In recent years a desire to provide uniform health care standards has been clearly expressed by the medical community. Establishment of clinical guidelines grounded in evidenced-based medicine has become a major focus for national and international health care organizations around the world. It is of no surprise then that the role of steroid administration in acute spinal cord injury (SCI) has become subject to critical re-evaluation. Most physicians today prescribe steroids in this setting, not because of an understanding of the evidence surrounding their use but largely because the practice has become so common. The fear of medicolegal reprimand is also pervasive. Specialty groups have been slow to provide useful guidance to their members. This article attempts to provide an overview of the evidence to date and allows the reader to take part in the process of formulating a practice recommendation.
Several publications have undertaken to evaluate the efficacy of steroid administration in acute SCI in the clinical arena. Clearly, the most well-known and comprehensive efforts belong to the National Acute Spinal Cord Injury Study (NASCIS) group. However, attempts to elucidate a treatment effect have also been made by other investigators. In weighing the contribution of these studies to our present level of knowledge, it is useful to consider the design of each study and its outcome, in the context of level of evidence. The Canadian Task Force on the Periodic Health Examination has classified level of evidence into three main categories to help develop clinical practice recommendations. 18 Level I evidence for adopting a therapeutic strategy requires support from at least one properly randomized trial. Level II evidence is characterized by studies with control groups appropriate for the research question; however, the studies are not required to be prospective or randomized. Level III evidence rests with the opinions of respected experts (Table 1).
Depending on the level of evidence established in the literature and after consideration of issues of safety and efficacy, practice guidelines can be formulated defining a treatment as follows: a standard of care, a recommended treatment, a treatment option, or not recommended.
An example of a gold standard is the use of insulin to treat Type I diabetes. Whether using a bovine or human preparation, there are no equal or better alternatives to insulin for this disease. Moving down the list, if one type of therapy clearly stands out above others in a group of treatment strategies, it is considered a recommended treatment. For instance, amoxicillin can be considered the recommended treatment for pharyngitis caused by Group A Streptococcus, as opposed to a multitude of other potential antibiotic regimens. Finally, when a variety of treatments are available, all with similar clinical results, they can be classified as treatment options. Both hydrochlorothiazide and propanol can be considered treatment options for patients with mild hypertension.
A fifth category might also be added in cases in which clinical evidence is incomplete: that of investigational status. An investigational drug would be one whose safety and efficacy have not yet been clearly established (e.g., the use of recombinant bone morphogenic protein in promoting bone fusion) and therefore can be considered “not recommended.” However, under extenuating circumstances such as for compassionate use, investigational therapies are occasionally prescribed in a clinical setting.
To date, nine clinical studies have been published examining the effect of steroids on acute, nonpenetrating SCI (Cross reference from published literature and Medline Search [Spinal Cord Injuries, Therapy, Drug Therapy, limit to human]). Three have been reported by the NASCIS group, and six have been independently reported (Table 2). At first glance, based on the author’s conclusions and according to the criteria of Woolf et al, 18 there exists Level I evidence for the use of methylprednisolone in the treatment of acute SCI. However, there is also Level I evidence that fails to prove a treatment effect. Hence, the Woolf et al 18 criteria alone cannot help to formulate practice guidelines. Clearly, before any recommendations about the clinical use of methylprednisolone can be formulated, a closer look at the studies claiming to show a beneficial effect is required.
For the purpose of this review, several assumptions are made:
- Responsibility rests with the reporting authors to identify a priori comparisons in original reports and to precisely detail them in methods sections. All other comparisons are considered post hoc.
- Outcome measures identified in methods sections but not further reported are uninteresting (negative).
- Information disseminated by word of mouth or non–peer-reviewed publication cannot be considered as medical evidence.
Summary of the Literature
Bracken et al (1984) (NASCIS I).
The results of the NASCIS I trial were published in 1984. 1 This was a prospective randomized double-blind trial undertaken at nine hospitals in seven states. Patients with acute SCI were randomized to one of two treatment arms: 100-mg bolus followed by 25 mg every 6 hours for 10 days or a 1000-mg bolus followed by 250 mg every 6 hours for 10 days. A total of 330 patients were entered, of which 179 (54%) were available for the 6-month follow-up. No significant differences attributable to treatment were found in any of the primary neurologic outcome measures between the study groups. An almost 4× higher propensity toward wound infections was observed in the high-dose group (9.3%) compared with the low-dose group (2.6%). This reached statistical significance (P = 0.01). There were trends toward a higher incidence of sepsis, pulmonary embolus, and death in the higher-dose group that were not statistically important.
