the control group (RR (fixed) 0.96, 95% CI 0.89 to 1.03). Heterogeneity was absent (see Analysis 1.1). Combining the data provided in Table 1 (which excluded articles published as abstracts) with the overall mortality analysis based on risk of bias did not alter the overall picture: 645/1895 deaths (34.0%) in the AT III group compared with 728/1898 deaths (38.4%) in the control group (RR (fixed) 0.96, 95% CI 0.89 to 1.04).
Subgroup and sensitivity analyses
We did not find any statistically significant differences in subgroups: with adequate and inadequate components of risk of bias; and with and without adjuvant heparin (see Additional Table 2; Table 3).
Due to the ongoing debate about the interaction between AT III and heparin, we decided to make three separate subgroup analyses to examine the trial intervention based on interaction with heparin. The only difference between these subgroup analyses was the way in which the data from Warren 2001 were incorporated. Only in one subgroup analysis, splitting data from Warren 2001, did the subgroup without heparin show a statistically significant effect of AT III (RR (fixed) 0.87, 95% CI 0.75 to 0.99). As there was some heterogeneity (I² = 1.1%, P = 0.41), we applied the random-effects model as defined in our protocol and the effect was no longer significant (RR (random) 0.89, 95% CI 0.77 to 1.02) (see Analysis 1.14). Similarly, there was no statistically significant interaction with and without adjuvant heparin if all patients from Warren 2001 were analysed as participating in either a trial with (P > 0.3) or without (P > 0.3) concomitant use of heparin (see Analysis 1.12; Analysis 1.13; Analysis 1.14; Additional Table 3).
We did not find any statistically significant difference when examining the effects in subgroups according to: duration of intervention (equal or less than one week versus longer than one week); follow up less than or longer than the median of all trials; intervention among different populations (paediatrics, trauma, sepsis); or the effect of degree of follow-up completeness (see Analysis 1.5; Analysis 1.8; Analysis 1.9; Analysis 1.10; Analysis 1.11; and Additional Table 3; Table 4).
The funnel plot on overall mortality regardless of follow up (Figure 1) showed a symmetrical distribution that indicated no publication bias.
Adverse events, complications, and surgical intervention
Six trials with low risk of bias (Baudo 1998; Fulia 2003; Kobayashi 2003; Maki 2000; Schmidt 1998; Warren 2001) and three with high risk of bias (Langely 1993; Grenander 2001; Mitchell 2003) demonstrated a statistically significant increase in bleeding events in the intervention group compared to the control group (RR (random) 1.52, 95% CI 1.30 to 1.78). Heterogeneity was insignificant (I² = 0.3%, P = 0.43). No other outcome examining adverse events was statistically significant (see Analysis 1.15 to Analysis 1.20; Analysis 1.23; Additional Table 5; Table 6).
Quality of life
Only one trial examined the intervention's effect on quality of life (Rublee 2003: based on data from Warren 2001). There was an objective assessment of physical performance and dependency, and a subjective overall quality of life assessment analysis. Neither assessment supported intervention with AT III (MD -2.00, 95% CI -4.49 to 0.49; MD -2.00, 95% CI -5.01 to 1.01 respectively) (Additional Table 6).
Severity of sepsis
Only one analysis, multiorgan failure score (MOFS) (MD (random) -1.24, 95% CI -2.18 to -0.29), of the four different analyses reached statistical significance when examining the effect of AT III on various illness scores. Six trials provided data (Baudo 1998; Diaz-Cremades 1994; Eisele 1998; Haire 1998; Inthorn 1997; Schorr 2000) (see Analysis 1.24 to Analysis 1.27; Additional Table 6).
Six trials examined the effect of AT III on the incidence of respiratory failure (not present at admission) (Eisele 1998; Fourrier 1993; Kobayashi 2003; Maki 2000; Warren 2001; Waydhas 1998). There was no statistically significant difference with AT III (RR (random) 0.93, 95% CI 0.76 to 1.14). Heterogeneity was present (I² = 31.6%, P = 0.22). Three trials examined the effect of the trial intervention on duration of mechanical ventilation (Grenander 2001; Schmidt 1998; Waydhas 1998). There was no statistically significant difference (MD 2.20, 95% CI -1.21 to 5.60). Heterogeneity was absent (see Analysis 1.28; Analysis 1.29; Additional Table 5; Table 6).
Length of stay in the ICU and in hospital
Three trials examined the intervention effect on the length of stay in hospital (Haire 1998; Smith-Erichsen 1996; Waydhas 1998) with a MD (random) of -1.86 (95% -11.38 to 7.67). Heterogeneity was significant (I² = 64.3%, P = 0.06).
