Alternative to the statistical mass confusion of testing for “no effect”

In a highly interconnected network like a living organism, the proposition that one component is perfectly independent from another component is trivially false. By virtue of being part of the same organism, all molecular pathways and cells can be assumed to be either directly or indirectly connected. Detecting the connection might require extremely sensitive equipment and many samples, but the biological question is never “Is there a connection?” The meaningful question is always “How strong is the connection?”

The second problem with the no-effect hypothesis is that all experiments can be assumed to have some sampling bias (McShane et al., 2019). For instance, it is now recognized that circadian rhythms have detectable effects on most cellular processes. How much of the published biological literature has strong controls for time of day? Even if we could perfectly control the biology, there is no perfectly bias-free biology measuring device. Pointing out that no experiment is perfect is only necessary because no-effect tests are asking about an exact point value. Even if the true biological effect size were zero, we should not expect to record zero experimental effect.

Finally, and most fundamentally, the statistical models underpinning NHSTs are mathematical simplifications of biological processes. The assumptions underlying these models are, at best, approximations of experimental conditions. Using these models to ask how much bigger the observed effect size is than the range of effects predicted for a given hypothesis is a great way to make sense of data (Box 1). However, there should be no expectation that any statistical model can perfectly predict potential experimental results (Amrhein et al., 2019).

The upshot of these three sources of guaranteed deviations from the null hypothesis is that P values for all no-effect tests will become infinitesimally small as sample sizes approach infinity. Imagine a dial that increases the sample size in all publications. As we turn the dial up, asterisks begin appearing over every plot and bar graph. We can keep turning the knob until each bar has a string of asterisks that runs off the page, and the conclusion of every test is that the result was extremely statistically significant. The biology has not changed. The questions have not changed. But increasing the sample size has guaranteed the same answer to every question.

The quantitative claim being made by a test for no effect is not scientifically meaningful. So why have we spent decades feeling like P values tell us something useful about biology?

For most 20th century cell biologists, data acquisition was slow, equipment was noisy, and sample sizes were small (n = 3–100). With these sample sizes, a small effect (∼10% of the SD) should produce “P < 0.05” in about 5–10% of tests for no effect. Large effects (∼80% of SD) would produce P < 0.05 in about 12–99% of experiments. The difficulty of data collection also meant that there was a strong incentive to avoid testing for biological relationships that were unlikely to be important (low prior probabilities). If a research program mostly tests biological relationships with a high prior probability of being important and collects small sample sizes, then a claim based on consistently small P values is likely to reflect a large underlying biological effect.

Using low-sensitivity tests for no effect as a proxy for estimating effect size is not a quantitative or efficient use of data, but it is, at least, tethered to reality. The situation changes when automation allows a massive amount of high-quality data to be acquired and analyzed with minimum human supervision. Automation cuts the weak connection between no-effect testing and reality in three ways:

• (1)

  Giant samples of trivial effects produce arbitrarily small P values. In the case of the small effect size above (10% of SD), ∼95% of experiments with a sample size of 2,500 would produce P <0.05.

• (2)

  The ease of testing many parameters eliminates the incentive to only test relationships that are likely to be important (high prior probability). As a result, most of our low P value results are likely to reflect trivial true positives. If follow-up experiments also rely on no-effect testing, researchers will follow a random walk (Mlodinow, 2009) from one biologically insignificant discovery to the next.

• (3)

  Automated analysis can generate many highly derived measures from the same data. Interpreting derived measures with tests for no effect makes it possible to claim a result is significant without anyone understanding what is being measured.

The reason testing for no effect distorts scientific reasoning is that it allows us to analyze measurements without thinking about effect size. Effect size is usually measured as the difference in means between two groups, but effect size can refer to any quantifiable difference, relationship, or change. Effect size matters because (1) experimental measurements are about effect size. (2) Effect size determines the importance of interactions. (3) Models of cells run on effect sizes. (4) Effect sizes—unlike P values—can be compared between experiments. (5) Consideration of effect size—unlike P values—determines whether a field of inquiry is quantitative. Currently, it is difficult to argue that cell biology is operating as a quantitative science.