Bracken et al (1990, 1992) (NASCIS II).
NASCIS II was a prospective randomized double-blind trial undertaken in 10 hospitals in eight states. 2,3 A total of 487 patients were randomized to one of three treatment arms: methylprednisolone 30 mg/kg bolus in the first hour and 5.4 mg · kg −1 · hr −1 infusion for 23 hours; naloxone 5.4 mg/kg bolus and 4.5 mg · kg −1 · hr −1 for 23 hours; and a placebo infusion. Follow-up (not including deaths) was 97% at 6 months and 95% at 1 year. Neurologic outcome measures were not different between any of the treatment groups. However, if patients were stratified according to time to treatment (≤8 hours, >8 hours), those receiving steroids within 8 hours were reported to demonstrate neurologic improvement (Table 3). When further subdivided into complete and incomplete injuries, motor improvement was reported at 1 year in those patients demonstrating motor and sensory complete deficits as well as those who were motor and sensory incomplete. There was a twofold increase in wound infection and pulmonary embolus in those patients treated with steroids compared with controls; this was not statistically significant, but a power analysis was not provided.
As a historical footnote, the NASCIS II results were published after 6-month follow-up data became available and again after 1-year follow-up data were obtained. 2,3 Release of early findings to the media, before peer-reviewed publication, created considerable pressure on physicians to prescribe steroids for acute SCI if they weren’t already doing so. One-year follow-up results (not quite as encouraging as the 6-month data) did not receive the same publicity. The practice of prescribing methylprednisolone for acute SCI has remained widespread ever since.
This is a retrospective study based on 620 patients with severe cervical SCI treated in Poland from 1976 to 1991. 10 Patients were admitted within 24 hours of their injury. Dexamethasone was given in dosages of <24 mg or ≥24 mg over 24 hours to 290 of these individuals. A total of 330 patients did not receive steroids. It is not clear whether penetrating trauma was included or excluded. Time from injury to initiation of steroid therapy ranged from <8 hours to >24 hours.
Neurologic outcomes were based on a novel classification scheme: Group 1, motor paralysis with preserved sensation to the feet; Group 2, quadriplegia causing functionally useless extremities; and Group 3, paresis of lesser intensity (MRC grade >3). Patients were reported to have shown significant improvement if they could be reassigned by at least one group. Proportionately more patients were reassigned to a better neurologic outcome when treated with dexamethasone compared with controls. Length of follow-up is not specified. No statistical analyses were performed. The overall mortality rate was 21%, comprised mainly of patients with complete cord injuries.
In summary, although the author concludes that dexamethasone should be administered routinely and as early as possible in acute SCI, this retrospective study demonstrates serious design flaws, unacceptable outcome measures, poor documentation, and a lack of objective analyses. As such, it cannot contribute to an evaluation of level of evidence for the use of steroids in acute SCI.
Otani et al (1994).
A total of 158 patients were prospectively randomized to two treatment arms (without blinding): Group 1, methylprednisolone 30 mg/kg bolus in the first hour and 5.4 mg · kg −1 · hr −1 infusion for 23 hours thereafter; and Group 2, routine medical management. 12 All Group 1 patients received treatment initiation within 8 hours of injury. Control patients were allowed to receive steroids other than methylprednisolone for the purpose of treating SCI, if considered appropriate by the attending physician. Neurologic outcome measures were identical to those used in the NASCIS studies with the exception of a modified sensory scale. Of the 158 patients entered in the study, 41 (26%) were excluded from the analyses (mostly controls) for protocol violations. Of the remaining 117 patients (methylprednisolone n = 70, control n = 47), a 6-month follow-up was available on all but one. The large discrepancy in numbers between patients in treatment and control groups is due to a disproportionately large number of patients withdrawn from the control group.
None of the neurologic outcome measures differed significantly between the two treatment groups (Table 4). Post hoc analyses suggested that significantly more patients in the steroid cohort experienced some degree of sensory improvement compared with controls (68%vs. 32%). Since overall mean improvement (American Spinal Injury Association [ASIA] scores) was no different between groups, this therefore dictates that the magnitude of recovery for those individuals who showed evidence of improvement was greater for control patients. No such differences were encountered with respect to motor function. Although the authors conclude that their results support the use of methylprednisolone in acute SCI, this closer look at the study reveals serious design flaws, overall negative outcomes, and counterintuitive post hoc results.
Prendergast et al (1994).
