Validation in terms of CV risk calculation or correlation with insulin resistance? I haven't seen it addressed here on Sensible Medicine. However it is one of Peter Attia's obsessions:
- as I recall, there are some data which suggest a difference in softer outcomes like AKI, when these two fluids are compared (I think the SALT-ED trial was one of these?)
- however, repeated large trials such as this one seem to confirm there is no mortality difference (at least, none that is detectable at the population level)
- Therefore, we left with the following situation: we have a choice between two possible interventions which are widely available, generally similar , and with no hard data supporting one or the other.
- however, we still need to make a decision.At this point it seems rational to decide on the basis of more speculative considerations. There’s a reasonable physiology argument to be made that lactated ringers is safer than NS. There’s also some evidence that it reduces AKIs, potentially. It also does not contribute to the acidosis we can see with prolonged NS administration.
- therefore, I pretty much always use LR based on the above considerations.
First, I think the term "estimand" is confusing to most people who read journals at this point and just refers to the thing you are trying to estimate. In this study, the estimand is the average effect of a hospital fluid policy on patient outcomes (primary outcome death or readmission). There's nothing special about this language -- it's unrelated to the somewhat odd study design.
Second, I think your criticism of the trial is dead on.
No one wonders whether KVO fluids with LR is better than with NS, so including such patients in the analysis just tends to cause a null result. If I want to know whether car airbags save lives, I can't include large amounts of driving in parking lots and driveways in my analysis -- I may have stated the question broadly -- "Do airbags save lives?" -- but I really, really wasn't wondering about whether they save lives while parking.
If you want to know whether large volume fluid repletion with LR is better than with NS, you could still use cluster randomization, but you need to have defined "large volume" before the trial starts and you need to be able to find the patients who got that amount of fluids.
I love reading articles which explain statistical methods in a way I can understand. Since I was never any good at all that I choose to go into private practice instead of academia. At the risk of making a complete fool of myself, not unheard of in my 35 year career in the ICU sitting for one malpractice deposition (which we won), I say I immensely disliked messing around with hypernatremic, hyperchloremic acidosis after a resuscitation. Valid or not that that’s what I chose years ago.
Around the turn of the century someone told us to spend a ton of money on CVO2 monitors, train ED docs to insert them and train ED nurses to use them because someone said watching the CVO2 go up was a good thing in septic patients. I went off that reservation before we got on it simply because it was too damned complicated and expensive, plus we actually had patients to actually take care of in our ED. And there isn’t even a plaque or a sign in the ED nurses break room thanking me for sparing them. Later, a financial relationship between the manufacturer those devices and the publisher of the study was made public…
Shortly after that, something called Xigris became available and a very influential international Critical Care maven stood up at a Las Vegas Weil symposium and proclaimed that it was “malpractice” to not use it in every septic patient with an elevated lactate. I know I heard that, and that made even less sense to me (and a lot of other people present). “Xigris” scared the hell out of me, which is why I didn’t use it more than once.
But I digress. The RL v Saline v albumin v dextrans “arguments” have been going on for a generation and has outlived me. As one commenter said. If no one can show a difference after all this time, there probably isn’t.
I'm a pretty good causal inference scholar. I do not agree with your criticism of the overall trial. You believe that there may have been non-zero treatment effects for subsamples. Sure. The trial creators could have pre-specified subsamples of interest. They could have required balance on subsamples (number of patients) between the two halves of the trial. They could have used inverse propensity weights or something like that to rule out the influence of random variation in observed patient characteristics. Subsamples would have been smaller, and standard errors would have been larger, so it would have been harder to find significant differences. But we still learn that there is no significant difference on average. Which provides evidence, not conclusive but still evidence, against differences.
Your criticism would be stronger if you had substantive reasons, based on underlying science, to expect differences for different types of patients, but you did not suggest that.
If, after having randomized thousands of patients over a large number of trials, there is no clear answer to the question of which fluid is better for volume-depleted patients, then it seems likely that there truly is no difference between them.
Better, perhaps to ask, why it should be anticipated that there would be a difference. That is, what are the electrolyte abnormalities that should be addressed by LR but not by NS? And how serious would these abnormalities need to be such that addressing them with (just) LR should make a life saving difference?