Prior to performing an experiment, we should be able to explain how a measure maps onto biological meaning. Ideally, we will have at least one real-world example of a small effect and one real-world example of an important effect. Imagine we have a mutant mouse model of a disease in which the number of mitochondria in each cell is reduced to half. We want to use this mouse model to test the efficacy of a drug treatment. The data we collect are the number of mitochondria, but we do not necessarily care whether a cell has 20 or 21 mitochondria. We care about recovery. We, therefore, define a scale with mutant mitochondria number at one end (0%) and healthy mitochondria number at the other end $(% Recovery=Treatment−MutantHealthy−Mutant×100$⁠, Fig. 1 A). When we talk about our results, we present both the raw mitochondria number and the percent recovery.

How should we analyze the effects of a treatment tested on these mutant mice? Our worst option is to put off thinking about statistics until we have the data. We then perform the default t test for no effect. If the null hypothesis is rejected, we conclude that the treatment was effective. We report our results with a series of bar graphs and asterisks (Fig. 1, A and B). By treating a weak version of an NHST as a rigorous test of a research hypothesis, we violate principles of science, statistics, and common sense. Critically, the P value fails to distinguish between a trivial effect, an ambiguous result, and a complete cure (Fig. 1, A and B). A reader who wants to determine if the treatment effect is biologically meaningful will have to decode the y axis of the plot, compare it to the SE bars, then look up the sample size, and then reread the text to try to determine what an important effect size might be.

NHSTs, weak or rigorous, are not a good way to understand biology. But, for the sake of argument, what would it take for a P value to mean roughly what we would like it to mean? In this case, we need a quantitative definition of “ineffective treatment.” Before the experiment, we might find that previous treatments achieved 5–10% recovery, a 30% recovery is required for a health improvement, and there is ∼5% batch-to-batch variation in mitochondria counts. We could argue 20% recovery is, therefore, a reasonable cutoff for identifying promising treatments. We would then need to define a P value threshold that reflects the relative costs of following up on a false positive result or neglecting to follow up on a false negative (Neyman and Pearson, 1933). We would analyze the variance of recovery measures to determine what kind of statistical model (parametric, nonparametric, or nonlinear) is appropriate. We should also perform a power analysis and preregister the experiment (Nosek et al., 2018). Finally, we would perform the experiment and perform an NHST for the hypothesis that the experimental effect was 20% or less. Given the totality of experimental design, data and analysis, a rejection of the null hypothesis would support the conclusion, “our best bet is to find out more about the treatment.”

Is that really the best we can do? If we understand the biological meaning of potential experimental effects and we have designed a rigorous experiment for measuring those effects, why not just ask, “What was the effect?”

Reading data to understand effect size starts with staring at scatterplots (Fig. 1 C). Are the data points from each group clearly clustered around one point, or are there multiple sub-clusters, extreme outliers, or a general lack of consensus? Are the data points spread across a biologically reasonable range of effects, or are most of the data points bunched together near some detection threshold? If we plot rich experimental information, such as which data points came from which experimental subject (see SuperPlots [Lord et al., 2020]), how much of our variance is coming from differences between measures, between individuals, or between batches? Finally, how big are the differences between groups compared with the differences within groups and the absolute value of our measures? There are worthwhile mathematical approaches to answering all these questions, but careful consideration of the scatterplot is a necessary sanity check and is often sufficient for making sense of a set of measures.

For thinking about the biology, reporting results, and making claims, we also want to calculate a conservative estimate of effect size. Effect size and precision are often summarized as a point estimate and a SE (e.g., mean = 5.0 ± 0.2 SE). While these are useful statistics, they are not quite the quantification we need for evaluating the biological meaning of data. First, when we see a point value (mean, median, and correlation coefficient), it is difficult for our brains not to register the point value as more “biologically true” than a range of nearby values. Second, making good use of the SE requires math, consideration of experimental design, and consideration of data characteristics.

When we report measurements, our goal should be to transparently report the range of effect sizes that make the most sense given the available data. This range is called an interval estimate. If we estimate that the recovery level of the treatment group was 84–100%, we can make a statistically and biologically meaningful claim that the treated group looks more like the healthy mice than the disease model mice (Fig. 1 C). If our interval is limited to trivial effect sizes (0–13%), we can start looking for alternative treatments. If our effect size estimation includes a wide range of potential effects (5–107%), then we need to perform additional experiments or analyses to determine if the range of results is due to measurement error, biological variation, or treatment variation.