Over a 4-year period from 1989 to 1992, bridging implementation of the NASCIS II 24-hour methylprednisolone protocol, 54 patients with acute SCI were reviewed. 16 Twenty-nine patients received steroids and 25 did not. Thirty-one patients with penetrating injuries were included. Follow-up extended over a 2-month period from the time of admission. Motor and sensory assessments were performed on admission, at 4 days, and at 1, 2, 4, and 8 weeks. There was no difference in neurologic improvement in patients with nonpenetrating (blunt) injuries treated with or without methylprednisolone. Of those patients with penetrating injuries, the group treated with steroids demonstrated neurologic deterioration compared with improvement observed in controls within the first week of injury that persisted thereafter. This difference was statistically significant (P < 0.05).
George et al (1995).
Over a 3-year period from 1989 to 1992, bridging implementation of the NASCIS II 24-hour methylprednisolone protocol, 130 patients with acute SCI were reviewed. 8 Seventy-five patients received steroids and 55 did not. Nine patients with penetrating injuries were included. Length of follow-up was not clearly specified but was likely between 3 and 6 months for 54% of patients. The steroid-treated group was younger and had lower Injury Severity Scores than the control group (P < 0.05), at least theoretically biasing them toward a potentially better outcome. Functional Independence Measure (FIM) scores were no different among the treatment groups. A trend toward higher infectious complications was observed in the methylprednisolone-treated patients but was not statistically significant.
Poynton et al (1997).
Seventy-one consecutive patients with acute SCIs in Dublin over a 31/2-year period were reviewed. 15 All patients were prospectively assessed with ASIA criteria on admission, before transfer to the rehabilitation unit, and at follow-up. The mean time to follow-up from injury was 30 months (range 13–57 months). Methylprednisolone was given according to the NASCIS II 24-hour protocol to patients seen within 8 hours of injury. Patients seen more than 8 hours from the time of injury were not given steroids; they served as the control group. Nonparametric statistical analyses failed to demonstrate differences in motor or sensory recovery between the two treatment groups.
Subanalyses according to level and severity of injury were also statistically insignificant. A trend toward better motor scores was observed in quadriplegic and quadriparetic patients receiving methylprednisolone. However, a trend toward poorer motor scores was noted in paraparetic patients treated with steroids. Greater sensory improvement was seen in quadriplegic patients treated with steroids, but poorer sensory scores were seen in quadriparetic patients treated with steroids. The best predictor of outcome was related not to treatment group but to severity of injury; incomplete patients showed significantly better recovery than complete patients.
Bracken et al (1997, 1998) (NASCIS III).
NASCIS III was a prospective randomized double-blind trial undertaken in 16 centers in the United States and Canada. 4,5 A total of 499 patients were randomized to one of three treatment arms: methylprednisolone 5.4 mg · kg −1 · hr −1 infusion for 24 hours; methylprednisolone 5.4 mg · kg −1 · hr −1 infusion for 48 hours; or tirilazad 2.5 mg/kg every 6 hours for 48 hours. All patients received a 20–40-mg/kg bolus of methylprednisolone before randomization. Treatment was initiated within 8 hours in all patients. Follow-up (not including deaths) was 95% at 6 months and 92% at 1 year (88% 1-year follow-up including deaths).
Motor and sensory scores (light touch, pinprick, and pressure sensation) were not different between any of the treatment groups. FIM scores were reported improved in the areas of self-care and sphincter control for the 48-hour group at 6 months. This effect was lost at 1 year. If patients were stratified according to time to treatment (<3 hours, 3–8 hours), those receiving therapy between 3 and 8 hours were reported to demonstrate improved neurologic function on the 48-hour protocol compared with the 24-hour protocol at 6 weeks and 6 months (Table 5). This effect was also lost at 1 year.
There was a 2× higher incidence of severe pneumonia and a 4× higher incidence of severe sepsis in the 48-hour group compared with the 24-hour patients. These differences were reported as statistically insignificant, but a power analysis was not willingly provided. Sample size calculations suggest that to statistically rule out a difference in the rate of wound infection would require a sample size of >1400 patients in each arm. 9 Although overall mortality rates were comparable between groups, there was a sixfold higher incidence of death due to respiratory complications in the 48-hour patients compared with the 24-hour cohort (P = 0.056).
Pointillart et al (2000).
