I like to
point to Keith Beven's (1987) conference paper, titled ‘Towards a new paradigm
in hydrology’, as a place for new hydrologists to start to develop an
understanding of uncertainty in the hydrological sciences[1].
In that paper Keith argued that “little to no success” had been made against
the fundamental problem of developing theories about how small-scale
complexities lead to large-scale behavior in hydrological systems[2].
The paper
discussed what hydrologists might do about this situation, and in the last two
paragraphs Keith made two predictions:
·
First, that hydrology of the future
will require a theoretical framework that is inherently stochastic to deal with
the “value of imperfect observations and qualitative knowledge in reducing
predictive uncertainty.”
·
Second, that hydrologists would not
actually develop this type of theoretical framework, but instead would
capitalize on the (then) emerging power of desktop computing to approximate
uncertainty; leading to results that “may not be pretty,” but which are “realistic
in reflecting both our understanding and lack of knowledge of hydrological
systems.”
Of
course, both of his predictions were essentially correct. In 2007 Jeff
McDonnell wrote “to make continued progress in watershed hydrology … we need
to … explore the set of organizing principles that might underlie heterogeneity
and complexity” (McDonnell et al., 2007). Jeff went on to describe
several possibilities for ‘moving beyond’ heterogeneity and process complexity,
but the point is nevertheless clear: the problem remains unsolved. Similarly,
Keith wrote last year that “our perceptual model of uncertainty is now much
more sophisticated … but this has not resulted in analogous progress in
uncertainty quantification” (Beven, 2016).
The
situation in hydrology right now is that we understand that macro-scale
behaviors of watersheds are governed by small-scale heterogeneities, but we
don’t have a theory about how this works, and we don’t have any fundamental
theory that allows us to (reliably) quantify predictive uncertainties related
to these processes.
Instead,
what we have are ad hoc strategies for obtaining numbers that seem like they
might be related with uncertainty. One example of this is the recent
proliferation of multi-parameterization modeling systems that allow the user to
choose between a variety of options for different flux parameterizations. An
example is the Structure for Unifying Multiple Modeling Alternatives; Clark et
al. (2015) wrote that “[SUMMA] provides capabilities to evaluate different
representations of spatial heterogeneity and different flux parameterizations,
and therefore tackle the fundamental modeling challenge of simulating the
fluxes of water and energy over a hierarchy of spatial scales.” It’s
unclear why predicting with a variety of different parameterizations of
scale-dependent processes allows us to ‘tackle’ scale-related challenges: we
still lack a fundamental theory of hydrologic scaling, and making predictions
with several different parameterizations is not in any way reflective of the
actual nature of our lack of knowledge about the principles and behavior of
hydrologic systems.
Other
methods that we often use for uncertainty quantification suffer from similar
problems. Bayesian methods allow us to do precisely one thing: inter-compare or
average several different competing models. Bayesian methods, and indeed any
methods for model inter-comparison or model averaging, are fundamentally
incapable of helping us to understand the difference between our family of models
(i.e., those models that are assigned finite probability by the prior)
and the real system. Gelman & Shalizi (2013) give a philosophical treatment
of this problem that is worth reading.
It has
been suggested that we might use empirical methods to develop probability
distributions over different components of predictive imprecision (e.g.,
Montanari and Koutsoyiannis, 2012), but this type of approach assumes
stationarity not only in those aspects of the hydrological system that are
captured by the model, but also stationarity in the relationship between model error and
those parts of the hydrological system that are not captured by the
model.
The point
is that uncertainty is tautologically inestimable, and so it is really no
surprise that Keith’s second prediction came true – there was never any real
possibility to develop a rigorous theoretical basis for understanding
uncertainty, scale-dependent or otherwise. More than that, the methods that we
have come up with to approximate uncertainty don’t actually do that at all – at
least not in any way that is fundamentally or theoretically reliable. I
propose the following challenge: provide a theorem that proves a bounded,
asymptotic, or even consistent relationship between any quantitative estimator
and real-world uncertainty under evaluable assumptions. I offer the
standard wager for scientific controversy[3]:
a bottle of Yamazaki 12 year, or comparable.
Until we
have such a theorem, I propose that it is not useful to talk about uncertainty
quantification – approximate or otherwise, – because none of our estimators are
related to real uncertainty in any systematic way.
Instead,
I predict a new paradigm change in hydrology. I suspect that within the next 30
years, the conversation in hydrology will be about information rather than
uncertainty. The reason for this is that while it is impossible to estimate
uncertainty (even approximately), it is possible to obtain at least bounded
estimates of information measures (Nearing and Gupta, 2017). The main project
of science seems to be about comparing the information contained in observation
data with the information provided by a hypothesis-driven model. Similarly, the
problem of scaling under heterogeneity seems to be fundamentally about
cross-scale information transfers, rather than about uncertainty. Given recent
work in basic physics (e.g., Cao et al., 2017), I suspect that it will
not take three more decades for us to discover real scaling theories under this
type of perspective.