Types of interval estimates include confidence intervals (frequentist statistic) (Neyman, 1937), credible intervals (Bayesian statistic) (Morey et al., 2016), prediction intervals (forecasting future results) (Billheimer, 2019), tolerance intervals (defined by proportion of population) (Owen, 1964), and likelihood intervals (likelihood function) (Hudson, 1971). It is also possible to report a two-sided (50–103%) or one-sided interval (>60%). Choosing the best method for estimating an effect size interval requires careful consideration of how much is already known about the system and the goals of the research program (Hahn and Meeker, 1991).

In the succeeding discussion, I will focus almost exclusively on two-sided confidence intervals, and I will recommend that confidence intervals be adopted as the next default statistic in cell biology. This recommendation is not because confidence intervals are ideal for every cell biology experiment. The recommendation reflects the current culture of cell biology and how we do experiments. Key to this recommendation is the fact that our field can make the profound switch to effect-size–based science simply by reporting the confidence intervals generated by the same statistical models we previously used to perform NHSTs.

NHST for no effect became ubiquitous because there is a genuine need for a simple and universally understood quantification of what we see when we look at scatterplots. Reporting P values was a reasonable idea, but overuse, misuse, and misinterpretations proved disastrous. Compared with P values, confidence intervals are an efficient and transparent approach to reporting both effect size and precision (Box 2). Confidence intervals also respond in an intuitive way to how much information is available. More data means, on average, greater precision of effect size estimation. As a default statistic, confidence intervals have a huge advantage in that they provide useful information across wide ranges of experimental designs, including preliminary experiments, rigorous descriptive studies, qualitative hypothesis testing, and quantitative hypothesis testing. Given these benefits, confidence intervals are the most commonly proposed alternative to P values (Cohen, 1994; Thompson, 2014; Neyman, 1937; Nakagawa and Cuthill, 2007).

Treating confidence intervals as cell biology’s default statistic (technically our default inferential construct) does not mean that all data must be analyzed with a confidence interval. Making it our default statistic means that the confidence interval is what we would use when we collect measurements and do not have a better idea of how to summarize our data. We would make sure that every student is comfortable calculating and interpreting a confidence interval. When readers, reviewers, and editors evaluate a publication, the confidence interval would define the minimum level of statistical sophistication and meaning that they should expect from the analysis of sample measurements.

There are a variety of parametric and nonparametric methods for calculating a 95% confidence interval (Resource Box 2), but the goal is the same. The nominal performance of a 95% confidence interval means that, in an infinite number of ideal experiments, the real test parameter would fall within the bounds of the interval in 95% of trials (Fig. 2, A and B). How close the actual interval performance gets to the nominal performance depends on how well the assumptions of the model match the conditions of the experiment (Miao and Chiou, 2008; Puth et al., 2015). Critically, the “95%” value is not the probability that an individual interval includes the true population value. A single interval is either right or wrong.

How, then, should we translate a CI95% into a belief about something we are measuring? If the statistical model is appropriate to the experiment and the experiment is well constructed, it is reasonable for us to think of the biological effect as existing within the bounds of the 95% confidence interval. We also need to understand that we will be wrong more than 5% of the time. Accepting that at least 5% of cell biology experiments will produce misleading results should not rock our view of the field (Border et al., 2019; Errington et al., 2021). Our actual confidence in our understanding of a system should reflect the accumulation of consistent evidence from independent experiments that, ideally, use independent experimental approaches. In some cases, this accumulation of evidence can be quantified (Santos et al., 2024). Most of the time, we will have to rely on our own critical evaluation of the literature (Nosek and Errington, 2020).

One advantage to using confidence intervals is that they make sense even when experiments are preliminary or exploratory. Calculating a confidence interval does not require a hypothesis or prior information about effect size or variance size. Calculating a confidence interval does require a model of variance and a minimum number of samples. However, using a t-distribution (t test) to calculate a confidence interval from 10 data points that look Gaussian will usually get us in the right ballpark (Fig. 2, A–D). Note that a small sample size limits a confidence interval’s information about both effect size and precision. At very small sample sizes (<8), interval widths for samplings of the same underlying population vary wildly (dashed curves, Fig. 2 C). At these sample sizes, reporting a mean and an a priori precision (Trafimow, 2017) (Fig. 2 C, red line, see below) might be a more useful way to discuss results.