In this prospective trial from France (originally published in French 13), 14 106 patients were randomly assigned to one of four treatment groups: methylprednisolone 30 mg/kg bolus in the first hour and 5.4 mg · kg −1 · hr −1 infusion for 23 hours; nimodipine 0.015 mg/kg/hr for 2 hours followed by 0.03 mg · kg −1 · hr −1 for 7 days; both agents together; and a placebo group. Medications were initiated within 8 hours of the time of injury. An independent examiner, blinded to the treatment protocol, assessed neurologic outcomes based on the ASIA scoring system. One patient was lost to follow-up, five patients died, and 100 patients were available for examination at 1 year. No significant differences were found after 1 year between any of the treatment arms (Table 6). Although study numbers are small, it is clear that not even a trend toward improvement was observed in steroid-treated patients. However, a trend toward infectious complications was observed in those receiving methylprednisolone (66%vs. 45%). This did not reach statistical significance.
Of the nine published studies available to judge level of evidence to date, only two actually report significant improvement from the use of steroids in SCI in a reasonably scientific manner: NASCIS II and NASCIS III. Technically, at face value they may both be considered as Level I evidence supporting the use of methylprednisolone in acute SCI because of their prospective randomized nature. How then can one resolve the discrepancy of having Level I evidence both for and against the use of steroids in SCI? Clearly, further considerations are required, above and beyond simple summarization of trial design and outcomes, to help better judge the quality of this Level I evidence.
Critically Addressing the Quality of Level I Evidence
The criteria of Woolf et al 18 define a critical first step in evidence-based analyses, allowing literature to be ranked or weighted according to trial design. However, these criteria alone provide no insight with respect to the quality of evidence within this ranking. It is important to have a mechanism to assure that the authors’ conclusions are warranted by the results they have published.
Quality of evidence can be appreciated in detail through a short series of considerations, or a checklist. 9 Briefly, acceptance of a new treatment should be forthcoming when the clinical evidence is in the form of a prospective randomized double-blind trial that is well designed, is well executed, demonstrates compelling data (with face validity and internal consistency), is subjected to appropriate statistical analyses, and shows changes in outcomes meaningful to the patient (Table 7). It also follows that the results of such a study should be independently reproducible. In considering these criteria, one can quickly appreciate that the evidence for a new treatment must meet not just one, but each specific requirement. Failure in any one category critically undermines the validity of the study and disqualifies the treatment from becoming routinely used in a clinical setting.
Several reviews have been recently published, severely criticizing interpretation of the data and subsequent conclusions of the NASCIS II and III studies. 7,9,11,17 Most of the faults cited can be classified into the last four items of the checklist. So far, NASCIS authors have not made their data available for independent examination, to either refute or confirm these criticisms. They are summarized in the following paragraphs.
All primary outcomes, defined before patient enrollment, were negative. The only interesting findings were encountered when post hoc analyses were performed on an arbitrary stratification of patients into those treated before and those treated after 8 hours from the time of injury. The rationale behind this particular time window is based on a median time to treatment of 8.5 hours. 6 However, a total of 487 patients were entered into the NASCIS II study; analysis of a true median time to treatment would assign 50% of patients (244 of 487) before an 8.5-hour cutoff and 50% after. These results are not available. Instead, an apparently arbitrary cutoff of 8 hours was chosen, allowing for only 38% of patients (183 of 487) to be included in the post hoc analysis. Poor performance of the <8 hour control group compared with the total group of controls has been noted. 7 The subsequent results are therefore suspicious for a random event. They are also external from the primary analyses and therefore cannot be considered as Level I evidence.
Reported treatment effects are small. 9 In addition, these small changes in neurologic function cannot be assigned clinical significance. 11 For example, an improvement of 5 motor points spread across five motor segments is likely of little clinical significance, especially if the grade is improving from 0–5 to 1–5. Alternatively, an increase from 0–5 to 5–5 in only one muscle group is also unlikely to be of clinical significance. When mean improvement is examined not as a function of baseline but rather as a function of the entire measurement scale (representing complete quadriplegia to normalcy), the difference between treatment groups becomes obscure (Figure 1). Despite huge clinical relevance, the other half of the available (contralateral) neurologic data are not accessible to either confirm or negate these differences, again making published observations suspicious for a random event.
Statistical comparisons of neurologic outcomes are performed by >60 t tests. No corrections are provided for multiple comparisons. Had repeated measures analysis of variance or multivariate analyses been performed, it is likely that none of the results would have been significant. In addition, violations of the assumptions of normal distribution suggest that nonparametric statistical methods should have been employed, likely with a similar negative outcome. 7
In summary, if more than half of the patients enrolled in the study are excluded and if more than half of the neurologic data are ignored, the only potentially interesting finding in NASCIS II after 1 year of follow-up is a 5-point increase in mean motor improvement compared with controls. The statistical significance of this result is doubtful, as is the clinical relevance. Because of these marginal findings, it is unlikely that the study will ever be repeated. No other investigators have been able to reproduce the results of NASCIS II.