One trial with low risk of bias (Baudo 1998) and five trials with high risk of bias (Albert 1992; Diaz-Cremades 1994; Fourrier 1993; Smith-Erichsen 1996; Waydhas 1998) examined the intervention effect on length of stay in the ICU. There was insufficient evidence to support any beneficial effect of the intervention (MD 0.01, 95% CI -1.75 to 1.76). Heterogeneity was absent (see Analysis 1.30; Analysis 1.31; Additional Table 6).
In this systematic review of 20 trials with 3458 patients we found no significant beneficial effect of AT III on mortality. The analyses on mortality showed no heterogeneity and were robust when performing different subgroup analyses. Conversely, AT III increased the risk of bleeding and it appeared to improve only one of the reported severity of sepsis scores (MOFS). None of the other secondary outcomes reached statistical significance.
Neither the meta-analysis nor the subgroup analyses demonstrated a statistically significant effect of AT III on mortality. However, this is not evidence of the absence of a beneficial effect; but the data suggest that a potentially beneficial effect of AT III must be modest compared to what had been expected. The point estimate of the potential intervention effect as suggested by the low bias trials is a 5% relative risk reduction (RRR) (see Analysis 1.1). In order to demonstrate or reject a beneficial effect on mortality in a single trial, assuming a RRR of 5% (an absolute risk reduction of 2.3%, from 48.5% to 46.2%) at least 14,294 patients should be randomized (Additional Figure 3) (with 80% power and alpha 0.05, assuming a double-sided type I risk of 5% and a type II risk of 20%). However, solid evidence may be obtained with a lesser number of patients if eventually the cumulative meta-analysis z-curve crosses the trial sequential monitoring boundary constructed for a required information size of 14,294 randomized patients. On the other hand to demonstrate or reject an a priori anticipated intervention effect of a RRR of 10%, 3317 patients should be randomized. As 3458 patients have already been included in the meta-analysis, without becoming statistically significant, a RRR of 10% or more on mortality is unlikely (Additional Figure 4).
Subgroup analysis of duration of intervention and length of follow up
Based on follow up less than or longer than the median of all trials, we undertook a subgroup analysis to examine the intervention effect on mortality. However, there was no statistically significant association between follow up and mortality (see Analysis 1.7). The median follow-up time was 32 days.
We also examined intervention effect based on the median duration of intervention being less than or longer than one week. Only two trials with a total of 125 participants had a median duration of intervention longer than one week. The current evidence does not support a longer duration of intervention.
Subgroup analyses on paediatric, obstetric and trauma populations
Based on the existing data, we have to conclude that there is insufficient data to help us support or refute the use of AT III intervention among trauma, obstetric, or paediatric populations.
Subgroup analyses regarding septic populations
Very few trials met our requirements in terms of trial intervention effect on various illness scores. We accepted the various definitions provided by the authors and undertook four different meta-analyses. The range of participant numbers in these analyses ranged from 28 to 156 and only one meta-analysis reached statistical significance. The meta-analyses examining the overall mortality in the septic population, based on 2601 participants, also failed to demonstrate a statistically significant reduction of mortality.
The heparin issue
A detrimental interaction between AT III and heparin was suspected before the Warren 2001 trial, and use of ATIII with and without heparin was predefined in the protocol for secondary analyses. However, the patients were not stratified according to heparin administration and the protocol allowed concomitant use of heparin by indication, after randomization to AT III or placebo. Even if the baseline comparison of patients allocated to AT III and placebo, in the subgroup without heparin, showed similar characteristics the randomization is violated in the subgroup analysis.
Pooling all trials with and without concomitant use of heparin, with the Warren 2001 trial as either a trial with concomitant use of heparin or as a trial without use of heparin, does not provide evidence of a statistically significant intervention effect of AT III. Splitting the Warren 2001 trial into two 'separate trials', with and without concomitant use of heparin, and pooling these results with the other trials does not provide a statistically significant intervention effect of AT III in the subgroup of trials without adjuvant heparin administration (RR 0.89, 95% CI 0.71 to 1.02; using a random-effects model (I² = 1.1%)). However, splitting the Warren 2001 trial violates the randomization procedure.
Trial sequential analysis
In a single trial, interim analysis increases the risk of type I errors. To avoid type I errors, group sequential monitoring boundaries (Lan 1983) are applied to decide whether a trial could be terminated early because of a sufficiently small P value, that is the cumulative z-curve crosses the monitoring boundaries. Sequential monitoring boundaries can be applied to meta-analysis as well, called trial sequential monitoring boundaries. In trial sequential analysis the addition of each trial in a cumulative meta-analysis is regarded as an interim meta-analysis and helps to decide whether additional trials are needed.
