Goal directed fluid therapy: careful with conclusions

Sir, With great interest, I have read the article by Bisgaard et al on the hemodynamic optimization in lower limb artery surgery. The authors randomized prospectively 40 patients into two groups. The intervention group received fluid therapy guided by stroke volume index by the LIDCOTMplus system; the control group was given fluid guided by surrogate parameters such as hourly urine output, standard hemodynamic parameters and arterial blood gas values. The primary outcome was the incidence of post-operative complication. I note four limitations in this study that were not discussed in the paper but I want to discuss here. First, the authors intended to demonstrate a 33% decrease in an assumed complication rate of 0.25. This results in a complication rate of 17% in the intervention group. With 72 + 72 patients included, the power will be only 0.22 (0.33 if two-sided test). To reach a power of 0.80, the authors need to include 320 + 320 patients (406 + 406 if two-sided test). A power of 0.80 with 72 + 72 patients included correlates to a reduction from 0.25 to 0.08, which is a reduction of nearly 70%. This would in my eyes be an unrealistic reduction of complications. I ask the authors to clarify how they performed the sample size calculation. Also, they should state if a one-sided or twosided test was performed, as it is recommended to use a twosided test to avoid false-positive trials. Second, the authors planned to include 144 patients but managed only to include 40 and evaluate these patients only. This is valid, but the authors state also that they excluded patients from a secondary hospital because of slow inclusion rate. When including less than one-fourth of the scheduled patient number in the analysis, the study is heavily underpowered. I do not understand why the authors then exclude the patients from the secondary hospital. Slow inclusion rate is not an exclusion criterion for this study. A proper analysis would include all patients randomized for this study. Third, the authors used multiple regression and stepwise elimination to analyze the data. In a sample size as small as presented, this method leads to ‘overfitting’ of the results. Overfitting yields too optimistic results of the data, while the findings do not really exist in the population and are not replicable. The use of this method is highly discouraged in small samples. The authors should explain why they justified the use of this method. Fourth, there is an error when presenting the primary outcome: number of patients with complications. Of all 20 + 20 patients, 5 in the intervention group and 11 in the control group developed a complication, presented statistically as a difference of P = 0.05. The authors conclude that the intervention decreased the number of complications in this study. However, when recalculating significance level with a one-sided Fisher’s exact test, I find P = 0.05267 (confidence interval 0.00–1.016), which is above the significance level. A two-sided test would result in P = 0.105 In conclusion, there are several major limitations in this study: the study is heavily underpowered with low sample size, patients are excluded from the study without proper explanation, the analyzed method causes overfitting, and the primary outcome should be presented as not significant, especially because one-sided tests were used. The authors need to be careful with any conclusion given these limitations. This study cannot give any conclusions on whether individualized goal-directed therapy has any influence on post-operative complications or not. However, I think it is highly important for the scientific community that also these kinds of studies with no significant results are published. Conflict of interest: The author has no conflict of interest.