Just because something might make a difference doesn’t mean it actually does.
Time to spend precious research dollars on more pressing questions.
Certainly. The first clinical trial of Viagra—a randomized clinical trial with a crossover design—was conducted with only nine (9) patients, meaning a total sample size of N = 18. And that was enough to demonstrate, to this day, its remarkable efficacy, with a Number Needed to Treat (NNT) just above 1.
It never required a meta-analysis, except for subsequent studies aimed at assessing its safety in certain patient groups.
In other words, when an intervention is truly and genuinely effective, this becomes clinically evident with the very first patient subjected to comparison.
If the effect is only modest, then large sample sizes are needed to demonstrate those modest differences. However, the efficacy of an intervention cannot “increase” simply by increasing the sample size—which is what meta-analyses do. They only provide greater statistical power and reduce type II error (1 - beta) to detect differences if those differences truly exist.
I have been following this debate on fluids since ~1975. It was a question being asked during my ~4 years working as a professional ambulance EMT and was still a question when I retired from the practice of Emergency Medicine in 2010. One wonders if all the money spent on this would have been better spent elsewhere. With this as context, I am not opposed to the reorientation and cuts in funding now being forced upon our healthcare research industry...
Interestingly, I just wrote about the need for more Bayesian analysis in nutrition especially with respect to observational research.
I’m a little confused though — was the study meant to examine whether LR is more protective than normal saline or the extent to which LR itself is protective? Because those are obviously two different questions and it feels like the Bayesian conclusion didn’t contemplate group differences, merely overall effectiveness?
The first rule of external validity—or the possibility of generalizing or extrapolating results from the study population to a target population—is to have excellent internal validity. Programmatic studies, in their attempt to achieve generalization, are only valid if they do not violate the fundamental methodological principles that ensure internal validity.
In principle, a crossover design—initially used as an alternative random allocation method—in a population different from the one existing before the crossover, with an unblinded (i.e., open-label) intervention, and carried out unsystematically (perhaps by different personnel who may hold biases about the interventions—for example, I personally trust and prefer Ringer’s lactate ten times more than saline solution, or vice versa, in my everyday practice)—may have introduced such a degree of bias that any potential differences disappeared.
In other words, the potential success that random allocation might have produced—as would be evident in a well-balanced Table 1—was lost once the allocation sequence and the nature of the intervention were known, at least to those performing the intervention.
Incidentally, I vividly recall that the first RCT on pulmonary surfactant for the prevention of hyaline membrane disease in preterm infants failed to demonstrate evidence of the clinical effect—which is otherwise quite evident—because the study was “open” and unblinded. As a result, the nursing staff delivered “schizophrenically meticulous” care and airway cleaning for patients in the non-intervention arm.
Incidentally, so-called “Normal” or “Physiological” Saline Solution is neither physiological nor normal. It has an extremely low pH (around 4.5) and contains nearly 50% more chloride than human plasma. Thus, the use of large volumes of saline for resuscitation—especially in pediatrics—can lead to hyperchloremic acidosis.
It is certainly true that large volumes of NS leads to a transient hyperchloremic metabolic acidosis in babies and young children. So maybe it makes sense to hypothesize that using LR instead is better. But what is “better”? An example of where LR might be better than NS (and could prompt an RCT).
In this case, the key observation is that the NS-induced acidosis is mild, transient, and requires no treatment. However, in fact, it doesn’t matter in either the short or long term which fluid is used. And so, the beaten horse could be left alone to recover.
Very sharp observation. Clearly, the human kidney and the neuro-endocrine-metabolic system know more than the collective brains of all physicians.
This matter reminds me of the major debate that took place about 20 years ago, when the efficacy of resuscitation—specifically regarding mortality outcomes—was tested in patients with sepsis and capillary leak. The comparison of crystalloids versus colloids led to the conclusion that colloids actually increased mortality.
But also, my dear JDM, let’s not forget that the “invention” of normal saline—or “physiological serum”—as an emulation of plasma solvent, was never experimentally evaluated against more physiologically adjusted solutions tailored to the cause and type of fluid loss requiring resuscitation.
