Reading a Dose-Response Figure Critically

A dose-response figure is a compact argument. It asserts that a measured signal varies with concentration in a specific and monotonic way, that the variation is larger than the noise around it, and that one number — an EC50, an IC50, a maximal effect — fairly summarizes the whole relationship. Those three claims fail independently of one another, and each failure leaves a visible trace in the figure if you know which feature carries it.

This guide is about reading such a figure rather than making one. It concerns only what a concentration-response experiment measures: how a defined signal in a defined assay changes as the concentration of a test article changes. Nothing about an organism follows from it. In order, the things worth checking are:

• What the reported n counts, and whether those units were independent
• Which statistic the error bars show, stated in the legend
• What was chosen as 100%, and whether its own uncertainty is carried
• Whether either axis is truncated, and where the vehicle condition is plotted
• Whether the data reach a top and a bottom plateau, or the model supplies them
• Whether the transition is resolved by more than two concentrations

Start with n, and with what n counts

The number in the legend means nothing until you know which unit was replicated. Lazic and colleagues argue that the relevant distinction is between biological units, experimental units and observational units, and that independent replication of the correct entity-intervention pair is what forms the basis of statistical inference; replicating the wrong one inflates the apparent sample size and the apparent evidence, producing false positives ^[1]. Their survey covered a narrow design — published animal experiments from 2011 to 2016 in which the intervention was applied to parents and effects examined in offspring — and found that only 22% of studies (95% CI 17%-29%) replicated the correct pair, 46% (95% CI 38%-53%) showed pseudoreplication, and 32% (95% CI 26%-39%) gave too little information to judge ^[1]. That is not a measurement of cell-culture practice, but the three-unit distinction the authors set out is the one to apply to an in vitro figure.

For cell work specifically, Lord and colleagues take the position that the sample size used for statistical tests should represent biological replicates, meaning independent measurements of the population made in separate experiments, and they provide figure designs that display both the cell-level variability and the experiment-to-experiment reproducibility at once ^[2]. A figure that shows only one of those two is showing you half the question.

The arithmetic consequence is large. Suppose three wells per concentration are run on each of three plates, all seeded from one thaw and dosed from one dilution series, and the legend reports n = 9. Hold the per-well standard deviation fixed at 12 signal units to isolate the effect of n alone. Drawn as a standard error with n = 9, the bar is 12 / √9 = 12 / 3 = 4.0 units. Drawn with the three genuinely independent runs, n = 3, it is 12 / √3 = 12 / 1.732 = 6.93 units. The bar you are looking at is 4.0 / 6.93 = 0.577 of the honest length — 42% shorter, where the denominator is the honest bar at 6.93, not the drawn one.

The error bar is three different pictures

Cumming, Fidler and Vaux point out that error bars may show confidence intervals, standard errors, standard deviations or other quantities, that these give quite different information, and that the figure legend therefore has to state which ^[3]. An unlabeled bar is not a weak claim; it is an uninterpretable one.

The substitution that matters most is the standard error in place of the standard deviation. Nagele's argument is that because the standard error of the mean is always smaller than the standard deviation, reporting it to describe a sample misleads the reader into underestimating the variability between individuals within that sample; auditing four anesthesia journals for 2001, he found this misuse in 23% of articles (198 of 860), ranging from 11.5% to 27.7% across the four titles ^[4]. Motulsky lists over-reliance on standard errors, which he describes as often misunderstood, among four mistakes investigators often make, alongside P-hacking and an overemphasis on P values rather than the actual size of the observed effect; his argument is that poor understanding of statistical concepts may be one reason among many that published findings fail to reproduce ^[5].

Several journals now legislate the point. The revised author instructions Michel, Murphy and Motulsky describe for three ASPET journals hold that variability should be described by standard deviation or interquartile range, that precision should be described by confidence intervals, that standard errors should not be used, and that figures should give as much granularity as possible, with scatter plots in place of bar graphs wherever feasible ^[6].

At n = 9 the standard error is the standard deviation divided by √9 = 3. Relabeling identical data from SD to SEM therefore shortens every bar by (SD − SD/3) / SD = 2/3, or 66.7%, with the SD bar as the denominator. No data changed. The picture of reproducibility changed completely.