All primary outcomes, defined before patient enrollment, were negative. Similar to NASCIS II, the only interesting findings were encountered when post hoc analyses were performed. This time patients were arbitrarily divided into those treated before 3 hours and those treated between 3 and 8 hours from the time of injury. The rationale behind this particular time window is unknown and not intuitive. Consequently, almost 70% of the study population is excluded from further analyses. The data from the ensuing subanalyses therefore raise suspicions of random events. They are also external from the primary analyses and therefore cannot be considered as Level I evidence.
Reported treatment effects within the select group of patients analyzed are small and, after 1-year follow-up, not statistically significant. Similar to NASCIS II, the small changes in neurologic function cannot be assigned clinical significance. FIM scores, obtained in NASCIS III to address the problem of clinical significance, were no different between treatment groups. When mean improvement is examined not as a function of baseline but rather as a function of the entire measurement scale (representing complete quadriplegia to normalcy), the difference between treatment groups remains obscure (Figure 2). Analysis of compliers has been proposed to provide even more significant results compared with the intent to treat analysis. 5 However, this type of comparison is invalid for several reasons and should not be considered further. 9
Statistical comparisons of neurologic outcomes are performed by >100 t tests. No corrections are provided for multiple comparisons. Concerns over violations of the assumptions of normal distribution also suggest that nonparametric statistical methods should have been used in this study as well. 7
In summary, if almost 70% of the patients enrolled in the study are excluded and if more than half of the neurologic data are ignored (right-sided deep pain and pressure sensory results, all left-sided sensory and motor scores), the only potentially interesting finding in NASCIS III after 1 year of follow-up is a 5-point increase in mean motor improvement in the 48-hour group compared with the 24-hour group when treated between 3 and 8 hours after injury. This result is not statistically significant and, in all likelihood, of no clinical relevance. Because of these marginal findings, it is also doubtful that NASCIS III will ever be repeated.
Detailed review of the NASCIS II and NASCIS III trials shows that despite classification as Level I evidence, they suffer from serious flaws in data analyses and subsequent conclusions (Table 8). Primary outcomes are uniformly negative. Conclusions are based solely on the results of post hoc comparisons.
Within the post hoc analyses a compelling treatment effect is not apparent (absent face validity). Internal consistency is lacking (variable trends toward improvement or deterioration among different outcome measures within the same group of patients). Errors in statistical methodology, particularly problems with multiple comparisons and the rationale behind time-to-treat analyses, create serious doubts about reported significance levels. Clinical relevance is indeterminate and likely negligible. Therefore, neither NASCIS II nor NASCIS III can be considered as providing acceptable evidence (Level I or otherwise) to support the use of methylprednisolone in acute SCI. From a guidelines perspective, neither study can be considered to support the use of methylprednisolone as a standard of care, as a recommended treatment, or even as a treatment option in acute SCI.
The positive results claimed in NASCIS II and NASCIS III have not, so far, been independently reproduced. There exists no convincing Class II or even Class III evidence that makes a reasonable argument in favor of the use of methylprednisolone for acute SCI. Neither efficacy nor safety has been established. Indeed, four of the nine studies reviewed have observed trends toward higher infectious complications in steroid-treated patients. The death rate from respiratory compromise may be up to 6× higher in those treated for 48 hours.
Until a reliable and reproducible therapeutic effect is better documented, 24-hour methylprednisolone administration should not be routinely used in patients with acute SCI. At the present time and until further trials are performed, 24-hour methylprednisolone must be considered as an investigational therapy. If, despite the lack of clinical evidence, its use is contemplated on purely compassionate grounds, implicit with this designation is a detailed process of informed consent. Each patient undergoing 24-hour methylprednisolone treatment must receive a thorough explanation about the agent’s investigational status and comprehensive information about risks as well as benefits.
Because of the lack of therapeutic evidence along with potentially harmful side effects including death, 48-hour methylprednisolone administration should not be prescribed in the setting of acute SCI at all.
- Review of published data does not support the routine use of 24-hour methylprednisolone in patients with acute spinal cord injury.
- Methylprednisolone administration for 48 hours in patients with acute spinal cord injury may be harmful.
The author thanks Dr. S. Nesathurai for his kind provision of an English translation of the article by Otani et al.
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