Hypovolemic shock due to hemorrhage is not the same as shock from cholera-induced diarrhea, or rotavirus-induced diarrhea, or cardiogenic shock, or neurogenic shock, and so on. That is why, in the bygone days “of barbaric nations,” we used to prepare crystalloids under laminar flow hoods, tailoring them to the specific etiology and mechanisms involved in our patients—an approach that, although observational rather than experimental, yielded enormous clinical benefits.
Alternate view. You are the CFO sitting with the CMO. The GPO you deal with sells NS at a discount to the LR. From a hospital-level POV, is there net harm or benefit from converting the system from one formulation to another? Some interventions are one-size-fits-all and have a positive ROI, while others may not (e.g., VTE prophylaxis for all strategy).
Can I go off on a tangent here? I was pondering a trial design where the arms are two different patient selection algorithms. Let's use nasal surgery for OSA as our scenario. Right now the patient selection algorithm is that an otolarygologist offers you a surgery. There is no filter. The surgery has a 15% success rate. So far this is not a hypothetical. This is literally what happens in the real world.
Now let's imagine a different patient selection algorithm. Sleep Medicine measures your overnight breathing with a pressure-sensitive cannula. If you breathe through your mouth all night, you are referred to otolaryngology for nasal surgery. Nasal-breathers are not referred because the surgery won't help. Lo and behold success rates are now (hypothetical, this would be the point of the study) way better, say 75%.
Is there some reason we can't implement this as an RCT where we measure the difference in successful surgeries between the current patient selection algorithm and my new and improved one? The arms are selection algorithms not treatments.
Has anyone written on the advanced cardiac IQ lipid panel? Do those tests by quest, such as LPL particle size have real world validation? Thank you
Validation in terms of CV risk calculation or correlation with insulin resistance? I haven't seen it addressed here on Sensible Medicine. However it is one of Peter Attia's obsessions:
https://peterattiamd.com/the-straight-dope-on-cholesterol-part-v/
"In this post we’ll address the following concept: Does the size of an LDL particle matter?"
There's gotta be hours of The Drive devoted to it. Maybe listen to the Dayspring or Sniderman interviews among others.
My thoughts about this question:
- as I recall, there are some data which suggest a difference in softer outcomes like AKI, when these two fluids are compared (I think the SALT-ED trial was one of these?)
- however, repeated large trials such as this one seem to confirm there is no mortality difference (at least, none that is detectable at the population level)
- Therefore, we left with the following situation: we have a choice between two possible interventions which are widely available, generally similar , and with no hard data supporting one or the other.
- however, we still need to make a decision.At this point it seems rational to decide on the basis of more speculative considerations. There’s a reasonable physiology argument to be made that lactated ringers is safer than NS. There’s also some evidence that it reduces AKIs, potentially. It also does not contribute to the acidosis we can see with prolonged NS administration.
- therefore, I pretty much always use LR based on the above considerations.
Dr. Mandrola, two thoughts on this:
First, I think the term "estimand" is confusing to most people who read journals at this point and just refers to the thing you are trying to estimate. In this study, the estimand is the average effect of a hospital fluid policy on patient outcomes (primary outcome death or readmission). There's nothing special about this language -- it's unrelated to the somewhat odd study design.
Second, I think your criticism of the trial is dead on.
No one wonders whether KVO fluids with LR is better than with NS, so including such patients in the analysis just tends to cause a null result. If I want to know whether car airbags save lives, I can't include large amounts of driving in parking lots and driveways in my analysis -- I may have stated the question broadly -- "Do airbags save lives?" -- but I really, really wasn't wondering about whether they save lives while parking.
If you want to know whether large volume fluid repletion with LR is better than with NS, you could still use cluster randomization, but you need to have defined "large volume" before the trial starts and you need to be able to find the patients who got that amount of fluids.
Thanks for doing this review of the study!