The idea in trial sequential analysis is that if the cumulative z-curve crosses the boundary a sufficient level of evidence is reached and no further trials are needed. If the z-curve does not cross the boundary then there is insufficient evidence to reach a conclusion. To construct the trial sequential monitoring boundaries the information size is needed and is calculated as the least number of participants needed in a single trial (Pogue 1997; Pogue 1998; Wetterslev 2007). The intervention effect suggested by the low-level of bias trials in the meta-analysis of the effect of AT III on mortality is a relative risk reduction (RRR) of 5% (Additional Figure 3) and the low-bias heterogeneity adjusted information size (LBHIS) calculated based on this intervention effect is 14,294 participants (Additional Figure 3). With an accrued information size of 3458 patients and no boundaries crossed so far, only 24% of the required information size is actually available to reject or accept a 5% RRR of overall mortality. To demonstrate or reject an a priori anticipated intervention effect of a RRR of 10% 3317 should be randomized. As 3458 patients are included in the present review without the meta-analysis becoming statistically significant an RRR of 10% or more on mortality is unlikely (Additional Figure 4).
Strengths and limitations
Our systematic review has several potential limitations. As for all systematic reviews our findings and interpretations are limited by the quality and quantity of available evidence on the effects of AT III on mortality. The risk of bias of the included trials was assessed by using the published data, which ultimately may not reflect the truth. All authors were contacted but only a few responded and provided further information. Three trials with 260 participants reported zero mortality in both study groups (Kobayashi 2003; Maki 2000; Mitchell 2003). Exploratory analysis adding an imagined trial with one death and 130 participants in each study group had no noticeable effect on the result.
We excluded six trials reporting mortality data from 285 participants since they were only published as abstracts (Balk 1995; Korninger 1987; Muntean 1989; Palareti 1995; Paternoster 2000; Schuster 1997). Data from these trials showed a 20% mortality in both the AT III and control groups (Additional Table 1). This is not in contrast to data provided by the included trials. When performing a sensitivity analysis combining the mortality data of these trials with the included trials any difference did not reach statistical significance (RR 0.96, 95% CI 0.89 to 1.04; using a fixed-effect model).
There was variation in the patient population; the type, dose, and duration of AT III treatment; and length of follow up. We observed the most beneficial effects of AT III on mortality in two trials with high risk of bias (Baudo 1992; Eisele 1998) and in two trials with low risk of bias (Fulia 2003; Haire 1998), with a total population of 180 patients.
Our decision to perform trial sequential analyses was taken after the protocol for this review was published. Despite the risk of being accused of performing post-hoc analyses, it is important to mention that this method was, in the main part, developed only after publication of our protocol (Deveraux 2005; Wetterslev 2007). Due to lack of convincing evidence in favour of AT III in settings without heparin, we chose to implement trial sequential analysis results since the hypothesis of a beneficial effect of AT III in critically ill patients still generates much attention.
Although there was minimal heterogeneity among trial results on mortality, we are aware that we pooled very heterogeneous trials in terms of patients, settings, and treatment regimens. Thus, the validity of our meta-analysis may be criticised for mixing apples and oranges. However, all included conditions cause low levels of AT III, can result in DIC, and have similar inflammatory pathways. Therefore, we think that there is a good biologic reason to perform a broad meta-analysis, which also considerably increases the generalizability and usefulness of the review. Further, a broad meta-analysis increases power, reduces the risk of erroneous conclusions, and facilitates exploratory analyses which can generate hypotheses for future research (for example adjuvant heparin) (Gotzsche 2000).
Implications for practice
There is insufficient evidence to support the use of AT III in any category of critically ill patients. We did not find a statistically significant effect of AT III on mortality; and AT III increased the risk of bleeding events. Subgroup analyses performed according to duration of intervention, length of follow up, different patient groups, and use of adjuvant heparin did not show differences in the estimates of intervention effects. Thus. based on this finding, we cannot recommend the routine use of AT III. Trial sequential analysis shows that there is sufficient evidence to reject a beneficial effect of more than 10% RRR (5% absolute risk reduction) on mortality and there is still the possibility that use of AT III may be harmful.
Implications for research
There is a need for a randomized trial with low risk of bias to evaluate the effectiveness of AT III without heparin before this intervention can be used routinely in critically ill patients. We recognize the heterogeneity in the patient population in the included trials and, as a consequence of the high mortality rate in the septic population, we believe that a new trial should address the effect of AT III in septic patients.
We would like to thank Dr John Carlisle, Prof Marcus Müllner, Dr Francois Fourrier, Dr Geoffrey Playford, Dr Christian Josef Wiedermann, Kathie Godfrey, and Nete Villebro for their help and editorial advice during the preparation of the protocol for the review.