Confidence intervals are also a useful way to summarize data in studies that are not preliminary or exploratory. If we want to know how a mutation in protein-A relates to the rate of cell division, we can measure the rate of cell division in animals with and without the mutation. We can choose a sample size that reflects the effect sizes we are interested in and the known variance of the rates. We can then calculate a confidence interval for how much the mutation changed the rate of cell division (CI95[55%, 59%]). That interval can help us understand the clinical impacts of the mutation, build models of the regulation of cell division, or compare the effects of protein-A to the effects of other possible regulators of cell division.

A confidence interval can also be used to compare data to a hypothesis. Imagine we have enough information to formulate a biological model of the behavior of protein-A. This model predicts that the planned mutation would result in a 90% increase in the rate of cell division. The 90% increase is our quantitative hypothesis. An experimental result of “CI95 [55%, 59%]” looks like evidence against our model of protein-A. How should we evaluate the difference between our hypothesis and our confidence interval? Values outside the bounds of a standard 95% can be thought of as null hypotheses that would have been rejected by a two-sided t test with a P value threshold of 0.05. However, if we treat the bounds of a confidence interval as binary thresholds for accepting or rejecting hypotheses, we are subject to the same distortions and confusion that come from using P value thresholds to dichotomize data.

Confidence intervals are useful for evaluating hypotheses because they allow us to independently judge the distance between a quantitative hypothesis and the interval and the width of the interval on a scale that has a biological interpretation. A narrow confidence interval that is far from the hypothesis could argue that there is something important going on that is not adequately described by our model of protein-A. A narrow confidence interval that includes the test hypothesis could support our prior understanding of protein-A. A very wide confidence interval could mean that our experiment is not precise enough to affect our beliefs about protein-A. In contrast to significance testing, a narrow interval that is very close to our hypothesis, without including it, could also provide support for our existing model of protein-A.

Our interpretation depends on being able to assign biological meaning to “close,” “far,” “narrow,” and “wide”. How do we decide if CI95 (91.0%, 91.1%) is close to 90%? Assume the following pre-experiment information: (1) Mutating other relevant proteins changes cell division rate by 0–1,000%. (2) When labs try to replicate these types of measures, there is 1–20% error between experiments. (3) There are four equally likely biological models of protein-A that predict effect sizes of 5%, 90%, 200%, and 500%, respectively. Given that information, a difference of 1.0–1.1% between the hypothesis and the estimated effect size is remarkably small and supports the 90% model.

In an ideal statistical analysis, prior information about competing biological models, biological variation, and measurement error would be used to build statistical models that provide more nuanced information than a standard confidence interval (see below). However, as an easy default statistical analysis, confidence intervals that are interpreted relative to expected effect sizes, biological variation, and measurement error provide quantitative answers to quantitative questions. If you do not have a quantitative question, but you want to challenge an existing biological model by testing a quantitative prediction of that model, confidence intervals can also serve that purpose. How often do cell biologists need statistical analysis to tell them “true” or “false” instead of “how much?”

For many years, cell biologists were told that good science is hypothesis-driven science and that hypothesis-driven science means performing manipulation experiments that either reject or fail to reject a mechanistic hypothesis. Studies that did not fit this formula were often dismissed as “merely descriptive.” Analyzing every experiment with an NHST to reject a no-effect strawman was treated as consistent with the Popperian program of hypothesis falsification.

It is difficult to summarize all the problems with the above view of science. First, a research hypothesis is not the same thing as a statistical hypothesis. Second, rejecting an impossible hypothesis is not falsification science. Third, falsification science is not how cell biology works. To the philosopher Karl Popper, the question of where theories came from was “irrelevant to the logical analysis of scientific knowledge”(Popper, 1959). To cell biologists, theories come from centuries of hard work building instruments that can observe things that could not be observed before and then systematically doing the observing. Rigorous non-hypothesis–testing studies are the bulk of the research that needs to be funded and published if we want our field to generate theories that are worth testing.

Cell biology has produced an incredibly successful, unified, and coherent model of how cells evolve, develop, behave, interact, build tissues, and fall apart. When we identify important gaps in this model, we map and manipulate the phenomena of interest until the gap is filled. If the next big gap in knowledge is the sequence of the human genome, and we can map the human genome, then no hypothesis middleman needs to get involved. This logic includes experimental manipulations. If there is a good reason to care about how much a mutation increases cell division, and we can measure that increase, framing our analysis as a hypothesis test is misleading and unnecessary.