Of
course, we will always want to know the reliability of our model predictions,
and for this reason the concept of uncertainty will never go away completely. I
propose, however, that the tractable and meaningful challenge is to understand
the actual predictive precision implied by our hydrological theory and
hypotheses. At present, we do not do this. Current practice is to build
models that are over-precise, and then append ‘uncertainty’ distributions to
their predictions. This method of dealing with a lack of complete knowledge
stems fundamentally from our Newtonian heritage. Essentially all process-based
hydrological models are expressed as PDEs, which must admit solution in order
to make a prediction.
There are
two problems with building dynamical models as PDEs. First, such models make ontological
predictions (predictions about what will happen), whereas what we actually want
are epistemological predictions (predictions about what we can know
about what will happen). The uncertainty probabilities that we append to our
models are the latter, and they are what we actually need for both hypothesis
testing and decision support. But these probabilities are not the product of
actually solving our model equations. Even if our model is a stochastic PDE,
the random walk component is simply an ad hoc appendage on the drift function.
Sampling model inputs or different model structures does not actually tell us
anything about our lack of knowledge associated with any of those model
structures. Models built as PDEs simply do not solve for anything that
represents what we can know from our physical theory and hypotheses.
The
second problem is that a PDE only provides a prediction if it can be solved.
This requires that we prescribe values (or distributions) over all parameters
contained in our hypothetical parameterizations, some of which are impossible
to measure and otherwise difficult to estimate. It would be exciting to have a
method for constructing models that allows us to assign values to only those
parameters that we feel we actually have some information about.
But there
is, in principle (although I have no example of such), a way to build this type
of model. Instead of expressing conservation principles using differential
equations, we could express them as symmetry constraints on probability
distributions. To do this, we might specify a Bayesian network such that each
node is a random variable representing a particular scale-dependent quantity at
a particular time and location within the modeled system; conservation laws
could then be used to effectively rule out large portions of the joint space of
values over these random variables. By imposing conservation laws and other physical principles as constraints on joint probability distributions, our models would fundamentally solve
for what we can know about the future or unobserved behavior of a dynamical
system conditional on whatever information (theories, hypotheses, data) are
used to build the model. In principle, anything that we do know, or wish to
hypothesize, could be imposed as a constraint on the joint distribution over a family of random variables representing different aspects of system behavior.
Although
such a strategy would not allow us to measure epistemic uncertainty
(uncertainty is always and still inestimable), at least it would allow us to
know what information we actually have about the behavior of hydrologic
systems. This would be a very different way of approaching model building than appending uncertainty distributions to PDE solutions, and would allow us to
actually quantify the information content of our scientific hypotheses and
models.
So
perhaps my predictions about paradigm change will not come to pass. I am, after
all, essentially arguing against two of the most fundamental concepts in our
science: that we should not use Bayesian methods to evaluate models, and
that we should not use differential equations to build models. I do
suspect that I am right about both of these things, in the sense that our
science (indeed, any science of complex systems) would accelerate by abandoning
these ideas in favor of information-centric philosophies and methods, but perhaps it will take longer than 30 years to demonstrate that
such a substantial change is necessary.
------
Beven, K. 'Towards
a new paradigm in hydrology'. Water for the Future: Hydrology in
Perspective. , Rome, Italy: IAHS Publication.
Beven, K. J. (2016)
'Facets of uncertainty: Epistemic error, non-stationarity, likelihood,
hypothesis testing, and communication', Hydrological Sciences Journal,
(9), pp. 1652-1665.
Cao, C., Carroll,
S. M. and Michalakis, S. (2017) 'Space from Hilbert space: Recovering geometry
from bulk entanglement', Physical Review D, 95(2), pp. 024031.
Clark, M. P.,
Nijssen, B., Lundquist, J. D., Kavetski, D., Rupp, D. E., Woods, R. A., Freer,
J. E., Gutmann, E. D., Wood, A. W. and Gochis, D. J. (2015) 'A unified approach
for process‐based hydrologic modeling: 2. Model implementation and case
studies', Water Resources Research, 51(4), pp. 2515-2542.
Dooge, J. C. I.
(1986) 'Looking for hydrologic laws', Water Resources Research, 22(9S),
pp. 46S-58S.
Gelman, A. and
Shalizi, C. R. (2013) 'Philosophy and the practice of Bayesian statistics', British
Journal of Mathematical and Statistical Psychology, 66(1), pp. 8-38.
McDonnell, J. J.,
Sivapalan, M., Vaché, K., Dunn, S., Grant, G., Haggerty, R., Hinz, C., Hooper,
R., Kirchner, J. and Roderick, M. L. (2007) 'Moving beyond heterogeneity and
process complexity: A new vision for watershed hydrology', Water Resources
Research, 43(7).
Montanari, A. and
Koutsoyiannis, D. (2012) 'A blueprint for process-based modeling of uncertain
hydrological systems', Water Resources Research, 48(9), pp. n/a-n/a.
Nearing, G. S. and
Gupta, H. V. (2017) 'Information vs. uncertainty as a foundation for a science
of environmental modeling', https://arxiv.org/abs/1704.07512.
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