We thank Dr John Carlisle (content editor), Dr Marialena Trivella (statistical editor), Dr Mark Simmonds (statistical comments), Prof Fourrier François; Dr Geoffrey Playford and Dr Christian J. Wiedermann (peer reviewers), and Kathie Godfrey (consumer representative) for their help and editorial advice during the preparation of this review.
We would also like to thank our local librarians for their assistance in developing the search strategy process and Dr Roberto S Oliveri for his support and advice during the preparation of this review.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Differences between protocol and review
- Index terms
Appendix 1. Search strategies
Last assessed as up-to-date: 4 November 2006.
Protocol first published: Issue 3, 2005
Review first published: Issue 3, 2008
Contributions of authors
Conceiving the review: Arash Afshari (AFSH), Ann Merete Møller (AMM)
Co-ordinating the review: AFSH
Undertaking manual searches: AFSH
Screening search results: AFSH, Jørn Wetterslev (JW)
Organizing retrieval of papers: AFSH
Screening retrieved papers against inclusion criteria: AFSH, JW, AMM
Appraising quality of papers: AFSH, JW, AMM
Abstracting data from papers: AFSH, JW
Writing to authors of papers for additional information: AFSH, JW
Providing additional data about papers: AFSH
Obtaining and screening data on unpublished studies: AFSH
Data management for the review: AFSH, JW
Entering data into Review Manager (RevMan 5.0): AFSH, JW
RevMan statistical data: JW, AFSH
Other statistical analysis not using RevMan: JW
Double entry of data: (data entered by person one: AFSH; data entered by person two: JW)
Interpretation of data: AFSH, JW, AMM, Jesper Brok (JB)
Statistical analysis: JW, AFSH
Writing the review: AFSH. JW, AMM, JB
Securing funding for the review: AMM
Performing previous work that was the foundation of the present study: AMM
Guarantor for the review (one author): AFSH
Person responsible for reading and checking review before submission: AFSH
Declarations of interest
Sources of support
- Cochrane Anaesthesia Review Group (CARG), Denmark.
- No sources of support supplied
Differences between protocol and review
We decided after publication of our protocol for this review to also include randomized trials examining the effect of ATIII on malignant diseases and cirrhosis. The decision was based on the desire to increase precision and power without confounding our data. The generalisability and usefulness of meta-analyses are increased considerably if the individual trials cover different patient populations, settings, and treatment regimen. Further, a broad (lumping) meta-analysis increases power, reduces the risk of erroneous conclusions, and facilitates exploratory analyses, which can generate hypotheses for future research. Usually it is also recommended to pool a broad range of studies (Gotzsche 2000).
We chose to exclude trials with AT III in patients with cardiovascular diseases, since ATIII in this field has been used to compare various simultaneous active interventions. For instance, AT III has been used in cardiovascular by-pass procedures in order to evaluate graft function versus conventional anti-coagulant therapy and in ischaemic patients, AT III has been compared to other anticoagulants in invasive trans-cutaneous-interventions as an adjunctive therapy to stent procedures. We believe it would be appropriate to examine its role in cardiovascular diseases in a separate systematic review.
We did not include trials reported only as abstracts unless they were part of ongoing and current studies. The reason for exclusion of 10 studies only published as abstracts in this review was due to serious shortcomings in reporting and design. The latest of these trials are over 10 years old and are still not published. These abstracts do not provide us with valid and sufficient data to examine mortality, bias, design, follow-up and intention-to-treat analysis. We anticipated that it would be impossible to contact the investigators and the authors. However, we do provide the limited mortality data that we were able to retrieve from these trials and have also conducted a sensitivity analysis examining the role of these data in the overall mortality of the included trials.
We also extended our search strategy to include the following additional databases: Latin American Caribbean Health Sciences Literature (LILACS); the Chinese Biomedical Literature Database; and CINHAL (Cumulative Index to Nursing & Allied Health Literature).
We decided to employ trial sequential analyses as a way of estimating the level of evidence of the experimental intervention.
In our protocol we defined the secondary outcome "Bleeding events within 14 days". However, we changed this to "Bleeding events" since we found it more relevant to look at the overall bleeding without applying any time constraint. Additionally, we found very few trials reporting bleeding events within the first 14 days.
We defined bleeding events as noted by the authors (requiring transfusions) and related to the intervention.
In our protocol we stated that in cases of heterogeneity (I
Medical Subject Headings (MeSH)
Anti-Inflammatory Agents [adverse effects; *therapeutic use]; Anticoagulants [adverse effects; *therapeutic use]; Antithrombin III [adverse effects; *therapeutic use]; Critical Illness [*mortality]; Randomized Controlled Trials as Topic
MeSH check words
* Indicates the major publication for the study