The difference between a P value and a confidence interval is in which part of a statistical prediction is binarized. You can report a P value, the precise fraction of a probability distribution defined by two magnitudes (null hypothesis and observed result). Alternatively, you can report a confidence interval, two magnitudes corresponding to a defined fraction of a probability distribution. In favor of reporting confidence intervals is the fact that there is no clear way to think about what a precise fraction of a hypothetical probability distribution means for our understanding of the world. The widespread confusion about P values and probability reflects not just a lack of statistical sophistication but also a genuine epistemological conundrum. In contrast, the values reported in a confidence interval are numbers with clear biological interpretations.

It is possible to visualize the relationships between effect sizes and P values without thresholding them. A compatibility curve is a two-dimensional plot of the P values (y axis) that would be obtained for a range of plausible hypotheses (x axis) given the observed data and a statistical model (Amrhein and Greenland, 2022; Berner and Amrhein, 2022; Poole, 1987) (Fig. 3). The example shows the compatibility curves generated by two simulated experiments (n = 20) that estimate a population mean using t-distributions (a bunch of t tests). The two points where the compatibility map intersects P = 0.05 are equivalent to the bounds of the 95% confidence interval. Note that the peak of each compatibility curve (P = 1) is simply the mean of the experimental sample. There is no statistical magic that suggests that these peaks are “probably” the true mean. Reporting the results of a statistical model with a compatibility curve is especially useful for non-normal distributions that are not readily summarized by confidence intervals.

The close relationship between confidence intervals and P values means that confidence intervals are subject to many of the same limits and misinterpretations as P values (Trafimow et al., 2024; Morey et al., 2016). If confidence intervals become the default summary statistic in cell biology, we can expect to see similar overinterpretations of what confidence intervals can tell us about our data (Greenland et al., 2016). We can also expect effect sizes to be systematically inflated by measurement bias (Vul et al., 2009; Fiedler, 2011), publication bias (Yang et al., 2023), and the winner’s curse (Button et al., 2013; Ioannidis, 2008).

One form of measurement bias warrants special attention because it often results from an attempt to objectively analyze large and complicated data sets (images and omics). A researcher will perform an experiment with thousands of potentially interesting variables (voxels, RNAs, genes, or cells). They use a criterion such as a P value for identifying which variables were affected by some manipulation. They then calculate an effect size for the identified variables. The problem is that the variance that influences selection is not independent from the variance that influences effect size estimation. Ironically, the more conservative the selection criterion (P < 0.00001), the more the average reported effect size will be inflated (Ioannidis, 2008). The solutions include defining an independent criterion for selection (Fiedler, 2011) or performing an adjustment to the effect size estimate that takes the selection criterion into account (Holland et al., 2016).

While confidence intervals are a good starting point for cell biology, they do not make full use of the available data. As a measure of precision, confidence intervals lump together different classes of error (measurement precision, variation within the population, and sampling error) that could be calculated and reported separately (Trafimow, 2018). If the data exist for positing prior probabilities, then a Bayesian credibility interval will leverage more of the available information than a confidence interval (Morey et al., 2016). More generally, statisticians point out that statistical techniques are constantly being improved and that it is wrongheaded to expect one type of analysis to be optimal, or even appropriate, for most experiments (Wasserstein and Lazar, 2016; Amrhein and Greenland, 2018; Cumming and Calin-Jageman, 2016).

Given the limitations of confidence intervals, why is it worth pushing tens of thousands of cell biologists to replace “P value” with “CI95?” Currently, cell biologists can publish sample measurements without discussing effect size. Asking cell biologists to stop what they are doing and read an effect-size–centric statistics textbook (Cumming and Calin-Jageman, 2016) before designing their next experiment is not realistic or polite. Switching to confidence intervals, in contrast, provides useful information about the effect size, requires no change in experimental design, requires no change in statistical model, and makes P values superfluous. Confidence intervals are a remarkably low-cost first step toward overturning a dysfunctional status quo.