I love reading articles which explain statistical methods in a way I can understand. Since I was never any good at all that I choose to go into private practice instead of academia. At the risk of making a complete fool of myself, not unheard of in my 35 year career in the ICU sitting for one malpractice deposition (which we won), I say I immensely disliked messing around with hypernatremic, hyperchloremic acidosis after a resuscitation. Valid or not that that’s what I chose years ago.
Around the turn of the century someone told us to spend a ton of money on CVO2 monitors, train ED docs to insert them and train ED nurses to use them because someone said watching the CVO2 go up was a good thing in septic patients. I went off that reservation before we got on it simply because it was too damned complicated and expensive, plus we actually had patients to actually take care of in our ED. And there isn’t even a plaque or a sign in the ED nurses break room thanking me for sparing them. Later, a financial relationship between the manufacturer those devices and the publisher of the study was made public…
Shortly after that, something called Xigris became available and a very influential international Critical Care maven stood up at a Las Vegas Weil symposium and proclaimed that it was “malpractice” to not use it in every septic patient with an elevated lactate. I know I heard that, and that made even less sense to me (and a lot of other people present). “Xigris” scared the hell out of me, which is why I didn’t use it more than once.
But I digress. The RL v Saline v albumin v dextrans “arguments” have been going on for a generation and has outlived me. As one commenter said. If no one can show a difference after all this time, there probably isn’t.
In my more simplistic
In my more simplistic PA brain, Doctor 909,
I'm a pretty good causal inference scholar. I do not agree with your criticism of the overall trial. You believe that there may have been non-zero treatment effects for subsamples. Sure. The trial creators could have pre-specified subsamples of interest. They could have required balance on subsamples (number of patients) between the two halves of the trial. They could have used inverse propensity weights or something like that to rule out the influence of random variation in observed patient characteristics. Subsamples would have been smaller, and standard errors would have been larger, so it would have been harder to find significant differences. But we still learn that there is no significant difference on average. Which provides evidence, not conclusive but still evidence, against differences.
Your criticism would be stronger if you had substantive reasons, based on underlying science, to expect differences for different types of patients, but you did not suggest that.
Bernie Black, Northwestern University
I love reading the comments as much as the articles. I learn something every single time.
If, after having randomized thousands of patients over a large number of trials, there is no clear answer to the question of which fluid is better for volume-depleted patients, then it seems likely that there truly is no difference between them.
Better, perhaps to ask, why it should be anticipated that there would be a difference. That is, what are the electrolyte abnormalities that should be addressed by LR but not by NS? And how serious would these abnormalities need to be such that addressing them with (just) LR should make a life saving difference?
Just because something might make a difference doesn’t mean it actually does.
Time to spend precious research dollars on more pressing questions.
Certainly. The first clinical trial of Viagra—a randomized clinical trial with a crossover design—was conducted with only nine (9) patients, meaning a total sample size of N = 18. And that was enough to demonstrate, to this day, its remarkable efficacy, with a Number Needed to Treat (NNT) just above 1.
It never required a meta-analysis, except for subsequent studies aimed at assessing its safety in certain patient groups.
In other words, when an intervention is truly and genuinely effective, this becomes clinically evident with the very first patient subjected to comparison.
If the effect is only modest, then large sample sizes are needed to demonstrate those modest differences. However, the efficacy of an intervention cannot “increase” simply by increasing the sample size—which is what meta-analyses do. They only provide greater statistical power and reduce type II error (1 - beta) to detect differences if those differences truly exist.
I have been following this debate on fluids since ~1975. It was a question being asked during my ~4 years working as a professional ambulance EMT and was still a question when I retired from the practice of Emergency Medicine in 2010. One wonders if all the money spent on this would have been better spent elsewhere. With this as context, I am not opposed to the reorientation and cuts in funding now being forced upon our healthcare research industry...
Interestingly, I just wrote about the need for more Bayesian analysis in nutrition especially with respect to observational research.
I’m a little confused though — was the study meant to examine whether LR is more protective than normal saline or the extent to which LR itself is protective? Because those are obviously two different questions and it feels like the Bayesian conclusion didn’t contemplate group differences, merely overall effectiveness?