Normalization moves the plateaus before you see them

Almost every published dose-response figure is normalized, and the choice of what counts as 100% is made before the curve is drawn. Vehicle control, untreated control, a reference compound, and the fitted top of the curve itself are four different denominators that produce four different figures from one dataset.

Consider a raw signal of 0.20 units at the top concentration against a vehicle control mean of 1.00. Percent of control is 0.20 / 1.00 = 20%, so inhibition is (1.00 − 0.20) / 1.00 = 80%, with the control as the denominator. Now let that control be estimated from three wells with a 15% coefficient of variation. The standard deviation of the control mean is 0.15 / √3 = 0.0866, about 8.7% of the control value. A plate whose control happens to read 1.10 gives 0.20 / 1.10 = 18.2% of control, or 81.8% inhibition; a plate reading 0.90 gives 0.20 / 0.90 = 22.2%, or 77.8% inhibition. The same raw measurement spans four percentage points of apparent inhibition, and the error bars drawn on the normalized points frequently do not carry the control's own uncertainty at all.

Normalizing instead to the fitted top of the curve is worse in a specific way: the algebra guarantees the top plateau lands at 100% whether or not the data ever reached it. That is not evidence of a plateau — it is a rescaling that erases the question. A figure that also shows a raw-signal panel lets you check; one that does not, does not.

The axes: a scale you read differently, and a break that hides the baseline

Concentration is conventionally plotted on a base-10 logarithmic axis, with concentrations spaced at half-log steps such as 1, 3, 10, 30 and 100 nM. The transform is a design choice, not a neutral display. Ciccione, Sablé-Meyer and Dehaene measured trend extrapolation from scatterplots in 521 participants and found linear extrapolation precise and largely unbiased but noisy exponential growth consistently underestimated, a bias they report was mitigated by participants' mathematical knowledge, by plotting the response on a logarithmic y-axis scale, and by showing a noiseless curve rather than a noisy data plot ^[7]. Their experiments concerned linear and exponential trends, not sigmoidal concentration-response curves, so the finding does not transfer directly; what it does establish is that axis scaling changes what a reader extrapolates from the same underlying data.

Truncation of the response axis is the more common distortion, and its effect is straightforward to quantify. A five-unit difference on an axis running 0 to 100 occupies 5 / 100 = 5% of the plot height. The same five units on an axis running 80 to 100 occupy 5 / 20 = 25%. The denominator is the axis span, and shortening it magnifies the apparent effect fivefold without touching a single data point. Truncation on the concentration axis does the mirror-image damage: dropping the lowest concentrations because they came out flat removes the very evidence that the bottom plateau exists.

Check also whether the zero-concentration or vehicle condition appears in the plot at all. It cannot be placed on a logarithmic axis, so it is normally handled with an axis break, an offset symbol or omission. If it is omitted, the baseline in the figure is a fitted parameter rather than a measurement, and the distinction is worth making explicitly rather than assuming.

A missing top plateau makes the EC50 an extrapolation

An EC50 is a parameter of an assumed model, not a reading taken off the data. Ritz and colleagues make this explicit in describing dose-response infrastructure: the analysis begins by specifying model assumptions about the dose-response relationship, and inference is then carried out on parameters derived from the fitted model ^[8]. If the highest concentration tested has not turned the corner, the top of that model is being inferred from data that never constrained it.

Take the simplest case, a Hill slope of 1, where the response is Emax × C / (EC50 + C). Rearranging, EC50 = C(1 − f) / f, where f is the fraction of Emax reached at concentration C. Suppose the highest concentration tested, C_top, gives 70% of the fitted maximum. Then EC50 = C_top × (1 − 0.70) / 0.70 = C_top × 0.30 / 0.70 = 0.429 × C_top. Now suppose the true maximum is 25% higher than the fitted one. The same measured response is then a fraction 0.70 / 1.25 = 0.56 of the true maximum, and EC50 = C_top × (1 − 0.56) / 0.56 = C_top × 0.44 / 0.56 = 0.786 × C_top. The potency estimate has moved by a factor of 0.786 / 0.429 = 1.83 — close to a doubling — and the two fits diverge most above the highest concentration tested, where the figure has no points to tell them apart. Whether the fit constrained the top plateau to a fixed value, and on what grounds, is a modeling decision that belongs in the methods.