As humans and scientists, we theorize that there is a universe that we can collect information about through our experiences. From these experiences, we build mental models of bits of the universe (inference) that make predictions about future experiences. If the universe works like X, we can expect Y to happen. A statistical model is an abstracted version of a cognitive model whose behavior can be described mathematically. The brilliance of these statistical models is that they can be applied by many different observers to many different processes and that their predictions are repeatable and quantifiable. However, the extent to which the model tells you something useful about the universe depends on how well each assumption of the model corresponds to the behavior of the patch of the universe you are investigating.

Our statistical claims are philosophically valid when we treat statistical inference as thought experiments instead of facts about the world (Amrhein et al., 2019). However, a useful cognitive model requires that we eventually summarize evidence as something like, “I’m pretty sure most cell bodies are about 10 μm in diameter.” The numbers from statistical analysis can help us refine “pretty sure,” “most,” and “about,” but the relationship is not one-to-one. That is, the probability distributions predicted by a statistical model exist within the bounds of our uncertainties about both the appropriateness of the model and the reliability of the experimental controls.

One path out of these philosophical ambiguities is to perform our analysis of precision before conducting the experiment. Trafimow and colleagues argue for combining an a priori procedure for calculating precision with a gain-of-probability diagram to analyze results (Trafimow et al., 2024; Trafimow, 2017). The simplest version of an a priori procedure is to determine the sample size needed to estimate a mean. We first define our target precision as some number of SDs between a true mean and a measured mean (±0.5 SD). We then define our target probability that a measured mean would fall within this precision range (for 95%, z-score = 1.96). Finally, we calculate the minimum sample size that would satisfy our two goals $(n=(1.960.5)2=16)$⁠.

A second path out of the philosophical confusion is for more cell biologists to perform statistical analysis by programming Monte Carlo simulations (Buckland, 1984) (Resource Box 1). Programming these simulations allows a researcher who is unfamiliar with the fine points of statistical theory to ask their question in the most straightforward way possible: “If the system worked like this and I ran my experiment 100,000 times, what would I expect to see?” The act of writing the simulation forces the researcher to think of the statistical model as a system of “if, then” statements that may or may not match reality. It can also push the researcher to question whether the hypothesis they are programming is really a plausible way for the system to work.

The criterion of “biologically meaningful effect size” is a much higher bar than “statistically significant.” Under this criterion, many fewer studies can be expected to claim important experimental effects. This aspect of increased statistical rigor does not necessarily mean fewer papers will be published. An unbiased literature requires publishing both “positive” and “negative” results. Focusing our analysis on effect size does mean that we will have to accept the reality that most experimental results are ambiguous and incremental. The implicit and, sometimes, explicit interpretation of P values is that the result of every experiment is either “effect” or no effect. When we take interval estimates seriously, we will often have to conclude that we do not have enough data to understand what is going on.

Discussing confidence intervals will also require more work than discussing tests for no effect. It is convenient for everyone to agree that there is a statistic (P value) that tells you that something important happened even when it is not clear what is being measured. In the absence of this fiction, our claims will require more explanation about how our measures relate to the biology and how the observed effect sizes relate to our question.

Arguing that we should produce a more detail-oriented literature filled with ambiguous and negligible effects is not the most appealing pitch for changing the way cell biology quantifies data. What we could gain is a literature in which biological claims reflect meaningful quantification, a literature from which we can judge the replicability of experiments, and a literature from which we can build better models of how cells work.

Imagine again the dial that increases sample size in all publications. When we were testing for no effect, increasing sample size eventually drove every experiment to reject the null hypothesis. What happens when publications, instead, base their claims on confidence intervals? As the sample size approaches infinity, the confidence intervals shrink to point values that are the actual population value. When effect size estimation is the foundation of our analysis, more data lead to more understanding.

The MATLAB (MathWorks) code used to generate figures and that can be used to experiment with different types of distributions is available at https://github.com/MorganLabShare/betterThanChance.

Thanks to Hrvoje Šikić, Tim Holy, Phil Williams, Daniel Kerschensteiner, and Julie Hodges for reading the manuscript and providing feedback.

This work was supported by an unrestricted grant to the Department of Ophthalmology and Visual Sciences from Research to Prevent Blindness, by a Research to Prevent Blindness Career Development Award, and by the NIH (EY029313).

Author contributions: J.L. Morgan: conceptualization, data curation, formal analysis, funding acquisition, investigation, methodology, project administration, resources, software, supervision, validation, visualization, and writing—original draft, review, and editing.