Dr. Mandrola,
The first rule of external validity—or the possibility of generalizing or extrapolating results from the study population to a target population—is to have excellent internal validity. Programmatic studies, in their attempt to achieve generalization, are only valid if they do not violate the fundamental methodological principles that ensure internal validity.
In principle, a crossover design—initially used as an alternative random allocation method—in a population different from the one existing before the crossover, with an unblinded (i.e., open-label) intervention, and carried out unsystematically (perhaps by different personnel who may hold biases about the interventions—for example, I personally trust and prefer Ringer’s lactate ten times more than saline solution, or vice versa, in my everyday practice)—may have introduced such a degree of bias that any potential differences disappeared.
In other words, the potential success that random allocation might have produced—as would be evident in a well-balanced Table 1—was lost once the allocation sequence and the nature of the intervention were known, at least to those performing the intervention.
Incidentally, I vividly recall that the first RCT on pulmonary surfactant for the prevention of hyaline membrane disease in preterm infants failed to demonstrate evidence of the clinical effect—which is otherwise quite evident—because the study was “open” and unblinded. As a result, the nursing staff delivered “schizophrenically meticulous” care and airway cleaning for patients in the non-intervention arm.
Incidentally, so-called “Normal” or “Physiological” Saline Solution is neither physiological nor normal. It has an extremely low pH (around 4.5) and contains nearly 50% more chloride than human plasma. Thus, the use of large volumes of saline for resuscitation—especially in pediatrics—can lead to hyperchloremic acidosis.
It is certainly true that large volumes of NS leads to a transient hyperchloremic metabolic acidosis in babies and young children. So maybe it makes sense to hypothesize that using LR instead is better. But what is “better”? An example of where LR might be better than NS (and could prompt an RCT).
In this case, the key observation is that the NS-induced acidosis is mild, transient, and requires no treatment. However, in fact, it doesn’t matter in either the short or long term which fluid is used. And so, the beaten horse could be left alone to recover.
Dear JDM,
Very sharp observation. Clearly, the human kidney and the neuro-endocrine-metabolic system know more than the collective brains of all physicians.
This matter reminds me of the major debate that took place about 20 years ago, when the efficacy of resuscitation—specifically regarding mortality outcomes—was tested in patients with sepsis and capillary leak. The comparison of crystalloids versus colloids led to the conclusion that colloids actually increased mortality.
But also, my dear JDM, let’s not forget that the “invention” of normal saline—or “physiological serum”—as an emulation of plasma solvent, was never experimentally evaluated against more physiologically adjusted solutions tailored to the cause and type of fluid loss requiring resuscitation.
Hypovolemic shock due to hemorrhage is not the same as shock from cholera-induced diarrhea, or rotavirus-induced diarrhea, or cardiogenic shock, or neurogenic shock, and so on. That is why, in the bygone days “of barbaric nations,” we used to prepare crystalloids under laminar flow hoods, tailoring them to the specific etiology and mechanisms involved in our patients—an approach that, although observational rather than experimental, yielded enormous clinical benefits.
Alternate view. You are the CFO sitting with the CMO. The GPO you deal with sells NS at a discount to the LR. From a hospital-level POV, is there net harm or benefit from converting the system from one formulation to another? Some interventions are one-size-fits-all and have a positive ROI, while others may not (e.g., VTE prophylaxis for all strategy).
Can I go off on a tangent here? I was pondering a trial design where the arms are two different patient selection algorithms. Let's use nasal surgery for OSA as our scenario. Right now the patient selection algorithm is that an otolarygologist offers you a surgery. There is no filter. The surgery has a 15% success rate. So far this is not a hypothetical. This is literally what happens in the real world.
Now let's imagine a different patient selection algorithm. Sleep Medicine measures your overnight breathing with a pressure-sensitive cannula. If you breathe through your mouth all night, you are referred to otolaryngology for nasal surgery. Nasal-breathers are not referred because the surgery won't help. Lo and behold success rates are now (hypothetical, this would be the point of the study) way better, say 75%.
Is there some reason we can't implement this as an RCT where we measure the difference in successful surgeries between the current patient selection algorithm and my new and improved one? The arms are selection algorithms not treatments.