The general hazard of reading a model outside the range where it was constrained is not confined to cell assays. Comparing extrapolation methods in a large animal bioassay of more than 40,000 animals that exhibited sub-linearity, Wheeler and Bailer found that approaches accounting for model uncertainty produced dose estimates closer to the observed risk than linear extrapolation from a point of departure ^[9]. That is a regulatory toxicology setting with its own conventions, so it does not license a claim about in vitro fits; it does illustrate that once you leave the observed range, the answer is a property of the model you chose.

A missing bottom plateau is the same problem upside down

If the lowest concentrations still show a response distinguishable from control, the bottom of the curve is extrapolated too, and any EC50 read against it inherits the error. Constraining the bottom to zero is a common fix, and it forces the very shape the figure is presented as demonstrating. A different signal is a bottom that never returns to the control value anywhere in the range, which may indicate an effect present at every concentration tested rather than a concentration-dependent one.

Steepness is a claim, and usually a prompt to check

The slope parameter is often reported and rarely interrogated. In a screen of 70,563 library molecules tested for detergent-sensitive inhibition at seven or more concentrations each, Feng and colleagues identified 1,274 inhibitors of which 1,204 were unambiguously detergent-sensitive, concluded that 95% of the actives in that screen were aggregate-based, and reported that aggregate-based inhibition is correlated with steep dose-response curves, although not absolutely ^[10]. That was one enzyme-based campaign against one library, so the prevalence figure describes that screen. The methodological point survives: a slope substantially steeper than one is a reason to run a control for a non-specific mechanism, not a verdict on its own.

There is also a purely geometric caution. With half-log spacing, each interval spans about 0.5 log units. If the entire transition from baseline to maximum happens between two adjacent concentrations, the slope has not been estimated — it has only been bounded by the spacing of the points, and any steeper value would fit the same data equally well.

Was the assay window large enough to carry a curve?

A curve fitted across a small separation between the two control conditions is a curve fitted mostly to noise. Zhang, Chung and Oldenburg defined a screening window coefficient, the Z-factor, that is reflective of both the assay signal dynamic range and the data variation associated with the signal measurements, and proposed it as a dimensionless statistic for comparing assay quality ^[11]. The form in routine use subtracts three combined standard deviations from the separation of the two control means and divides by that separation.

With control means of 1.00 and 0.10 and a standard deviation of 0.05 on each, the coefficient is 1 − 3 × (0.05 + 0.05) / |1.00 − 0.10| = 1 − 0.30 / 0.90 = 1 − 0.333 = 0.667. The denominator is the separation between the control means, 0.90, not either mean on its own. Double both standard deviations to 0.10 and the same separation gives 1 − 3 × 0.20 / 0.90 = 1 − 0.667 = 0.333. Nothing about the compound changed; the assay's capacity to support any curve at all halved by this measure.

What the figure cannot tell you

Several questions are structurally outside the reach of a plotted curve. The concentration on the axis is the nominal concentration prepared; whether the concentration at the target matched it depends on adsorption to labware, degradation over the incubation, solubility at the top of the range and binding to components of the medium, none of which the figure records. Whether this was the only curve run, or the one that worked, is not visible either. Whether the model and the outlier rules were fixed before the data were seen is exactly the granularity the ASPET guidelines ask authors to state, distinguishing preplanned hypothesis-testing work from exploratory work and requiring that any exclusion of data points or entire experiments be declared along with when the rules for it were defined ^[6]. The guidance issued by the British Journal of Pharmacology was likewise written to serve as an explicit rubric for peer review ^[12], which tells you these are checkable items rather than matters of taste.

Two EC50 values from two figures are comparable only if the assay, readout, cell background, incubation time and normalization match, and usually they do not. An honest reading ends with a list of what remains unknown, and that list is longer than the curve makes it look.