To the Editor:-I read with interest the recent study of transient radicular irritation (TRI) by Pollock et al. This is the first such study to be reported from the United States, and the results provide important confirmation of data from two European institutions. [2-4]These findings verify that transient neurologic symptoms frequently occur when lidocaine is used for spinal anesthesia and reinforce concern about the continued intrathecal use of this anesthetic. However, some aspects of the study's design and analysis warrant comment.
The strength of a randomized trial rests on "designing interventions that have only one major difference between any two study groups". It is, therefore, surprising that the authors chose to administer a hyperbaric solution of 5% lidocaine with 0.2 mg epinephrine, a hyperbaric solution of 0.75% bupivacaine without epinephrine, and an isobaric glucose-free solution of 2% lidocaine without epinephrine. (Though not specifically stated, it is also likely that the glucose concentrations of the hyperbaric lidocaine and hyperbaric bupivacaine solutions differed.) Therefore, among three experimental groups, there is no single comparison between any two that differs by only one relevant variable. This flaw in design hinders analysis of the potential effects of anesthetic agent, anesthetic concentration, glucose, baricity, and epinephrine, and sends the discussion into a tailspin of circular reasoning. For example, the possible contribution to TRI of one relevant factor such as epinephrine is ignored when interpreting the effect of a second, such as lidocaine concentration; conversely, the concentration of lidocaine is assumed to have no effect when interpreting the effect of epinephrine. The authors do offer a partial explanation for the choice of anesthetic solutions, stating that "Epinephrine was specifically included in only patients receiving 5% hyperbaric lidocaine in an attempt to determine whether the addition of epinephrine might increase the incidence of TRI." However, this reasoning would be valid only if epinephrine were the sole variable in question (but, then, there would be no reason to systematically vary anesthetic concentration or glucose content).
Because of the study's multiple variables, we must try to simplify interpretation by identifying factors likely to be irrelevant to the outcome variable. For example, the article references work in which it is demonstrated that glucose does not affect the potential of intrathecally administered lidocaine to induce sensory impairment in the rat. However, caution must be used in extrapolating to transient clinical effects-as appealing as the concept may be, it has not been established that anesthetic-induced neurologic injury and transient pain/dysesthesia share a common mechanism. In addition, preliminary data generated in the same model sharply conflict with findings in the current study (i.e., in the rat, adding epinephrine increases neurologic impairment induced by intrathecal lidocaine. Although we must be careful extrapolating from animal data, we must be even more cautious embracing unproven concepts, such as assuming that epinephrine might increase the incidence of TRI without entertaining the possibility that it might be protective.
The authors tried to "eliminate relative anesthetic potency as a possible cause of TRI" by basing their doses on potency data reported in an abstract by Langerman et al. Unfortunately, as Pollock et al. note, the 9:1 ratio initially reported for bupivacaine:lidocaine was subsequently modified to 8:1 before publication in a research manuscript. It is, therefore, puzzling that Pollock et al. continue to describe their doses as "equipotent". They also fail to consider that epinephrine may affect potency, despite data (including some obtained by co-authors of their study ) suggesting that epinephrine enhances intrathecal lidocaine anesthesia. Of greater concern, however, is the authors' reliance on this single study of potency, without reference to other relevant literature. Specifically, they acknowledge the limitation of applying potency data determined in the "intrathecal rat model"-actually obtained in the mouse-but do not consider that the 9:1 (or 8:1) ratio for bupivacaine:lidocaine is among the highest (if not the highest) ever reported for these two compounds, [11-13]including intrathecal data [12,13](some of which is contained in their reference list ). Interestingly, their own data also cast doubt that the anesthetic doses were equipotent-lidocaine and bupivacaine had a similar duration of anesthesia, suggesting that lidocaine, a shorter-acting agent, was administered at a relatively higher dose. Does it really matter that the potency of bupivacaine relative to lidocaine might have been overestimated? Very much so: if overestimated, we cannot be confident that an observed difference in TRI is not due, at least in part, to a disparity in dose.
Pollock et al. misinterpret the hypotheses and conclusions generated in our 1991 report of four cases of neurologic injury after continuous spinal anesthesia (CSA). Before this report, it was conventional wisdom that, with the possible exception of chloroprocaine. available local anesthetics did not produce "any neurotoxic effect when administered at recommended clinical concentrations." However, our analysis of these four cases suggested that injury occurred from a "direct neurotoxic effect of local anesthetic." We postulated that injury resulted when two factors, maldistribution and a relatively high dose of anesthetic, "exposed neural tissue to a toxic concentration of anesthetic." We described circumstances and factors that might favor maldistribution during CSA, such as sacral placement of a catheter or use of small-bore tubing. Finally, we proposed guidelines for the safe clinical practice of CSA, which included elimination of anesthetic solutions, such as 5% lidocaine, which greatly exceed minimum effective concentration. Pollock et al. focus on one of these elements, apply a form of analysis we would not use, and present a conclusion we would not reach (i.e., they assert "It was postulated, however, that the mechanics of microcatheters ... and large doses of local anesthetics were more to blame for cauda equina syndrome than toxicity specific to the local anesthetic." The argument that one element is "more to blame" than another might be appropriate in a lawsuit, but such reductionism trivializes critical interactions among etiologic factors, hinders understanding and misassigns risk. In addition, if one were to engage in such argument, simple logic would dictate that the anesthetic, not the catheter, was the culprit-anesthetic neurotoxicity can occur in the absence of a catheter, but not in the absence of an anesthetic.
Unfortunately, the authors' claim that this is the first prospective, randomized, double-blinded study of TRI is inaccurate. A study that meets these criteria was published by Hampl et al. 5 months before acceptance, and 9 months before publication, of the current article. Although this prior study likely appeared while the current article was under revision, the authors should have been aware of its publication, given their citation of subsequent work by the same investigators and by others. 
Ironically, one of the findings of the Hampl study was that the incidence of TRI with 5% lidocaine was equivalent whether lidocaine was administered with 7.5% or 2.7% glucose, a finding that suggests that differences in glucose concentration in the current study did not confound interpretation of other variables. Indeed, the contribution of the current study will continue to increase as other carefully controlled clinical studies eliminate concern regarding possible confounding variables and permit interpretation of the results of Pollock et al. 
Kenneth Drasner, M.D., Associate Professor of Anesthesia, University of California, San Francisco, San Francisco, California 94143-0648.
(Accepted for publication September 11, 1996.)